Reviewer #2 (Public review):

Summary:

In this study, the authors investigate high-frequency oscillations (HFOs) in the prefrontal cortex during REM sleep. They identify a specific pattern where these HFOs occur in "chains" that are phase-locked to theta oscillations, primarily during the "phasic" periods of REM. The study contrasts these events with isolated HFOs and NREM ripples, suggesting a unique role for these chains in coordinating activity between the prefrontal cortex and the hippocampus. Most notably, the authors report that a specific subset of hippocampal cells-those that co-fire with the prefrontal cortex during these HFOs-increase their firing rates over the course of sleep, suggesting a potential mechanism for selective memory consolidation.

Strengths:

The study addresses an under-explored area of sleep physiology: the fine-grained temporal coordination between the cortex and hippocampus during REM sleep. The identification of HFO "chains" and their association with higher theta power provides an interesting framework for understanding how the brain might organize information transfer outside of NREM sleep. The observation that specific hippocampal populations show differential firing rate changes based on their participation in these HFO events is a striking finding that warrants further investigation.

Weaknesses:

The primary weakness of the study lies in the lack of a clear distinction between global brain states and the specific events being analyzed. Because the authors compare HFOs across different sleep stages (NREM, tonic REM, and phasic REM) without sufficient controls, it is difficult to determine if the observed differences are intrinsic to the HFOs themselves or simply a reflection of the different physiological states in which they occur.

Furthermore, the evidence for "structured reactivation" is not yet convincing. The temporal alignment of these reactivation events appears inconsistent, with peaks occurring well before the HFO itself, and the analysis does not sufficiently control for pre-existing cellular assembly strengths. Additionally, some of the sleep architecture presented appears atypical, such as very short REM bouts and direct NREM-to-REM transitions that bypass standard progression, raising questions about the consistency of the sleep detection across animals. Finally, the study does not account for potential confounds like baseline firing rates when interpreting the behavior of "high-cofiring" neurons, which may simply be the most active cells in the population.

Reviewer #3 (Public review):

Summary:

Shin et al. examine hippocampal-prefrontal interactions during sleep using simultaneous CA1 and prefrontal cortex recordings in rats performing a spatial memory task. They identify high-frequency oscillation (HFO) events in PFC during REM sleep that occur in theta-modulated chains and are associated with increased CA1-PFC coherence and sequential, sparse reactivation of cortical ensembles. This pattern contrasts with the synchronous reactivation observed during NREM cortical ripples. Together with a simple cholinergic network model, the authors propose that REM HFO chains represent a distinct mechanism for hippocampal-cortical coordination that complements NREM ripple-mediated processing during sleep.

Strengths:

A major strength of the work is the extensive electrophysiological dataset, which includes simultaneous recordings of large neuronal populations in both hippocampus and prefrontal cortex across behaviour and subsequent sleep. The analyses linking high-frequency events to population dynamics, interregional coherence, and ensemble reactivation are technically sophisticated and provide an incredibly detailed description of REM-associated cortical activity patterns. In particular, the demonstration that REM HFOs occur in chains aligned to theta phase and organise sequential activation of cortical assemblies represents a potentially important advance in understanding the neural structure of REM sleep activity. The integration of experimental data with a computational model further provides a useful framework for interpreting the observed differences between REM and NREM network states in terms of neuromodulatory influences.

Weaknesses:

While overall this study provides a highly valuable body of work, there are two primary limitations, which, if overcome, would provide substantially more significance to the overall characterisation of REM HFOs. Specifically:

(1) Distinction from wake HFOs

The results largely support the authors' claim that REM HFO chains represent a distinct pattern of neural coordination compared to NREM cortical ripples. The analyses consistently show differences between REM and NREM events in terms of neuronal modulation, ensemble structure, and interregional coupling. However, similar high-frequency events during wake are not examined. Since REM sleep shares several network features with wakefulness, including strong theta oscillations, evaluating whether comparable PFC HFOs occur during wake would provide clarity on whether these events are specific to REM sleep (and its associated functions) or represent a more general theta-associated phenomenon.

(2) Link to memory consolidation

The manuscript proposes throughout that REM HFO chains may contribute to memory consolidation by coordinating hippocampal-cortical reactivation, but the evidence for this functional role remains indirect. The authors do highlight this as a limitation of the study - the inability to link their findings to learning - but it is not clear why. Further details of the behaviour results should be included. If no learning occurred across the eight behavioural sessions, this should be reported. If learning did occur, but could not be linked to HFO events, this should also be reported.

Author Response:

Reviewer #1 (Public review):

Summary and Strengths:

Shin et al deepen our understanding of high-frequency oscillations in the frontal cortex during REM in a manner that sheds important light on the roles of these events. In particular, they reveal that cortical HFOs are modulated by theta oscillations, occur in chains and recruit cortical neuronal activation patterns in a manner that is distinct from other high-frequency events during non-REM or in the hippocampus. They also show that these events occur during increased oscillatory cross-talk between hippocampus and cortex and may protect cortical neurons from downregulation of firing during sleep. Overall, this is important work with several novel observations pointing towards an important role for these events that will become increasingly understood over time.

I also wanted to comment that 2D is a beautiful illustration of separate and essentially exclusive communication channels used during HF events in NREM vs REM. They almost perfectly complement each other's frequencies.

We thank the Reviewer for the positive comments and for highlighting the importance of our work, especially the distinct communication patterns during NREM and REM cortical high-frequency events.

Weaknesses:

I have only one major scientific critique: I believe we need to see quantification of how phasic REM theta waves with versus without HFOs differ. What do REM HFOs add to the "normal" theta oscillation? Without this comparison, it is more difficult to interpret the meaning of these events. Given that HFO chains have IEIs around the time of a theta cycle duration, are the repeating spiking activities stronger during HFO repeats than during adjacent theta waves without HFOs?

We agree with the Reviewer that differences in activity during HFOs versus theta in the absence of HFOs is an important comparison to make to determine whether activity during HFOs reflect a unique state of information processing during REM sleep, or is redundant with theta oscillation signatures. We attempt to clarify this point in Figure S4I where we examined PFC population activity during theta periods outside of HFOs. Here, we extracted REM theta periods at least 250 ms away from detected HFOs and split the theta cycles into quartiles based on the theta power at the preferred theta phase bin determined by theta-coupled-HFOs (during that specific sleep session). We expect that using the preferred phase of HFOs is the most accurate choice for this comparison (compared to random phases). Lastly, we aligned PFC population activity to these theta phases and found that even in the highest theta power quartile, theta modulated fluctuations in PFC population activity were absent without HFOs. This indicates that theta-associated HFOs are the primary driver or signature of the observed population activity patterns (Figures 1H, 3F, S4I). An explanation of this procedure can be found in the Methods section under “Control for periods of high theta power”.

Regarding the comment “what REM HFOs add to the "normal" theta oscillation”, we hypothesize that generation of HFOs and associated population activity is the result of theta-mediated input from other brain regions that converge on PFC. It is possible that CA1 is a candidate region, since we observed that theta frequency activity in CA1 leads PFC (Figure 4K, Phase slope index result). Additionally, the high concentration of acetylcholine and the high inhibitory tone in REM sleep is conducive to local suppression in response to external drive, as shown in the model and noted in the Discussion. Thus, we propose that HFOs delineate transient windows where sparse populations of PFC neurons are activated in the backdrop of overall suppression, potentially to link specific ensembles across PFC and other brain areas such as the hippocampus – a phenomenon that differs from baseline theta activity in REM.

To address this point, we will provide additional analyses investigating PFC activity profiles during theta periods adjacent to HFOs. We will also reorganize the results and figures to highlight these important control analyses.

What percentage of theta waves contain HFOs, and what is the firing rate during those theta waves with vs without HFOs? Is there differential firing rate modulation? The authors may even consider that all REM-HFO-specific quantifications should be shown as differential from phasic theta cycles without HFOs.

To address these points, we will perform the requested analyses and explicitly quantify firing rate differences during HFO and non-HFO theta periods for further clarification.

As a non-scientific comment on the manuscript itself: unfortunately, the paper is difficult to read and understand at times, requiring great effort by the reader. This is to an extent that communication is hindered. The paper is dense with changing methods, often from panel to panel. Unfortunately, the panel quantifications are not explained in the results section in a manner that readers can understand without going to read the methods, often for each individual panel. These measures should be explained in a way that lets readers understand the conclusions of each panel and what gross calculations were used to reach those. Instead, too much jargon is used rather than clear descriptions of the overall calculations being done for each panel.

The point is well-taken and we apologize for the dense text and lack of methodological detail in the results section. We agree with the Reviewer that enhancing clarity and adding additional details about the quantitative methods within the main text and figure panels/legends would improve readability and make the manuscript more accessible for a wider audience.

To address this point, we will include important details in the results section and legends to clarify the methods and calculations used. We will also reorganize the manuscript text and reorder some figure panels for readability, and update the Methods section to parallel the Results/Figure order to the extent possible.

The authors mention in the discussion section that they see increased functional connectivity between mPFC and CA1, but most data suggesting this seems to be based on LFP rather than spiking. Functional connectivity is best defined by spiking-spiking relationships. And these authors have spiking data. So I believe either the descriptive language should be pulled back to something like "oscillatory coupling" or more analyses should be dedicated to showing spike-spike coordination across regions.

To address this point, we will temper the claims of functional connectivity and replace all instances with “oscillatory coupling”.

Reviewer #2 (Public review):

Summary:

In this study, the authors investigate high-frequency oscillations (HFOs) in the prefrontal cortex during REM sleep. They identify a specific pattern where these HFOs occur in "chains" that are phase-locked to theta oscillations, primarily during the "phasic" periods of REM. The study contrasts these events with isolated HFOs and NREM ripples, suggesting a unique role for these chains in coordinating activity between the prefrontal cortex and the hippocampus. Most notably, the authors report that a specific subset of hippocampal cells-those that co-fire with the prefrontal cortex during these HFOs-increase their firing rates over the course of sleep, suggesting a potential mechanism for selective memory consolidation.

Strengths:

The study addresses an under-explored area of sleep physiology: the fine-grained temporal coordination between the cortex and hippocampus during REM sleep. The identification of HFO "chains" and their association with higher theta power provides an interesting framework for understanding how the brain might organize information transfer outside of NREM sleep. The observation that specific hippocampal populations show differential firing rate changes based on their participation in these HFO events is a striking finding that warrants further investigation.

We thank the Reviewer for finding our work interesting and for the positive comments regarding our manuscript.

Weaknesses:

The primary weakness of the study lies in the lack of a clear distinction between global brain states and the specific events being analyzed. Because the authors compare HFOs across different sleep stages (NREM, tonic REM, and phasic REM) without sufficient controls, it is difficult to determine if the observed differences are intrinsic to the HFOs themselves or simply a reflection of the different physiological states in which they occur.

We appreciate this concern. We do agree that the generation of these ripples/HFOs in NREM and REM sleep are inextricably linked to global brain state (ex. cholinergic tone, as shown in the model), which results in differing patterns of activity across sleep states. However, we also show that activity associated with ripples and HFOs in NREM and REM sleep, respectively, delineate unique periods that underlie intra- and interregional interactions that differ from activity associated with other phenomena, such as spindles or baseline theta periods, in each respective sleep state. Regarding NREM PFC ripples, in our previous publication (Shin and Jadhav 2024), we show that PFC ripples are strongly associated with spindles and slow oscillations, but when PFC activity was assessed by aligning to each of these events separately, we observed significant differences in activity profiles (Shin and Jadhav 2024), indicating that NREM PFC ripples are indeed periods of differential PFC activity during which local reactivation is particularly strong. Similarly, here, in REM sleep, we see that PFC HFOs are strongly coupled with gamma oscillations and that these two frequency bands separately engage PFC neurons (Figures 2C, S3J, differences in phase locking preference of PFC neurons to gamma and HFO). While we observed strong theta modulated neuronal population activity in response to HFOs (Figure 1H), we did not observe the same for gamma events that were uncoupled from HFOs (Figure S3L, right). However, we did observe the population activity suppression when examining gamma events that were coupled with HFOs, but the theta modulated activity was largely absent (Figure S3L, left), indicating that, in terms of higher frequency oscillations, precise alignment to HFOs drives the theta modulated activity. Furthermore, we provide a control for baseline theta periods outside of HFOs to demonstrate that the phasic, theta-modulated activity (Figures 1H, 3F) is due to association with HFOs, and not a common feature during baseline theta activity (Figure S4I). Together, these results demonstrate that the theta modulated, phasic PFC activity that we report is primarily associated with the presence of HFOs.

To address this point, we will provide a more detailed explanation for the theta controls that we performed, and conduct additional analyses to control for different baseline periods during REM sleep, similar to the response to Reviewer 1’s first comment.

Furthermore, the evidence for "structured reactivation" is not yet convincing. The temporal alignment of these reactivation events appears inconsistent, with peaks occurring well before the HFO itself, and the analysis does not sufficiently control for pre-existing cellular assembly strengths.

We thank the Reviewer for raising these important points. Regarding the temporal alignment of assemblies during REM HFOs, since gamma activity is linked to and precedes HFO activity in REM (Figure S3F,G), we posit that assembly activation preceding HFO alignment may be gamma frequency driven. Indeed, we do observe gamma-associated peaks in PFC population activity temporally adjacent to the start of HFO chains in REM (Figure S5F), which we propose is driving the assembly activation.

Related to our response to Reviewer 1, the hypothesis that we have regarding this finding is that theta-mediated input to PFC, possibly from several brain areas including the hippocampus, converges and elicits cross-frequency activity spanning gamma and HFO bands. We hypothesize that these gamma and HFO oscillations work in concert to evoke the structured reactivation.

Furthermore, as the Reviewer accurately points out, we are not able to determine whether the assembly patterns active during the REM HFOs pre-existed prior to their assessment during sleep. Since there was not enough REM sleep during the earlier sleep epochs, we were not able to investigate assembly activation patterns during REM in the first pre-task sleep session prior to W-Track exposure.

To address these points, we will provide additional support for our claims, add clarification to major points, and expand on the methods used to assess structured reactivation. We will also analyze the spatial rate maps of assemblies during behavior on the W-Track and attempt to link these representations to assembly activity during REM HFOs. If sufficient controls cannot be provided, we will temper the claims of “reactivation” and replace all mentions with assembly “activation”.

Additionally, some of the sleep architecture presented appears atypical, such as very short REM bouts and direct NREM-to-REM transitions that bypass standard progression, raising questions about the consistency of the sleep detection across animals.

The reviewer is presumably referring to the hypnograms in Figure S1H. In Figure S1H, we presented concatenated hypnograms across all 9 sleep sessions, regardless of whether they were included for analysis. Furthermore, these hypnograms illustrate the output of just the sleep scoring algorithm and do not take into account the secondary, manual inspection that is performed to confirm sleep epoch inclusion. Individual epoch sleep state plots (e.g. Figure S1B) were visually inspected to confirm robust increases in theta-to-delta ratio detected in the absence of movement – epochs where microarousals or persistent subthreshold fluctuations in animal movement induced noisy TD ratio increases, and thus inaccurate REM designation, were excluded. We also want to note that omitting the edge cases, which is a minor part of the REM sleep data, does not change any results.

Another consideration is that these animals were running a strenuous learning task that required repeated traversal of multiple maze arms over multiple behavioral session, which likely increased sleep pressure and thus may have altered sleep state dynamics in a subset of animals (Leemburg et al. 2010; Yang et al. 2012).

To address these points, we will provide updated hypnograms that explicitly highlight the epochs used in analysis to resolve ambiguities. We will also further demonstrate that our procedure for sleep state designation is accurate and consistent across animals with supporting materials, including additional sleep stage classification examples, and REM-specific sleep examples marking tonic and phasic REM.

Finally, the study does not account for potential confounds like baseline firing rates when interpreting the behavior of "high-cofiring" neurons, which may simply be the most active cells in the population.

When we compared low and high cofiring neurons in CA1, we did indeed compare baseline firing rates between the two groups and found no differences. We compared both mean firing rates across entire sleep sessions as well as mean firing rates restricted to REM sleep (Figure S7A). We apologize that this important control was not emphasized more clearly.

To address this point, we will explicitly reference this figure in the main text as a standalone point.

Reviewer #3 (Public review):

Summary:

Shin et al. examine hippocampal-prefrontal interactions during sleep using simultaneous CA1 and prefrontal cortex recordings in rats performing a spatial memory task. They identify high-frequency oscillation (HFO) events in PFC during REM sleep that occur in theta-modulated chains and are associated with increased CA1-PFC coherence and sequential, sparse reactivation of cortical ensembles. This pattern contrasts with the synchronous reactivation observed during NREM cortical ripples. Together with a simple cholinergic network model, the authors propose that REM HFO chains represent a distinct mechanism for hippocampal-cortical coordination that complements NREM ripple-mediated processing during sleep.

Strengths:

A major strength of the work is the extensive electrophysiological dataset, which includes simultaneous recordings of large neuronal populations in both hippocampus and prefrontal cortex across behaviour and subsequent sleep. The analyses linking high-frequency events to population dynamics, interregional coherence, and ensemble reactivation are technically sophisticated and provide an incredibly detailed description of REM-associated cortical activity patterns. In particular, the demonstration that REM HFOs occur in chains aligned to theta phase and organise sequential activation of cortical assemblies represents a potentially important advance in understanding the neural structure of REM sleep activity. The integration of experimental data with a computational model further provides a useful framework for interpreting the observed differences between REM and NREM network states in terms of neuromodulatory influences.

We thank the Reviewer for finding our work important and for the positive comments regarding the manuscript.

Weaknesses:

While overall this study provides a highly valuable body of work, there are two primary limitations, which, if overcome, would provide substantially more significance to the overall characterisation of REM HFOs. Specifically:

(1) Distinction from wake HFOs

The results largely support the authors' claim that REM HFO chains represent a distinct pattern of neural coordination compared to NREM cortical ripples. The analyses consistently show differences between REM and NREM events in terms of neuronal modulation, ensemble structure, and interregional coupling. However, similar high-frequency events during wake are not examined. Since REM sleep shares several network features with wakefulness, including strong theta oscillations, evaluating whether comparable PFC HFOs occur during wake would provide clarity on whether these events are specific to REM sleep (and its associated functions) or represent a more general theta-associated phenomenon.

We thank the Reviewer for this suggestion. Indeed, this is an important comparison to make, since electrophysiological patterns of activity are similar across wake and REM sleep states.

To address this point, we will detect and analyze HFOs during running behavior on the W-Track to determine if they elicit similar, phasic population responses in PFC.

(2) Link to memory consolidation

The manuscript proposes throughout that REM HFO chains may contribute to memory consolidation by coordinating hippocampal-cortical reactivation, but the evidence for this functional role remains indirect. The authors do highlight this as a limitation of the study - the inability to link their findings to learning - but it is not clear why. Further details of the behaviour results should be included. If no learning occurred across the eight behavioural sessions, this should be reported. If learning did occur, but could not be linked to HFO events, this should also be reported.

This point is well-taken and we will reduce emphasis on memory consolidation in the manuscript. We do want to note that the primary focus here was to investigate new cortical-hippocampal activity patterns during sleep states that are established to be important for memory consolidation, in this case, REM sleep. Indeed, several major discoveries of reactivation and cortical-hippocampal physiological patterns in rodent sleep and wake states thought to be important for memory consolidation were initially reported without a link to memory consolidation, e.g., NREM hippocampal reactivation and replay (Wilson and McNaughton 1994; Lee and Wilson 2002), cortical – hippocampal activity coordination in slow-wave sleep (Siapas and Wilson 1998; Ji and Wilson 2007), waking replay in hippocampus (Foster and Wilson 2006; Karlsson and Frank 2009), etc. As Reviewer 1 noted, we expect that an important role for these novel events reported here will become increasingly understood over time.

The connection between learning and REM HFO activity is a line of investigation that we find very interesting. However, due to the experimental design and the rapid pace at which the animals learn this task (Shin, Tang, and Jadhav 2019), we were not able to robustly relate REM HFO activity to learning. Firstly, with our threshold criteria for REM sleep detection (>10 s) as well as a total REM sleep duration criterion for sessions, most of the sleep epochs included for analysis came from the later sessions when REM sleep was more abundant (Figure SF,G). Consequently, many of the sleep sessions following the earlier behavioral/learning sessions were excluded. Making a claim about the contribution of REM HFOs to the learning process requires the inclusion of REM sleep periods after each behavior session to examine incremental changes in response to learning. Furthermore, a comparison of these REM sleep periods to pre-task REM sleep (pre-task sleep session #1 prior to task exposure) is important to demonstrate that any changes are dependent on experience. However, we were unable to make this comparison due to lack of REM sleep in pre-task sleep session #1. It is likely that an investigation of the role of these novel events in memory consolidation may require rodent task designs that are known to require REM sleep, such as inference tasks (Abdou et al. 2024; Ellenbogen et al. 2007), motor learning (Nitsche et al. 2010), or emotional memory (van der Helm and Walker 2011; Cairney et al. 2015).

To address this point, we will reinforce this as a limitation of our study, reduce emphasis on memory consolidation, and further clarify that we were not able to link REM HFO activity to learning. We will also include additional details about the behavioral results.

References

Abdou, K., M. Nomoto, M. H. Aly, A. Z. Ibrahim, K. Choko, R. Okubo-Suzuki, S. I. Muramatsu, and K. Inokuchi. 2024. 'Prefrontal coding of learned and inferred knowledge during REM and NREM sleep', Nat Commun, 15: 4566.

Cairney, S. A., S. J. Durrant, R. Power, and P. A. Lewis. 2015. 'Complementary roles of slow-wave sleep and rapid eye movement sleep in emotional memory consolidation', Cereb Cortex, 25: 1565–75.

Ellenbogen, J. M., P. T. Hu, J. D. Payne, D. Titone, and M. P. Walker. 2007. 'Human relational memory requires time and sleep', Proc Natl Acad Sci U S A, 104: 7723–8.

Foster, D. J., and M. A. Wilson. 2006. 'Reverse replay of behavioural sequences in hippocampal place cells during the awake state', Nature, 440: 680–3.

Ji, D., and M. A. Wilson. 2007. 'Coordinated memory replay in the visual cortex and hippocampus during sleep', Nat Neurosci, 10: 100–7.

Karlsson, M. P., and L. M. Frank. 2009. 'Awake replay of remote experiences in the hippocampus', Nat Neurosci, 12: 913–8.

Lee, A. K., and M. A. Wilson. 2002. 'Memory of sequential experience in the hippocampus during slow wave sleep', Neuron, 36: 1183–94.

Leemburg, S., V. V. Vyazovskiy, U. Olcese, C. L. Bassetti, G. Tononi, and C. Cirelli. 2010. 'Sleep homeostasis in the rat is preserved during chronic sleep restriction', Proc Natl Acad Sci U S A, 107: 15939–44.

Nitsche, M. A., M. Jakoubkova, N. Thirugnanasambandam, L. Schmalfuss, S. Hullemann, K. Sonka, W. Paulus, C. Trenkwalder, and S. Happe. 2010. 'Contribution of the premotor cortex to consolidation of motor sequence learning in humans during sleep', J Neurophysiol, 104: 2603–14.

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eLife Assessment

This study is useful and unique, since hagfish brains are of phylogenetic importance and can reveal features ancestral to all vertebrates. The manuscript is, however, incomplete and would benefit from contextualization with the current literature; comparisons with the recent amphioxus study are suggested, plus an increased focus on the specific, unique features of the hagfish brain. One significant concern is the apparent absence of Datx2 expression, given that the riboprobe was synthesized from cDNA derived from whole-brain RNA extracts. Ideally, the authors should identify a tissue in which Datx2 is known to be strongly expressed and then apply the probe as a positive control.

Reviewer #1 (Public review):

Summary:

The manuscript presents a three-dimensional and molecular atlas of the adult hagfish brain to investigate the evolutionary origin and early diversification of vertebrate brain organization. Using whole-brain tissue clearing, light-sheet microscopy, and computational reconstruction, the authors generate a high-resolution 3D anatomical model of the hagfish brain. They complement this structural analysis with gene-expression profiling of neurotransmitter systems and receptors, including glutamatergic, GABAergic, cholinergic, serotonergic, and dopaminergic markers.

Strengths:

Together, the work aims to establish a modern neuroanatomical reference for the hagfish. Given the phylogenetic importance of hagfish as one of two extant species of cyclostomes (the other being lamprey), and the fact that the hagfish brain has barely been studied in contrast to the lamprey, the atlas provides a foundational resource and should be of interest to evolutionary and comparative neurobiology.

Weaknesses:

However, there are several places where both data presentation and the narrative can be improved and clarified, and particularly some of the homology and evolutionary claims seem to be superlative and need to be toned down. I present more detailed comments below:

(1) The authors spend too much effort trying to convince readers of the monophyly of hagfish and lamprey to stress its importance for evolutionary comparisons. This is now well accepted; instead, there could be more details on some of the specific, unique features of the hagfish brain relevant to a comparative atlas. For instance, the unusual fusion of the telencephalon anteriorly with the olfactory bulb and posteriorly with the diencephalon (Wicht and Northcutt, 1992), the degenerate visual system, the absence of the pineal gland, and the oculomotor system can be discussed in reference to the generated atlas and examined marker expression in related structures and their possible identity.

(2) The assertion that the MGE is absent in the lamprey is incorrect based on Sugahara et al. (2016; 2017), who identified lamprey paralogues of Nkx2.1/2.4 that are expressed in the ventral subpallium. This should be corrected.

(3) The major contribution of this study, in my mind, is the "three-dimensional atlas" of the hagfish brain. However, the atlas itself is not presented; A video of the 3D reconstructed Nissl-stained hagfish brain would be an important data resource and should be added. Annotations of forebrain, midbrain and hindbrain regions and constituent major structures can also be illustrated, which will be a useful resource.

(4) In the pallium, there seems to be an inner GABAergic cell layer and inner and outer glutamatergic cell layers, as noticed in lampreys (Suryanarayana et al., 2017). What are the overall proportions of glutamatergic and GABA neurons? In the images, it does seem that vGlut neurons are present in both P2 and P4, while there appear to be more GAD neurons in P4.

(5) As a general comment, homology claims should be toned down throughout the manuscript. This would at least require some connectivity data or transcriptomic analysis for any possible suggestions; the current data, with few markers, are insufficient for any reasonable comparisons.

(6) Expression of Pax6 and AChE is not sufficient to suggest a cerebellum-like structure. While it is true that embryonic Pax6 expression in the rhombic lip of the hagfish embryo is more comparable to other vertebrates than lamprey, and the presence of a rudimentary cerebellum-like structure would be of great interest, the evidence is too limited for such claims and should be toned down.

(7) Again, expression of Tbr1 and GAD1 in NCvl neurons does not suggest that these could be hippocampal neurons. One would at least need to rule out expression of prethalamic markers and demonstrate the presence of pallial markers through transcriptomic data (as in Lamanna et al., 2023).

(8) Presence of GABAergic neurons in the striatum - is there any data on expression of dopamine receptors, particularly given the seeming loss of the D2 receptor subtype in the hagfish?

Reviewer #2 (Public review):

Summary:

The work of Harada and collaborators fills an important gap in our knowledge of neuronal identities in the adult hagfish brain. There is essentially no modern, cell-type-level characterisation of neuronal identity in the hagfish brain yet. Existing data are limited to classical neuroanatomy (e.g. Nieuwenhuys) and sparse transmitter/gene-expression studies, mostly in embryos (e.g. work from the Kuratani lab). This study reveals a very broad peculiar pattern of dopaminergic identities and a strikingly unusual pattern of serotonergic transmission, with serotonergic cell bodies present in the telencephalon, which is uncommon for vertebrates and contrasts with previous reports (e.g., Kadota, 1991).

Strengths:

The three-dimensional reconstruction of the brain, including the ventricular system, is novel and very useful. Most of the neurotransmitter identity patterns presented here have not been previously described, and those that were published earlier, such as the serotonergic system (e.g. Kadota, Nieuwenhuys, Wicht), are old and would clearly benefit from re-evaluation using more modern approaches.

Weaknesses:

Neurotransmitter identities are highly relevant for interpreting the possible presence of LGE/MGE territories in hagfish (e.g. GABAergic patterns), for characterising the raphe nuclei (e.g. serotonergic system), and for refining our understanding of the central prosencephalic complex in relation to other vertebrate brain architectures. However, the authors do not address these points and overlook recent evidence from the amphioxus brain that could help interpret their results in an evolutionary context. Overall, the results are insufficiently discussed in relation to the current state of the art.

The study would clearly benefit from complementary gene expression profiling to place these neurotransmitter patterns within a broader framework of brain partitions, to enable more direct comparisons with other vertebrates, and, importantly, to interpret them in relation to the prosomeric model. Furthermore, the work lacks appropriate controls for the in situ hybridization experiments; Datx2 does not show any expression, so there is currently no evidence that this probe is functional. Including such controls would also strengthen the overall description of the dopaminergic system, especially given that the expression patterns of the different genes analysed appear very diffuse and somewhat random.

eLife Assessment

This important work outlines why commonly applied performance metrics in predictive modelling do not accurately reflect translational potential using the example of psychiatric care; it provides a web-based tool to contextualize effect sizes in psychiatry with respect to reliability and base rates, and to calculate the real-world utility of prediction models under different scenarios. The evidence supporting the conclusions is convincing, incorporating established psychometric principles that will be of use for multiple fields, along with transparent quantitative logic and example applications. The manuscript would benefit from further details about how the tool can be optimally applied and how the resulting outputs should be interpreted. The work will be of broad interest to both clinical experts and scientists in biomedicine and the life sciences.

Reviewer #1 (Public review):

Summary:

The manuscript provides a well‑argued discussion of the misalignment between common predictive performance evaluations reported in the literature and actually measuring clinical utility in the context of predictive psychiatry. Specifically, the authors discuss measurement reliability and prevalence as two neglected factors which can substantially inflate the assessment of model performance for clinical practice. To mitigate this, the authors offer a concrete framework and an accompanying web tool, with which to adjust performance metrics and additional predictive‑value and decision‑analytic measures.

Strengths:

The manuscript speaks convincingly about the risk of face validity and the practical irrelevance of seemingly promising predictive models in psychiatry. The authors outline how predictive performance estimations often fail to generalize to clinical contexts and thereby potentially mislead scientific efforts. In the face of ubiquitous biomarker models and incremental improvements in the literature, the reader is reminded that, irrespective of the glory of the proposed model, low reliability of clinical measurements fundamentally affects (and limits) both effect sizes and predictive performance ("garbage in, garbage out"), and that neglecting this can ultimately lead to misinformed decisions in the treatment of individual patients. The provision of an online tool with a user‑friendly interface and clearly worked examples is a major practical asset that will facilitate the adoption of the proposed framework beyond quantitative methodologists.

Weaknesses:

While the outlined issues highlight important aspects in the translational gap, the suggested solutions remain somewhat theoretical. For example, the use of prevalence might not reflect what a model would see in practice, assuming that population prevalence and the composition of actual clinical cohorts are aligned. Accounting for who presents to care, and under which referral or triage patterns, is a crucial determinant of effective base rates. While the authors do acknowledge the importance of using base rates from the target population, these nuances could be emphasized more prominently at the points where practical recommendations are made. Relatedly, the analytical context and the methodological assumptions are not clearly specified. Many arguments and demonstrations are derived in univariate, group‑comparison settings and then discussed in a way that can be read as broadly applicable.

Reviewer #2 (Public review):

Summary and strengths:

The authors present a description of their online tool to estimate real-world performance of predictive models. The authors bring together different calculations to make better-informed implementation choices. It is a very nice tool to go from effect sizes to base rates to decision curve analysis. The paper describes the background and use of the tool with examples and seems like an extended version of their online how-to. The methods themselves are not new, but I think the tool will be valuable for researchers from different fields. Tools already exist for the conversion of effect sizes (my current favorite is https://www.escal.site/), but I haven't seen measurement noise being incorporated previously. The main benefit is the evaluation of performance under different real-world scenarios. Code is available on GitHub, and the manuscript is well-written.

Weaknesses:

While comprehensive explanation and examples are important for correct use of the tool, I don't really see the added value above their online how-to guide, as the software itself has already been published (Karvelis, P. and Diaconescu, A. O. (2025b). E2p simulator: An interactive tool for estimating real world predictive utility of research findings. Journal of Open Source Software, 10(114):8334.)

Reviewer #3 (Public review):

Summary:

This important work provides a web-based tool to contextualize effect sizes in psychiatry with respect to reliability and base rates (collectively referred to as predictive utility analysis). The methods for the tool incorporate established psychometric principles that I think are of use for multiple fields in this seemingly easy-to-use tool. I agree with the critical importance of this tool and the methodological points made in this manuscript. Enthusiasm for the manuscript is weakened by a lack of clarity on the formulation of the paper and stated goals of the examples used, with the inferences and impact on clinical decision making from various parameterizations via this tool left open-ended.

Strengths:

This paper presents a well-considered and, what I think will be highly useful, web-based tool to contextualize effect sizes with respect to reliability and base rates. As the authors rightly point out, such a tool could be used in conjunction with widespread analytic power analysis tools in study planning. The paper also well contexualizes the need for such a tool in the relatively recent history of concerns of power, reliability, and inference in psychiatry specifically, and more general meta-scientific debates in psychology and neuroscience.

Weaknesses:

My primary feedback on this manuscript is the lack of clarity in what the paper itself, specifically, separate from the tool, is hoping to achieve. There is a central, but unresolved, tension in whether the reader is supposed to:

(1) focus on the specifics of the examples used and whether to reevaluate the substantive claims from the studies, (2) buy in to how various reliability and base rate parameters impact modeling outcomes, (3) receive an introduction to the tool itself.

In my estimation, the largest contribution to the field here is in (2) and (3), but currently much of the real estate of the paper is dedicated to several examples of (1). While these specific examples may be illustrative to some degree, I think given the number and brevity of such, they are unlikely to incidentally achieve points (2) and (3) above. Specific examples include the assertion of kappas for DSM diagnoses, without much nuance (e.g., see https://psycnet.apa.org/buy/2015-27500-001). Given the relatively limited space given to this example, however, it's hard to be entirely certain what the reviewer should take away.

A second point of concern is where this tool would be situated in the research pipeline. I agree with the authors that this tool could be used in ways that parallel power analysis. With that in mind, it seems the most common use of this tool for an individual investigator is likely to be in a priori study planning. In contrast, and with my point above in mind, the use of the tool for existing results is likely best done with multiple estimates of effect sizes, reliability, and base rates, as is common in meta-analysis or consensus reviews. Nevertheless, there is no real example or guidance around how this influences new study planning.

A third point is that more nuance would be useful in the introduction about the current state of psychiatry research. For example, I share many of the authors' concerns about reliability, power, reproducibility, and barriers to translation. That said, it is the case that while effect sizes should be considered considerably more, they are widely considered in psychiatry research via the common place of meta-analysis and other data pooling approaches. Another such example that the authors state in the context of reliability: "However, this [reliability] attenuation is rarely accounted for in routine analyses in psychiatry". This is true in practice, but somewhat misleading insofar as the method by which to do this remains unclear. For example, should we all report disattenuated associations, assuming there is no error and everything is perfectly reliable? This, of course, would be unrealistic to expect zero error. That we can achieve this with the new tool is clear, but the nuance of how and under what circumstances it should be done is not clear, and such nuance should be better reflected in the framing of the problem. That is, there is also a lack of clarity on what ought to be best practices and field-wide goals, rather than simply the lack of an ability to model these factors.

Minor point

For conceptual clarity, it would benefit the manuscript to at least briefly mention the role of validity in translational importance. Of course, the current psychometric issues of reliability, base rate, power, etc are critical, but it should at least be mentioned, given the potential wide audience of this manuscript, validity is important as well. For example, highly reliable measures may not be valid indicators of underlying disease etiology (e.g., fMRI head motion is a highly reliable trait-level feature, but typically not considered an important predictor or consequence of mental health worth investing translational resources in). Relatedly, confounding as a general topic would be useful to mention just briefly, to help with the spirit of considering underlying issues in translation.

eLife Assessment

The authors present useful findings demonstrating that the RNA modification enzyme Mettl5 regulates sleep in Drosophila. Through transcriptome- and proteome-wide analyses, the authors identified downstream targets affected in heterozygous mutants and proposed that Mettl5 regulates the translation and degradation of clock genes to maintain normal sleep function. Through additional analyses, the authors provided solid evidence supporting this model.

Reviewer #1 (Public review):

Summary:

Here the authors attempted to test whether the function of Mettl5 in sleep regulation was conserved in Drosophila, and if so, by which molecular mechanisms. To do so they performed sleep analysis, as well as RNA-seq and ribo-seq in order to identify the downstream targets. They found that the loss of one copy of Mettl5 affects sleep, and that its catalytic activity is important for this function. Transcriptional and proteomic analyses show that multiple pathways were altered, including the clock signaling pathway and the proteasome. Based on these changes the authors propose that Mettl5 modulate sleep through regulation of the clock genes, both at the level of their production and degradation, possibly by altering the usage of Aspartate codon.

Comments on revisions:

The authors addressed all my comments satisfactorily.

Reviewer #3 (Public review):

Xiaoyu Wu and colleagues examined a potential role in sleep of a Drosophila ribosomal RNA methyltransferase, mettl5. Based on sleep defects reported in CRISPR generated mutants, the authors performed both RNA-seq and Ribo-seq analyses of head tissue from mutants and compared to control animals collected at the same time point. A major conclusion was that the mutant showed altered expression of circadian clock genes, and that the altered expression of the period gene in particular accounted for the sleep defect reported in the mettl5 mutant. In this revision, the authors have added a more thorough analysis of clock gene expression and show that PER protein levels are increased relative to wild type animals a specific times of day, indicating increased stability of the protein. Given that PER inhibits its own transcription, the per RNA is low in the mutants. The revised manuscript included efforts toward a more detailed understanding of how clock gene expression was altered in the mutants, as well as other clarification of sleep phenotypes.

Comments on revisions:

All critiques have been addressed by the authors; the manuscript is much improved from its original submission. Thank you.

Author Response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Here, the authors attempted to test whether the function of Mettl5 in sleep regulation was conserved in drosophila, and if so, by which molecular mechanisms. To do so they performed sleep analysis, as well as RNA-seq and ribo-seq in order to identify the downstream targets. They found that the loss of one copy of Mettl5 affects sleep, and that its catalytic activity is important for this function. Transcriptional and proteomic analyses show that multiple pathways were altered, including the clock signaling pathway and the proteasome. Based on these changes the authors propose that Mettl5 modulate sleep through regulation of the clock genes, both at the level of their production and degradation, possibly by altering the usage of Aspartate codon.

Comments on revised version:

The authors satisfactorily addressed my comments, even though the precise mechanism by which Mettl5 regulates translation of clock genes remains to be firmly demonstrated.

Reviewer #3 (Public review):

Xiaoyu Wu and colleagues examined a potential role in sleep of a Drosophila ribosomal RNA methyltransferase, mettl5. Based on sleep defects reported in CRISPR generated mutants, the authors performed both RNA-seq and Ribo-seq analyses of head tissue from mutants and compared to control animals collected at the same time point. A major conclusion was that the mutant showed altered expression of circadian clock genes, and that the altered expression of the period gene in particular accounted for the sleep defect reported in the mettl5 mutant. In this revision, the authors have added a more thorough analysis of clock gene expression and show that PER protein levels are increased relative to wild type animals a specific times of day, indicating increased stability of the protein. Given that PER inhibits its own transcription, the per RNA is low in the mutants. Efforts toward a more detailed understanding of how clock gene expression was altered in the mutants, as well as other clarification of sleep phenotypes throughout is appreciated. As noted above, a strength of this work is its relevance to a human developmental disorder as well as the transcriptomic and ribosomal profiling of the mutant. However, there still remain some minor weaknesses in the manuscript. This reviewer is not in agreement with the interpretation of the epigenetic experiments. Specifically, co-expression of Clk[jrk] or per [01] with the mettl5 mutant recovered the nighttime sleep phenotype, but was additive to the daytime sleep phenotype such that double mutants showed higher sleep. This effect should be acknowledged and discussed. Overall, this is an interesting paper that indicates a molecular link between mettl5 and the circadian clock in regulation of sleep.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

The authors misunderstood my original comment for Fig 1A. Please provide an explanation for the significance of the boxed region. There is little or no detail in the legend to help guide the reader.

The information has been added to the figure legends for Figure 1A.

Efforts toward improving analysis of circadian genes as well as sleep phenotypes (sleep onset time, rebound, etc) is much appreciated, thank you. However, Figure S1H and G panel labels are mixed up; please label in the order that they appear and that they correspond to the main text. Why is Figure S1H labeled "ZT 14"?

Sleep latency is defined as the time from preparing to sleep to actually falling asleep. In this study, it specifically refers to the time taken for each individual fly to reach the sleep phenotype (i.e., 25 minutes of continuous sleep). We noted that this label was misleading, as the actual time to reach the sleep phenotype varied among individual flies. Therefore, in the revised figures, we have removed the ZT14 label. In addition, we have corrected the labeling of Figures S1G and S1H to ensure they appear in the correct order and correspond accurately to the descriptions in the main text.

Unfortunately, based on Fig S1A-C, I am not convinced that mettl5 localizes to neurons, as there are no cells that show double labelling. This figure does not support the statement: "we found expression in both neurons (colocalizing with ELAV staining: Figure S1A-C) (lines 91-92), and "Mettl5-Gal4 is expressed in distinct neurons and glia that appear crucial for sleep regulation." (line 297). What "distinct" sleep related neurons were labeled? The staining in Fig S1A shows a different distribution from that in Fig S1D, and so it's possible this was a technical issue. Is there a better example?

Thank you for your careful review and valuable comments. We agree that the colocalization of METTL5 with the neuronal marker ELAV is relatively sparse. However, as indicated by the arrows in Fig S1A–C, we did observe a few cells showing clear double labeling. These examples support the presence of METTL5 expression in neurons, albeit at a low frequency.

In Figure 4G-H, please indicate the time of day of tissue collection.

In Figure 4G-H, the tissue was collected at ZT0. We have now indicated this time point in the figure and legend to clarify the experimental timing.

As noted in the public comment, I remain in disagreement with the assessment that "the double mutant showed the similar phenotype as downstream genes". The striking significant increase in daytime sleep in the double mutants remains unexplained. No further experiments are necessary, but this should be acknowledged in the text. Instead of an epistatic effect, given that overall sleep is high in the double mutants, another possible explanation is that the flies are sick and so are less active and sleeping more.

Thank you for your suggestion. This has been acknowledged in the text. “Genetic epistasis experiments further supported this model, with clock gene mutants modified Mettl5 mutant phenotypes that suggesting both Clock and  Per downstream of Mettl5 (Figure 4I-N, Table 1). Secondary effect may exist for the significant increase in daytime sleep in the double mutants.”

eLife Assessment

This study provides valuable insights into the role of MATR3 in oocyte maturation and folliculogenesis, using conditional knockout mice and in vitro follicle culture systems to show that MATR3 is required for oocyte growth and gene transcription, with downstream effects on follicle development. The strength of the evidence is incomplete, as key findings lack independent validation, methodological details are insufficient, and inconsistencies in data presentation reduce confidence in the conclusions. The work will be of interest to researchers in reproductive biology and fertility.

Reviewer #1 (Public review):

Summary:

This study aims to clarify MATR3's function and molecular mechanism in oocyte growth and maturation, explore its association with OMA, and its potential as a diagnostic and therapeutic target using specific knockout mouse models, human OMA samples, and multi-omics technologies. And it has fully achieved preset objectives with results strongly supporting conclusions. Specifically, it addresses the gap in the synergistic mechanism of epigenetic and secretory signals regulated by RNA-binding proteins (RBPs) in oocyte growth and enriches the molecular etiological spectrum of oocyte maturation disorders. It is the first time the conservative function of MATR3 has been revealed in multiple species, providing a paradigm for cross-species research on RBPs in the field of reproductive biology. It also provides a new candidate target for OMA, a clinically refractory infertility disease, and is expected to promote the optimization of assisted reproductive technology and the development of precision medicine.

Strengths:

The strengths of this study are significant and prominent. First, the research system is comprehensive, integrating knockout mouse models, in vitro knockdown models, multi-species (mouse, porcine, and human) verification, combined with scRNA-seq, LACE-seq, CO-IP, and other multi-omics and molecular biology technologies, forming a complete and progressive evidence chain. Second, the mechanism analysis is in-depth, clarifying the dual molecular mechanisms of MATR3 regulating the transcriptional synthesis and secretion of GDF9 through "recruiting KDM3B to regulate H3K9me2 demethylation" and "directly binding to Rdx mRNA", with a clear logical closed loop. Third, the clinical correlation is close. It is the first time to find abnormal nuclear localization of MATR3 in oocytes of OMA patients, providing new clues for clinical disease mechanism research, and verifying the downstream function of GDF9 through rescue experiments, effectively enhancing the translational value of the results.

Weaknesses:

This study included only one OMA patient's oocyte sample. Without clinical screening for MATR3 mutations or abnormal expression, establishing a causal relationship between MATR3 and OMA remains difficult.

Reviewer #2 (Public review):

Summary:

This study investigates the role of MATR3 in oocyte development and folliculogenesis using conditional knockout mouse models together with in vitro follicle culture and molecular analyses. The authors aim to determine whether MATR3 regulates oocyte maturation and follicle development and to explore potential mechanisms linking MATR3 function to transcriptional and epigenetic regulation in growing oocytes.

Strengths:

A major strength of the work is the use of a conditional knockout mouse model combined with complementary in vitro follicle culture approaches, which together provide a useful framework for examining gene function during oocyte development. The study also attempts to integrate cellular phenotypes with molecular analyses of transcriptional activity and epigenetic markers.

Weaknesses:

Several weaknesses limit the strength of the conclusions. These include insufficient validation of key experimental manipulations (such as the efficiency of MATR3 knockdown in siRNA experiments), limited quantification or statistical analysis for some datasets, inconsistencies between the text and presented data in certain figures, and incomplete methodological descriptions that make it difficult to fully evaluate reproducibility.

Reviewer #3 (Public review):

Summary:

The study aims to elucidate the dual molecular mechanisms of the RNA-binding protein MATR3 in oocyte growth and maturation. The authors propose that MATR3, highly expressed in growing oocytes (GOs), regulates oocyte quality through two pathways: epigenetically, by recruiting KDM3B to remove the repressive H3K9me2 mark at the Gdf9 locus to activate transcription; and post-transcriptionally, by binding Rdx mRNA to maintain microvillus structure for GDF9 secretion. This mechanism ensures oocyte-granulosa cell communication and female fertility. The study also explores the link between MATR3 and human oocyte maturation arrest (OMA).

Strengths:

The study proposes an innovative dual-mechanism model encompassing "epigenetic transcriptional activation and cytoskeletal regulation," which not only expands the functional understanding of RNA-binding proteins in chromatin regulation but also reveals the coordination between nuclear transcription and organelle structure. By integrating scRNA-seq and LACE-seq, the authors constructed a comprehensive regulatory network for MATR3, identifying both key targets and numerous potential molecules, thereby providing rich resources for future mechanistic studies. Furthermore, the inclusion of oocyte samples from human OMA patients directly links the basic findings to clinical reproductive disorders. Despite the limited sample size, this approach demonstrates strong translational potential.

Weaknesses:

The partial phenotypic improvement achieved by exogenous GDF9 supplementation suggests that the downstream effector pathways may involve a more complex network regulation, implying that the current interpretation of GDF9's central role could be further explored. Regarding the developmental abnormalities of granulosa cells in the conditional knockout model, their pathological origins require in-depth analysis to determine whether they represent primary alterations or secondary adaptive responses resulting from the loss of oocyte signaling.

eLife Assessment

This important study combines cryo-EM, biochemical, and cell-based assays to examine how Gβγ interacts with and potentiates PLCβ3. The authors present evidence for multiple Gβγ interaction surfaces and argue that Gβγ primarily enhances PLCβ3 activity after membrane recruitment rather than serving mainly as a membrane-recruitment factor. The evidence is solid overall, although uncertainty remains about the physiological relevance and precise arrangement of the proposed interfaces because the structural model relies on engineered crosslinking.

Reviewer #1 (Public review):

The manuscript by Fisher et al describes the molecular mechanism underlying how G beta gamma subunits engage with the beta 3 isoform of PLC. The paper used a combination of cryo EM, BRET assays, and biochemical assays of PLC beta activity. A key discovery is that G beta gamma is not sufficient to drive membrane binding by itself, and instead promotes G alpha activation. The work is important, but suffers slightly from some ambiguity in the actual interface that is present in their cryo EM model, as crosslinkers could stabilise a transient and non-native complex. This is somewhat abrogated by the careful mutational analysis, which shows that mutation of any of these three sites does somewhat block PLC beta G beta gamma activation. However, there could be some improvement in the presentation of this data, as well as possible mutant selection. Overall, this paper is a nice complement to the Falzone et al paper, showing the membrane-bound complex of PLCB3 on membranes, with this work building on this work, highlighting the importance this will have in our full understanding of PLC beta activation.

Major concerns:

My biggest concern is the potential that this interface is artefactual based on the crosslinking strategy utilised. Here are thoughts on how this could be better validated, presented in a more convincing way.

(1) The authors' main claim is that there is a degree of plasticity of G beta gamma binding to the PLC beta 3 isoform, with three possible binding sites. The main complication of this is, of course, the possibility that the crosslinking stabilises a non-native complex, driven by a mutated cysteine.

Because of this, any other additional details about this interface are going to be critical for the scientific audience to judge if this is accurate.

What would greatly help Figure 1 is an evolutionary conservation analysis of the novel Gbg interface in PLC, to see how well this is conserved, and compare this to the conservation of the previously annotated sites. Conservation of these sites on both the G beta gamma and PLC side would help justify this as a native complex.

This will also help orient the reader to the identity of the mutated residues assayed in Figure 3.

(2) The g beta gamma orientation is also different than what I have observed in previous g beta gamma effector structures. Is there any precedent for this as an effector interface? A supplemental figure comparing this structure to other g beta gamma interfaces from other enzymes, for example recent Tesmer structure with PI3K.

(3) The mutational analysis in Figure 2D-G seems to give some strange results, and I have some question why certain residues were chosen rather than others. Mutation of the Gbg side will be more complicated, as of course that can affect any of the three surfaces. My main question is that, from the way Figure 2A is oriented, the main salt bridge in their novel interface to me looks like R199-D228, with K183 being in the wrong orientation to E226, and D167 being far from any charged residues. Why did the authors not make the corresponding R199 to D or E mutation?

(4) To help the reader's interpretation of Figure 2A, I would recommend a supplemental figure showing the density for interfacial residues, as that also would increase confidence in the interface.

Reviewer #2 (Public review):

In this manuscript, the authors dissect how Gβγ potentiates PLCβ3 signaling in cells. Using engineered crosslinking to stabilize a Gβγ-PLCβ3 complex, single particle cryo-EM, and cell-based functional assays, they identify and map multiple putative Gβγ interaction surfaces on PLCβ3, including a previously unrecognized binding mode. Structure-guided mutagenesis supports the functional relevance of these interactions and suggests that Gβγ potentiation is not primarily mediated by PLCβ3 membrane recruitment, but instead enhances PLCβ3 activity after the lipase is already at the membrane.

Previous reconstitution work on the membrane surface (Falzone & MacKinnon, 2023) proposed a recruitment/partitioning-centric model in which Gβγ increases PLCβ3 output largely by elevating its membrane surface concentration, whereas Gαq primarily increases catalytic turnover; under those reconstitution conditions, the two inputs can combine approximately multiplicatively. In receptor-driven cellular signaling, however, PLCβ3 is robustly recruited to the plasma membrane upon Gαq activation, which raises the question of whether Gβγ contributes mainly through additional recruitment or through a post-recruitment mechanism once PLCβ3 is already at the membrane.

This manuscript helps address that gap by using membrane-anchored PLCβ3 and complementary cellular readouts to separate "getting PLCβ3 to the membrane" from "boosting activity once PLCβ3 is already there." Their results argue that, in cells, membrane recruitment is largely dominated by Gαq·GTP, while Gβγ can further potentiate PIP2 hydrolysis after membrane association, consistent with a modulatory role at the membrane rather than primary recruitment.

Overall, the work provides a structural and mechanistic framework for Gβγ-PLCβ3 cooperation and helps clarify the basis of Gq pathway amplification. The manuscript is generally strong, but some issues need to be addressed.

Major comments:

(1) BMOE/BM(PEG)2 crosslinking may enforce a non-native docking geometry, potentially compromising the physiological relevance and precision of the Gβγ-PLCβ3 interface as described. Although a >50% 1:1 crosslinked complex is formed and remains active, the solution maps show lower local resolution for Gβγ, consistent with a dynamic, potentially heterogeneous, interface. One interface is captured via a single engineered cysteine pair (PLCβ3 E60C-Gβ C271), which could potentially bias the pose. It would be helpful if the authors could provide additional orthogonal support (e.g., alternative crosslinked sites) and bolster the clarification of its uniqueness and relevance.

(2) In the crosslinked structure, the authors report that GβD228 interacts with PLCβ3 R199 and K183. In Figure 2A, R199 appears closer to Gβ D228 than K183, yet only K183 is functionally tested. Testing R199 (e.g., R199E/R199A) would strengthen the structure-guided validation of this interface.

(3) The mutagenesis strategy appears inconsistent across figures/assays, which makes it difficult to interpret phenotypes and directly link the functional data to the proposed interfaces. For example, in Figure 2E, we see R185L but R215E, while residue L40 is mutated to Gly in the IP accumulation assays but to Glu/Lys (L40E/K) in the BRET assays (Figures 3B/3D/3F). The authors should (i) clearly justify the rationale for each substitution (conservative vs charge-reversal, interface disruption, etc.) and (ii), where possible, test the same mutants across assays (or provide evidence that alternative substitutions yield consistent conclusions).

Reviewer #3 (Public review):

Summary:

PLCβ3 is activated by both Gαq and Gβγ subunits. This paper follows previous solutions and cryoEM studies of PLCβ3 / Gβγ, trying to understand the molecular details of activation using cellular BRET assays and cryoEM.

Strengths:

The authors find evidence for multiple binding sites on PLCβ3 for Gβγ and suggest that Gβγ is not bone fide activator per se but enhances Gαq activation by positioning the catalytic site towards substrate, although this is not completely convincing. Although these sites may not naturally be operative, the authors might want to develop the potential role of these sites.

The authors also find that this activation is not through recruitment of the enzyme to the membrane by Gβγ released upon G protein activation, in accord with other PLCβ enzymes, but not for PLCβ3, and again, the authors might want to develop this point further.

Weaknesses:

(1) I'm confused as to why the authors feel that their mechanism is distinct from the two-state enzyme, the synergistic activation proposed by Ross in 2011, using a primarily thermodynamic argument. As written, the authors appear to be very reliant on structural and BRET studies that do not give the details that would disprove this interpretation. The main issue is that the author's mechanism does not fully explain how Gβγ activation occurs for PLCβ2 in reconstituted systems in the absence of Gαq subunits.

(2) In a recent study, McKinnon presents a model showing that Gαq and Gβγ activate PLCβ3 by two distinct pathways and that activation by Gβγ occurs through membrane recruitment. It is not surprising that the authors find that this is not true since the pelleting method used by McKinnon is subject to error. The authors should directly address the limitations of this previous work and the changes in proteoliposomes with sedimentation that alter partition coefficients. Although the inability of Gβγ to drive membrane binding is in accord with the quantitative studies of Scarlata, showing that the affinity of PLCβ3 to Gβγ is fairly weak as compared to the intrinsic membrane partition coefficient.

(3) It was proposed many years ago that in signaling complexes Gαq - Gβγ may not have to fully dissociate when binding PLCβ, but rather shift their relative orientation when binding to PLCβ to allow activation. Is their model consistent with this? Is it possible that PLCβ3 keeps Gβγ from diffusing to enhance the rate of Gq / Gβγ re-association?

(4) The authors find that Gβγ binds multiple sites, and it is clear that the PH domain site is the primary one in accord with previous work. Could these weaker sites be an artifact of the elevated concentrations used in cryoEM and BRET assays?

(5) Although their assays infer differences in binding affinities, it would strengthen the paper if the authors could estimate the association energies of these different binding sites. This estimation would also address the concern stated above.

Author Response:

Public Reviews:

Reviewer #1 (Public review):

The manuscript by Fisher et al describes the molecular mechanism underlying how G beta gamma subunits engage with the beta 3 isoform of PLC. The paper used a combination of cryo EM, BRET assays, and biochemical assays of PLC beta activity. A key discovery is that G beta gamma is not sufficient to drive membrane binding by itself, and instead promotes G alpha activation. The work is important, but suffers slightly from some ambiguity in the actual interface that is present in their cryo EM model, as crosslinkers could stabilise a transient and non-native complex. This is somewhat abrogated by the careful mutational analysis, which shows that mutation of any of these three sites does somewhat block PLC beta G beta gamma activation. However, there could be some improvement in the presentation of this data, as well as possible mutant selection. Overall, this paper is a nice complement to the Falzone et al paper, showing the membrane-bound complex of PLCB3 on membranes, with this work building on this work, highlighting the importance this will have in our full understanding of PLC beta activation.

Thank you for the positive feedback.

Major concerns:

My biggest concern is the potential that this interface is artefactual based on the crosslinking strategy utilised. Here are thoughts on how this could be better validated, presented in a more convincing way.

(1) The authors' main claim is that there is a degree of plasticity of G beta gamma binding to the PLC beta 3 isoform, with three possible binding sites. The main complication of this is, of course, the possibility that the crosslinking stabilises a non-native complex, driven by a mutated cysteine.

Because of this, any other additional details about this interface are going to be critical for the scientific audience to judge if this is accurate.

What would greatly help Figure 1 is an evolutionary conservation analysis of the novel Gbg interface in PLC, to see how well this is conserved, and compare this to the conservation of the previously annotated sites. Conservation of these sites on both the G beta gamma and PLC side would help justify this as a native complex.

This will also help orient the reader to the identity of the mutated residues assayed in Figure 3.

We agree that crosslinking can result in the capture a non-physiologically relevant interface. However, we do not observe any crosslinking between Gbg and a PLCb3 variant that retains a cysteine in the disordered region of the X–Y linker, nor crosslinking between PLCb3 and any other cysteine present in the Gbg heterodimer. The evolutionary conservation analysis is a great suggestion and will included in the revision for both Gbg and PLCb.

(2) The g beta gamma orientation is also different than what I have observed in previous g beta gamma effector structures. Is there any precedent for this as an effector interface? A supplemental figure comparing this structure to other g beta gamma interfaces from other enzymes, for example recent Tesmer structure with PI3K.

Yes, this is not the more typically observed Gbg–effector interaction, which is mediated by the narrow face of the Gbgtoroid. We are not aware of other structures in which Gbg interacts with a binding partner in the same way. A supplemental figure comparing this Gbg–PLCb interaction to the Gbg–PI3K and Gbg–GRK2 structures will be included in the revision.

(3) The mutational analysis in Figure 2D-G seems to give some strange results, and I have some question why certain residues were chosen rather than others. Mutation of the Gbg side will be more complicated, as of course that can affect any of the three surfaces. My main question is that, from the way Figure 2A is oriented, the main salt bridge in their novel interface to me looks like R199-D228, with K183 being in the wrong orientation to E226, and D167 being far from any charged residues. Why did the authors not make the corresponding R199 to D or E mutation?

Thank you for pointing this out. We are in the process of testing the PLCb3 R199E mutant in our assays and will include the results in the revised manuscript.

(4) To help the reader's interpretation of Figure 2A, I would recommend a supplemental figure showing the density for interfacial residues, as that also would increase confidence in the interface.

Thank you for the suggestion, this will be included in the revised manuscript.

Reviewer #2 (Public review):

In this manuscript, the authors dissect how Gβγ potentiates PLCβ3 signaling in cells. Using engineered crosslinking to stabilize a Gβγ-PLCβ3 complex, single particle cryo-EM, and cell-based functional assays, they identify and map multiple putative Gβγ interaction surfaces on PLCβ3, including a previously unrecognized binding mode. Structure-guided mutagenesis supports the functional relevance of these interactions and suggests that Gβγ potentiation is not primarily mediated by PLCβ3 membrane recruitment, but instead enhances PLCβ3 activity after the lipase is already at the membrane.

Previous reconstitution work on the membrane surface (Falzone & MacKinnon, 2023) proposed a recruitment/partitioning-centric model in which Gβγ increases PLCβ3 output largely by elevating its membrane surface concentration, whereas Gαq primarily increases catalytic turnover; under those reconstitution conditions, the two inputs can combine approximately multiplicatively. In receptor-driven cellular signaling, however, PLCβ3 is robustly recruited to the plasma membrane upon Gαq activation, which raises the question of whether Gβγ contributes mainly through additional recruitment or through a post-recruitment mechanism once PLCβ3 is already at the membrane.

This manuscript helps address that gap by using membrane-anchored PLCβ3 and complementary cellular readouts to separate "getting PLCβ3 to the membrane" from "boosting activity once PLCβ3 is already there." Their results argue that, in cells, membrane recruitment is largely dominated by Gαq·GTP, while Gβγ can further potentiate PIP2 hydrolysis after membrane association, consistent with a modulatory role at the membrane rather than primary recruitment.

Overall, the work provides a structural and mechanistic framework for Gβγ-PLCβ3 cooperation and helps clarify the basis of Gq pathway amplification. The manuscript is generally strong, but some issues need to be addressed.

Thank you for the positive comments.

Major comments:

(1) BMOE/BM(PEG)2 crosslinking may enforce a non-native docking geometry, potentially compromising the physiological relevance and precision of the Gβγ-PLCβ3 interface as described. Although a >50% 1:1 crosslinked complex is formed and remains active, the solution maps show lower local resolution for Gβγ, consistent with a dynamic, potentially heterogeneous, interface. One interface is captured via a single engineered cysteine pair (PLCβ3 E60C-Gβ C271), which could potentially bias the pose. It would be helpful if the authors could provide additional orthogonal support (e.g., alternative crosslinked sites) and bolster the clarification of its uniqueness and relevance.

We did attempt to isolate other crosslinked complexes. PLCb3-D892 self-crosslinked under all reaction conditions, while PLCb3-D892 XY_Cys , which retains an endogenous cysteine within the X–Y linker (C516), did not result in any crosslinked product when incubated with Gbg. Only the PLCb3-D892 E60C crosslinked to Gbg as confirmed by SDS-PAGE and SEC. All experiments also used wild-type Gb which contains two solvent-exposed cysteines in the effector binding site (C204 and C271). The greatest number of particles correspond to crosslinking between Gb C271 and E60C in PLCb3-D892. Crosslinking between PLCb3-D892 E60C and other residues in Gbg is possible, but there are not sufficient particle numbers corresponding to these species for 2D classing and reconstruction. These observations, together with the high efficiency of crosslinking, are consistent with a stable and persistent interaction.

(2) In the crosslinked structure, the authors report that GβD228 interacts with PLCβ3 R199 and K183. In Figure 2A, R199 appears closer to Gβ D228 than K183, yet only K183 is functionally tested. Testing R199 (e.g., R199E/R199A) would strengthen the structure-guided validation of this interface.

We agree, and functional analysis of PLCb3 R199E will be included in the revision.

(3) The mutagenesis strategy appears inconsistent across figures/assays, which makes it difficult to interpret phenotypes and directly link the functional data to the proposed interfaces. For example, in Figure 2E, we see R185L but R215E, while residue L40 is mutated to Gly in the IP accumulation assays but to Glu/Lys (L40E/K) in the BRET assays (Figures 3B/3D/3F). The authors should (i) clearly justify the rationale for each substitution (conservative vs charge-reversal, interface disruption, etc.) and (ii), where possible, test the same mutants across assays (or provide evidence that alternative substitutions yield consistent conclusions).

The mutagenesis experiments were initially carried out independently in the Lambert and Lyon groups. As the study progressed, additional mutations were designed based on prior results. The L40G mutation is one such example. Given its modest impact on activity in the IP accumulation assay, the L40E and L40K mutants designed to maximally disrupt the interface in the BRET experiments. The revision will include the rationale behind different substitutions and discussion of any potential differences.

Reviewer #3 (Public review):

Summary:

PLCβ3 is activated by both Gαq and Gβγ subunits. This paper follows previous solutions and cryoEM studies of PLCβ3 / Gβγ, trying to understand the molecular details of activation using cellular BRET assays and cryoEM.

Strengths:

The authors find evidence for multiple binding sites on PLCβ3 for Gβγ and suggest that Gβγ is not bone fide activator per se but enhances Gαq activation by positioning the catalytic site towards substrate, although this is not completely convincing. Although these sites may not naturally be operative, the authors might want to develop the potential role of these sites.

The authors also find that this activation is not through recruitment of the enzyme to the membrane by Gβγ released upon G protein activation, in accord with other PLCβ enzymes, but not for PLCβ3, and again, the authors might want to develop this point further.

Thank you for the suggestions.

Weaknesses:

(1) I'm confused as to why the authors feel that their mechanism is distinct from the two-state enzyme, the synergistic activation proposed by Ross in 2011, using a primarily thermodynamic argument. As written, the authors appear to be very reliant on structural and BRET studies that do not give the details that would disprove this interpretation. The main issue is that the author's mechanism does not fully explain how Gβγ activation occurs for PLCβ2 in reconstituted systems in the absence of Gαq subunits.

The reconstitution experiments rely on nM-mM concentrations of purified proteins and liposomes that contain up to 30% PI (4,5)2. PLCb2 and PLCb3 show dose-dependent increases in activity with increasing concentrations of Gbg. PLCb enzymes that interact with the liposomes would encounter liposome-tethered Gbg subunits, which would in turn bind the lipase, tethering to the membrane and helping position the active site for catalysis. While there is not yet experimental evidence that Gbg binding can displace the Ha2’ helix, it could facilitate interfacial activation given the net negative charge of PI (4,5) P2. In addition, PLCb2 is fundamentally different from the other PLCb isoforms in its sensitivity to heterotrimeric G proteins. Given its decreased sensitivity to Ga_q and increased basal activity, it is possible that autoinhibition by the proximal CTD is weaker. PLCb2 is also abundantly expressed in neutrophils, along with more Gi-coupled receptors. Thus, it is possible that Gbg directly activates PLCb2 in these cells, but future experiments are required to definitively answer this question.

(2) In a recent study, McKinnon presents a model showing that Gαq and Gβγ activate PLCβ3 by two distinct pathways and that activation by Gβγ occurs through membrane recruitment. It is not surprising that the authors find that this is not true since the pelleting method used by McKinnon is subject to error. The authors should directly address the limitations of this previous work and the changes in proteoliposomes with sedimentation that alter partition coefficients. Although the inability of Gβγ to drive membrane binding is in accord with the quantitative studies of Scarlata, showing that the affinity of PLCβ3 to Gβγ is fairly weak as compared to the intrinsic membrane partition coefficient.

Thank you for raising this point. The changes in composition, size, and structure when pelleting proteoliposomes may complicate data interpretation and will be discussed in the revision.

(3) It was proposed many years ago that in signaling complexes Gαq - Gβγ may not have to fully dissociate when binding PLCβ, but rather shift their relative orientation when binding to PLCβ to allow activation. Is their model consistent with this? Is it possible that PLCβ3 keeps Gβγ from diffusing to enhance the rate of Gq / Gβγ re-association?

The crosslinked complex is compatible with simultaneous binding of a Gbg –Gbg heterotrimer to the PLCb3 without disrupting the observed interface. It is possible that Gbg could interact with Gbg bound to the PH domain or the EF hands in the previously reported reconstruction. If so, the interaction would be mediated by the N-terminal helix of Gbg. Alternatively, the intrinsic GAP activity of PLCb3 may also prevent Gbg from diffusing to promote heterotrimer reassociation.

(4) The authors find that Gβγ binds multiple sites, and it is clear that the PH domain site is the primary one in accord with previous work. Could these weaker sites be an artifact of the elevated concentrations used in cryoEM and BRET assays?

Assuming the PH domain is the primary Gbg binding site, it is possible that the secondary EF hand site observed by Falzone and Mackinnon reflects high protein concentrations. However, it seems unlikely that we would reach these concentrations within cells. Our functional data is also consistent with the Gbg binding site in the EF hands playing a functional role in increasing PLCb activity.

(5) Although their assays infer differences in binding affinities, it would strengthen the paper if the authors could estimate the association energies of these different binding sites. This estimation would also address the concern stated above.

We appreciate this suggestion and will keep it in mind as we complete the revision.

eLife Assessment

Kim et al. provide important findings explaining how T3SS assembly is regulated by a conserved genetic context. The evidence supporting the conclusions is compelling, with numerous experiments demonstrating the validity of the findings. The work will be of interest to molecular biologists, biochemists, and microbiologists working on secretion systems or similar complexes. Further studies revealing similar mechanisms in other systems would enhance the impact of the current study.

Reviewer #1 (Public review):

Summary:

The authors set out to understand the complex regulation of the assembly of the Type 3 Secretion System of S. typhimurium. They found that the gene synteny as well as specific mRNA stem loops were important for the translational coupling of sctS and sctT. Without this regulation, SctT self-oligomerizes, which disrupts the export of effector proteins and leads to a decreased fitness of the pathogen. The work was done using a variety of convincing methods and leads to an updated picture of how T3SS assembly occurs. Since the same genetic synteny is found in a large majority of T3SS in different bacteria, it is likely that this is a general mechanism, but one that needs to be further experimentally validated.

Strengths:

The paper uses an impressive amount of experiments, with different techniques, to describe how they identified the genetic regulation of SctT production.

Weaknesses:

Only minor weaknesses are found.

(1) Regarding the use of the complex being unique. It is not well explained what makes this a unique complex.

(2) The paper would benefit from a discussion regarding how regulation might work in the minority of bacterial strains where the T3SS gene synteny is largely different. One would expect that those bacteria would have a different way of regulating T3SS assembly, but that is not discussed at all by the authors.

Reviewer #2 (Public review):

Summary:

In this manuscript, Samuel Wagner and colleagues describe an elegant mechanism to prevent promiscuous assembly of a core virulence type III secretion system protein, SctS. Starting from a bioinformatic standpoint, they demonstrate that synteny is highly conserved, and sctT occurs immediately downstream of sctS. Secretion is greatly reduced when sctT is removed or scrambled from its genomic context, and sctT expression is accordingly reduced (sctS synteny is also important, though less so). The distance between sctS and sctT is crucial. An elegant series of genetic experiments leads the authors to pinpoint a stem loop structure that occludes the Shine-Dalgarno sequence of sctT. This property is independent of the actual gene preceding sctT. In sum, this means that SctS is already expressed before SctT is expressed, preventing SctT from forming cytotoxic homooligomers.

Strengths:

The manuscript is very well-written, easy to follow, and describes a substantial amount of genetic detective work to identify the underlying mechanism. I have only a number of textual suggestions, mainly for the Introduction text, which I believe could be revised for a flagellar and broader audience.

Weaknesses:

Major concern:

While the work is rigorous and substantial, I am unsure as to whether its findings will appeal beyond a niche audience.

Minor points:

(1) Line 117: The number here seems to be very small. RefSeq has ~200,000 genomes. My guess is that at least 100,000 of these will be bacterial. Many (most?) bacteria have flagella, and some unflagellated strains have injectisomes, meaning I would have guessed that the authors would have ~50,000 genomes with SctRSTU. This estimate is error-prone, but not by too much. Can the authors explain the discrepancy between my estimate and their figure of almost two orders of magnitude? (SctRSTU/FliPQGFlhB should also be easy to pick up by sequence searches, so I don't think this is due to false negatives).

(2) Discussion: I would appreciate some discussion of how species that do not conserve the synteny of sctS and sctT prevent problems of sctT oligomerisation? It doesn't need to be evidence-based at this stage, but I'm sure the authors have thought about this, and the Discussion is an appropriate place to share their speculations.

Reviewer #3 (Public review):

At the core of the bacterial type III secretion system (T3SS), a nanomachine used to inject effector proteins into eukaryotic cells, five highly conserved proteins, SctRSTUV, form the export apparatus, which is the actual gate for effector proteins. Not only are these proteins the most strongly conserved parts of the system, but also their gene order is conserved, which is not the case for most other components of the T3SS. Interestingly, this order does not completely recapitulate the assembly order, which is SctR5-T4-S-U-V. Looking into the reasons for the conserved synteny, the authors noted a stem-loop in the mRNA of the Salmonella SPI-1 sctS gene, which is present in many other T3SS as well (and in fact had been found in Yersinia before). They then use an array of clever gene permutations and modifications to discern the benefit of this order for the bacteria. The combination of thorough sequence analysis with different, partly quantitative, protein expression and secretion assays and growth curves, both in the native Salmonella background and in heterologous systems, provides strong evidence for the interpretation of the authors: The stem-loop in sctS prevents the premature expression of SctT, which can otherwise assemble into "futile multimers" that can lead to ion loss. The presence of stem-loops in many other sctS/T genes gives weight to this finding.

This is a very nice and thorough study addressing an important point in the assembly of type III secretion systems. I only have a few suggestions.

(1) Conserved gene orders have been shown for many complexes, and the findings presented in this manuscript might be applicable to other membrane complexes.

The conservation of gene order and the presence of the stem loop give weight to the authors' findings. However, it is only mentioned quite late in the discussion that a similar stem loop was found in Yersinia upstream sctT earlier, and was interpreted differently. The authors' current discussion is somewhat evasive on this point. Why would these similar structures be used differently? Why would temperature not play a role in Salmonella SPI-1? And wouldn't the stem-loop also couple sctS and sctT expression in Yersinia? This should be addressed, if possible, by experiments (at least, the influence of temperature on the SPI-1 mRNA structure should be testable for the authors) and by a more detailed discussion (given the redundancy of RNA thermometers in the Yersinia T3SS, the interpretation in the current paper might well be the more compelling one).

(2) A point that deserves more attention is that a similar finding in Yersinia has been interpreted differently before (as a temperature sensor rather than translational coupling) - are these systems really different? Testing the different interpretations in the respective other system (at least the influence of temperature in the Salmonella SPI-1 system used in this manuscript) would have made the interpretation even more compelling.

(3) Another point that should be discussed in more detail is why this mechanism is present when replacement of the sctT ATG by weaker start codons and the simple omission of a separate SD sequence upstream sctT would achieve the same outcome. This could be tested in one of the nice heterologous systems, as used in Figure 4.

eLife Assessment

This valuable study presents a comparative dataset on crab locomotion to examine the evolution of sideways walking. The evidence supporting the authors' claims is largely convincing. This work will be of interest to researchers in animal locomotion.

Reviewer #1 (Public review):

Summary:

This is an interesting and well-written manuscript in which the authors set out to answer a simple, old question with a modern toolkit: where in crab evolution did sideways walking arise, how often has it been lost or regained, and is it plausibly linked to the ecological and taxonomic success of true crabs. To do this, they record locomotion from 50 live species, convert each species' movements into a quantitative index that compares forward versus sideways bouts, and then map the resulting states onto a recent crab phylogeny to infer the most likely evolutionary history of locomotor direction.

Strengths:

The strongest part of the study is the dataset itself. Comparable behavioral measurements across dozens of crab species are rare. The authors have done the field and husbandry work needed to make this possible. The overall pattern they recover, that most true crabs are strongly biased toward sideways movement (while a smaller set of lineages move predominantly forward), is interesting and likely to be useful to others. The phylogenetic mapping is also a reasonable way to address the "how many times" question (although this is peripheral to my expertise). The manuscript makes a convincing case that sideways locomotion is not simply a trivial byproduct of a crab-like body plan.

Weaknesses:

Where I am less convinced is in how strongly the authors describe the discreteness of the behavioral categories and the absence of intermediates. The manuscript states that the Forward-Sideways Index shows a clear separation between two locomotor types with little evidence for intermediates, and it cites a statistical test rejecting a single peak in the distribution. However, the histogram in Figure 3 appears structured within each labeled category, with subclusters inside both the forward and sideways groups rather than a single tight peak per group. This matters because the index is built by first placing each movement bout into "forward" versus "sideways" bins using a fixed angle boundary and then collapsing the result into a single ratio. That approach is simple and transparent enough, but it can also hide mixed strategies. For example, a species that produces substantial amounts of both forward and sideways walking can still end up with a strongly positive or negative index, and therefore be classified as a pure "type," even though the underlying behavior is mixed. In that context, rejecting a single peak in the across-species distribution does not, by itself, justify the stronger claim that intermediates are rare or absent.

Related to this, a key methodological choice is the use of 60 degrees as the cutoff between forward and sideways bouts. This boundary may be reasonable as a convention, but the paper does not explain why it is the right place to draw the line, and there is a plausible biological concern that a fixed angular cutoff does not mean the same thing across taxa.

Crabs vary in body shape and in how the legs are arranged around the body. In my own comparative work, for example, some species show an elliptical stance pattern elongated along the preferred direction of travel, while others show a more circular leg arrangement, and the latter can express more mixed forward and sideways behavior. When limb arrangement and body geometry differ across species, the same measured angle can correspond to different underlying mechanics and different functional "degree of sidewaysness." The practical implication is that the reported binary separation may partly reflect the imposed classification rule, rather than a sharp biological divide.

Another limitation that affects interpretation is the decision to use one individual per species. I understand the logistics, and for some questions, a single representative individual can be a reasonable first pass. But it is not strong support for negative claims about intermediates, especially in a group where individuals can change substantially with growth and allometry. Crabs can grow dramatically, often with pronounced allometric shifts in limb proportions that can alter the center of mass location. Size alone can alter the kinematics and choice of locomotor behaviors in crustaceans. In species where appendage proportions change with size, or where certain legs become disproportionately large (or calcified), it is plausible that locomotor direction and the distribution of movement angles shift across ontogeny. That makes it hard to treat a single individual as a complete description of a species-level strategy, particularly for species that fall closer to the boundary between categories.

In sum, this is a valuable and useful behavioral comparative study with a dataset that many in the field will appreciate. The main conclusions about the likely evolutionary placement of sideways walking are plausible, but several of the stronger claims about discrete locomotor types, the absence of intermediates, and the relationship to diversification would be more convincing if the analysis were less dependent on a fixed angular cutoff and on single individuals per species, or if the manuscript framed those points more cautiously so the conclusions track the strength of the evidence.

Reviewer #2 (Public review):

Summary:

The current work investigates the evolution of sideward locomotion in Brachyura in light of a single evolutionary origin. To this end, the authors first analysed the mode of locomotion in 50 crab species and observed mutually exclusive presence of sideways vs. forward movement. The phylogenetic analysis confirmed that there is indeed a single evolutionary origin for sideways movement, which was sometimes followed by several reversions to forward locomotion. This way, authors demonstrate how locomotor movement modes shape evolutionary diversification in animals by showing that species richness is much higher in side-ways-moving crabs than in the nearest groups. This is an interesting work that integrates behavioural analysis and phylogenetic relations, capitalising largely on crabs. I have a few suggestions and questions.

Firstly, I think the paper spends too much time on a straightforward analysis of the mode of locomotion. I was also wondering whether the phylogenetic analysis could be simply achieved by maximising an objective function in which the modes of movement are inversely coded for two putative groups, with all values calculated at all possible nodes.

Unfortunately, I find that the authors did not sufficiently discuss differences in the ecological niches of species with forward vs. sideways locomotion modes (including challenges of locomotion and substrate).

Likewise, what are the anatomic correlates of forward vs. sideways locomotion? For instance, how are the advantages assumed for sideways movement associated with a flattened body? Is it possible that the mode of motion is secondary to flattened/narrow body structure, which basically limits the distance between legs and thus makes the forward movement difficult - under this logic, the mode of movement would be a secondary phenomenon to body shape traits. How can one differentiate between this alternative and the one that puts the mode of movement in the centre of the story? On a related note, how do different modes of movement relate to the ability to fit into tight spaces - how does it relate to differences in leg joints?

Is it possible that the sideways movement maximises the scanned visual field per unit time/displacement, which may be beneficial for mostly forward-moving predators?

It is really difficult to decipher the information contained in the nodes (circles) in the printed black-and-white version of the manuscript.

Briefly, although I find the study interesting, the presented complexity may not be necessary given the endpoints; it can be achieved much more simply. Furthermore, the degree to which the conceptual analysis of different modes of locomotion was exercised was limited. The general approach may serve as a good model for the evolutionary analysis of other traits. The demonstration of traceability of the relations in question is a major contribution of the work.

Strengths:

The research question and the novel combination of different data types.

Weaknesses:

The complexity of the methods used, along with a limited discussion of the potential dynamics that may underlie the evolution of the sideways movement mode.

eLife Assessment

This important study shows that orientation tuning of V1 neurons is suppressed during a continuous flash suppression paradigm, especially in neurons with binocular receptive fields. These findings, made using cutting-edge imaging techniques, convincingly implicate early visual processing in continuous flash suppression, in agreement with previous studies suggesting reduced effective contrast of such stimuli in V1.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have submitted a second revision, largely to address a comment from Reviewer 2, which was "The failure to model the neural data with an explicit model is a missed opportunity." The authors have now included a computational model.]

This study makes a fundamental contribution to our understanding of interocular suppression, particularly continuous flash suppression (CFS). Using neuroimaging data from two macaque monkeys, the study provides compelling evidence that CFS suppresses orientation responses in neurons within V1. These findings enrich the CFS literature by demonstrating that neural activity under CFS may prevent high-level visual and cognitive processing.

Comments on previous revisions:

The authors have addressed all my previous comments.

Reviewer #2 (Public review):

Summary:

The goal of this study was to investigate the degree to which low-level stimulus features (i.e., grating orientation) are processed in V1 when stimuli are not consciously perceived under conditions of continuous flash suppression (CFS). The authors measured the activity of a population of V1 neurons at single neuron resolution in awake fixating monkeys while they viewed dichoptic stimuli that consisted of an oriented grating presented to one eye and a noise stimulus to the other eye. Under such conditions, the mask stimulus can prevent conscious perception of the grating stimulus. By measuring the activity of neurons (with Ca2+ imaging) that preferred one or the other eye, the authors tested the degree of orientation processing that occurs during CFS.

Strengths:

The greatest strength of this study is the spatial resolution of the measurement and the ability to quantify stimulus representations during CSF in populations of neurons preferring the eye stimulated by either the grating or the mask. There have been a number of prominent fMRI studies of CFS, but all of them have had the limitation of pooling responses across neurons preferring either eye, effectively measuring the summed response across ocular dominance columns. The ability to isolate separate populations offers an exciting opportunity to study the precise neural mechanisms that give rise to CFS, and potentially provide insights into nonconscious stimulus processing.

Weaknesses:

(The authors have now included a computational model in the second revision.)

Reviewer #3 (Public review):

Summary:

In this study, Tang, Yu & colleagues investigate the impact of continuous flash suppression (CFS) on the responses of V1 neurons using 2-photon calcium imaging. The report that CFS substantially suppressed V1 orientation responses. This suppression happens in a graded fashion depending on the binocular preference of the neuron: neurons preferring the eye that was presented with the marker stimuli were most suppressed, while the neurons preferring the eye to which the grating stimuli were presented were least suppressed. Binocular neuron exhibited an intermediate level of suppression.

Strengths:

The imaging techniques are cutting-edge.

Weaknesses:

The strength of CFS suppression varies across animals, but the authors attribute this to comparable heterogeneity in the human psychophysics literature.

Comments on previous revisions:

The authors have addressed my comments from the previous round of review, and I have no further comments.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

This study makes a fundamental contribution to our understanding of interocular suppression, particularly continuous flash suppression (CFS). Using neuroimaging data from two macaque monkeys, the study provides compelling evidence that CFS suppresses orientation responses in neurons within V1. These findings enrich the CFS literature by demonstrating that neural activity under CFS may prevent high-level visual and cognitive processing.

Comments on revisions:

The authors have addressed all my previous comments.

Thanks for the very warm comments!

Reviewer #2 (Public review):

Summary:

The goal of this study was to investigate the degree to which low-level stimulus features (i.e., grating orientation) are processed in V1 when stimuli are not consciously perceived under conditions of continuous flash suppression (CFS). The authors measured the activity of a population of V1 neurons at single neuron resolution in awake fixating monkeys while they viewed dichoptic stimuli that consisted of an oriented grating presented to one eye and a noise stimulus to the other eye. Under such conditions, the mask stimulus can prevent conscious perception of the grating stimulus. By measuring the activity of neurons (with Ca2+ imaging) that preferred one or the other eye, the authors tested the degree of orientation processing that occurs during CFS.

Strengths:

The greatest strength of this study is the spatial resolution of the measurement and the ability to quantify stimulus representations during CSF in populations of neurons preferring the eye stimulated by either the grating or the mask. There have been a number of prominent fMRI studies of CFS, but all of them have had the limitation of pooling responses across neurons preferring either eye, effectively measuring the summed response across ocular dominance columns. The ability to isolate separate populations offers an exciting opportunity to study the precise neural mechanisms that give rise to CFS, and potentially provide insights into nonconscious stimulus processing.

Weaknesses:

However, while this is an impressive experimental setup, the major weakness of this study is that the experiments don't advance any theoretical account of why CFS occurs or what CFS implies for conscious visual perception. There are two broad camps of thinking with regard to CFS. On the one hand, Watanabe et al., 2011 reported that V1 activity remained intact during

CFS, implying that CFS interrupts stimulus processing downstream of V1. On the other hand, Yuval-Greenberg and Heeger (2013) showed that V1 activity is in fact reduced during CFS. By using a parametric experimental design, they measured the impact of the mask on the stimulus response as a function of contrast, and concluded that the mask reduces the gain of neural responses to the grating stimulus. They presented a theoretical model in which the mask effectively reduced the SNR of the grating, making it invisible in the same way that reducing contrast makes a stimulus invisible.

In the first submission of the manuscript, the authors incorrectly described the Yuval-Greenberg & Heeger (2013) paper and Watanabe et al. (2011) papers, suggesting that they had observed the same or similar effects of CFS on V1 activity, when in fact they had described opposite results. Reviewer 1 also observed that the authors appeared to be confused in their reading of these highly relevant papers. In the revision, the authors have reworked this paragraph, now correctly describing these sets of opposing results. However, I still do not understand what the authors are trying to argue: "...these studies were not designed to quantify the pure effect of CFS on stimulus-evoked V1 responses." I do not understand what is meant by "pure" in this case.

This is clarified as: “Nevertheless, these studies contrasted monocular and dichoptic masking conditions to equate stimulus input while manipulating perceptual visibility, which were not designed to quantify the pure effect of CFS on stimulus-evoked V1 responses, that is, the difference of BOLD signals between binocular masking and stimulus alone conditions.” (line 63)

Regardless, it is clear that the measurements in the present study strongly support the interpretation of Yuval-Greenberg & Heeger (i.e., that V1 activity is degraded by CFS, 'akin' to a loss in the contrast-to-noise ratio of neural activity). It would be appropriate for the authors to communicate this clearly.

We agree and added the following sentence in the text: “These results support the conclusion of Yuval-Greenberg and Heeger (2013) that V1 activity is degraded by CFS, ‘akin’ to a loss in the contrast-to-noise ratio of neural activity” (line 122)

I continue to be of the opinion that this study is lacking an adequate model of interocular interactions that might explain the Ca2+ imaging. The machine learning results are not terribly surprising - multivariate methods, such as SVMs, are more sensitive than univariate approaches. So it is plausible that an SVM can support decoding of the coarse orientation information, even when no tuning is evident in the univariate analyses. However, the link between this result and the underlying neurophysiology is opaque. The failure to model the neural data with an explicit model is a missed opportunity.

We agree and put “An ocular-dominance-dependent gain control model” back to the text. Fig. 2D now shows the results of model fitting.

(line 167)

An ocular-dominance-dependent gain control model

We developed an ocular dominance-dependent gain control model to account for the impact of CFS on V1 population orientation tuning. The model development followed two steps.

Step I. Population orientation tuning functions before CFS

The population orientation tuning functions due to monocular stimulation exhibited different amplitudes among OD groups (Fig. 2D, red curves), which could be simulated with Equation 1, an OD-weighted Gaussian basis function:

where parameters A, σ, and B corresponded to the amplitude, standard deviation, and minimal response of the Gaussian basis function, respectively, and θ represented the preferred orientation of a bin of neurons relative to the actual orientation of the grating stimulus. The weight parameter w was the mean of linearly transformed ODIs of neurons in a neuronal group, which equated to (ODI +1)/2 or 1 - (ODI + 1)/2, depending on contralateral or ipsilateral eye grating stimulation, and ranged from 0-1. Thus, a smaller w would indicate a higher preference for the eye seeing the grating, and a larger w would indicate a higher preference for the unstimulated eye (or the eye seeing the flashing masker under CFS). The w equated to 0.33, 0.50, and 0.67 in Monkey A, and 0.32, 0.5, and 0.68 in Monkey B, for the grating eye-preferring group, binocular group, and the masker eye-preferring group, respectively. The exponent s represented a nonlinear transformation.

Equation 1 fitted the baseline data well (Fig. 2D, red curves), resulting in goodness-of-fit (R²) values at 0.94 and 0.95 for the two monkeys, respectively. This indicated that the equation captured the OD-dependent population orientation tuning characteristics of V1 neurons with monocular stimulation before CFS.

Step II. The impacts of CFS

In step II, the model introduced several binocular combination factors to account for population orientation tuning functions under CFS.

To account for the OD-dependent changes of orientation tuning bandwidths under CFS, a w-dependent inhibition factor wt was introduced, which scaled the σ of the tuning functions, changing the monocular tunings R into R’:

This allowed different groups of neurons to exhibit various degrees of orientation tuning function broadening, capturing the pattern in which neurons preferring the eye seeing the grating displayed a sharper population orientation tuning curve under CFS than those preferring the eye seeing the masker.

Previous studies have shown that binocular neuronal responses can be modeled by incorporating interocular suppression and summation processes (Kato et al., 1981; Dougherty, Cox, Westerberg, & Maier, 2019; Zhang et al., 2024). Therefore, R’ was further normalized by the neural response to the flashing masker to simulate interocular suppression, which was the first component of Equation 3. Additionally, the neural response to the flashing masker was summed to simulate binocular summation, which was the second component of Equation 3. These two components when summed, determining the final neural responses under CFS:

where N was the empirical neural response to the monocularly presented flashing masker stimulation, a and b were scaling parameters, and k and m were nonlinearity parameters. The interocular normalization by masker response led to amplitude reduction of population orientation tuning functions for different groups of neurons, while the binocular summation with masker response elevated the minimal responses of tuning functions to their corresponding heights.

During the step II model fitting, the parameters A, σ, and s were inherited from the monocular tuning fits derived from Equation 1 and served as inputs, while the parameters a, k, b, m, and t were optimized. The model captured the CFS modulation on population orientation tuning curves well, with R2 = 0.99 and 0.98 for Monkeys A and B, respectively (Fig. 2D, red curves).

Reviewer #3 (Public review):

Summary:

In this study, Tang, Yu & colleagues investigate the impact of continuous flash suppression (CFS) on the responses of V1 neurons using 2-photon calcium imaging. The report that CFS substantially suppressed V1 orientation responses. This suppression happens in a graded fashion depending on the binocular preference of the neuron: neurons preferring the eye that was presented with the marker stimuli were most suppressed, while the neurons preferring the eye to which the grating stimuli were presented were least suppressed. Binocular neuron exhibited an intermediate level of suppression.

Strengths:

The imaging techniques are cutting-edge.

Weaknesses:

The strength of CFS suppression varies across animals, but the authors attribute this to comparable heterogeneity in the human psychophysics literature.

Comments on revisions:

The authors have addressed my comments from the previous round of review, and I have no further comments

Thanks!

eLife Assessment

The authors adapt sequencing of nascent DNA (DNA linked to an RNA primer, "SNS-Seq") to map DNA replication origins in Trypanosoma brucei. The main impact of this work is reporting a new set of putative origins, which do not overlap with previously reported origins, but which appear to overlap with previously mapped DNA-RNA hybrid (R-loops). Thus, these valuable findings open up new avenues for further investigation into the mechanistic basis for firing of replication forks in this organism. However, the supporting evidence remains incomplete and would benefit from orthogonal validation. This work will be of interest to those studying DNA replication and epigenetic regulation of fork origins.

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data. Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(i) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(ii) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping, across the whole genome, to ensure full understanding and clarity.

In the revised manuscript, the authors have improved the presentation and analysis of their data, expanding the description of SNS-seq mapping across the genome, and more clearly assessing to what extent there is correlation between SNS-seq signal and previous mapping approaches to predict origins (by MFA-seq and ChiP-chip of ORC1/CDC6). With regard the correlation between SNS-seq and ORC/1CDC6 ChIP-chip, it should be noted that two datasets were generated in distinct strains of T. brucei (Lister 427 and TREU927, respectively), and it is unclear if the latter dataset can be accurately mapped to the strain used here. Notwithstanding this concern, these improvements clarify a number of aspects of the SNS-seq mapping: (1) the signal is more prevalent in the transcribed core of the genome than in the largely transcriptionally silent subtelomeres; and (2) whereas previous work revealed strong correlation between ORC1/CDC6 localisation and MFA-seq peaks at the ends of multigene transcription units, neither of these data show significant overlap with SNS-seq signal, which is not seen at transcription start or stop sites ('SSRs'; supplementary Fig.8D) and shows marked depletion at predicted ORC1/CDC6 sites (supplementary Fig.8C). To the authors' credit, they acknowledge this lack of correlation in the discussion.

The authors have not provided any new data to substantiate their assertion that SNS-seq accurately detects origins in T. brucei, and therefore the work rests on a single experimental approach, without validation. As a result, the suggestion of abundant, previously undetected origins in the intergenic regions of multigene transcription remains a prediction. One key untested limitation of the work lies in the observation that the very large majority of SNS-seq signal overlaps with previously RNA-DNA hybrids; without an experimental test, the suggestion that the authors have 'disclosed for the first time a strong link between RNA:DNA hybrid formation and DNA replication initiation' remains conjecture.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of origins of replications. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Between the initial submission and this revision, the raised major concerns have not been resolved, and no additional validation has been provided.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript is concluded with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) There are substantial discrepancies between the origins identified here and those reported in previous studies. Given that the other studies precede this manuscript, it is the authors' duty to investigate these differences. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

(2) I am concerned that up to 96% percent of all SNS-seq peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Upon request, the authors have performed a control, where randomly placed peaks were run through the same filtering process. Only approximately twice as many experimental peaks passed filtering compared to random peaks. While the authors emphasize reproducibility between replicates, technical artifacts from the protocol would also be reproducible. Moreover, in other SNS-seq studies, for example, Pratto et al. Cell 2021, Fig. 1B, + and − strand peaks always appear closely paired. This pattern contrasts strongly with Fig. 2A in this manuscript.

Further, I have some minor concerns that do not affect the main conclusions of the manuscript:

- Fig 2C: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions. This data would be better presented with all regions stretched to the same size. This has not been addressed in the revision.

- Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length. This has not been addressed in the revision.

Are claims well substantiated?:<br /> The identification of origins via SNS-seq appears to be incompletely supported to me.<br /> All downstream analyses depend on the reliability of origin identification.

Impact:<br /> This study has the potential to be valuable for two fields: In research focused on T. brucei as a disease agent, where essential processes that function differently than in mammals are excellent drug targets. Further, this study would impact basic research analyzing DNA replication over the evolutionary tree, where T. brucei can be used as an early-divergent eucaryotic model organism.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data. Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(i) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(ii) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping, across the whole genome, to ensure full understanding and clarity.

In the revised manuscript, the authors have improved the presentation and analysis of their data, expanding the description of SNS-seq mapping across the genome, and more clearly assessing to what extent there is correlation between SNS-seq signal and previous mapping approaches to predict origins (by MFA-seq and ChiP-chip of ORC1/CDC6). With regard the correlation between SNS-seq and ORC/1CDC6 ChIP-chip, it should be noted that two datasets were generated in distinct strains of T. brucei (Lister 427 and TREU927, respectively), and it is unclear if the latter dataset can be accurately mapped to the strain used here. Notwithstanding this concern, these improvements clarify a number of aspects of the SNS-seq mapping: (1) the signal is more prevalent in the transcribed core of the genome than in the largely transcriptionally silent subtelomeres; and (2) whereas previous work revealed strong correlation between ORC1/CDC6 localisation and MFA-seq peaks at the ends of multigene transcription units, neither of these data show significant overlap with SNS-seq signal, which is not seen at transcription start or stop sites ('SSRs'; supplementary Fig.8D) and shows marked depletion at predicted ORC1/CDC6 sites (supplementary Fig.8C). To the authors' credit, they acknowledge this lack of correlation in the discussion.

The authors have not provided any new data to substantiate their assertion that SNS-seq accurately detects origins in T. brucei, and therefore the work rests on a single experimental approach, without validation. As a result, the suggestion of abundant, previously undetected origins in the intergenic regions of multigene transcription remains a prediction. One key untested limitation of the work lies in the observation that the very large majority of SNS-seq signal overlaps with previously RNA-DNA hybrids; without an experimental test, the suggestion that the authors have 'disclosed for the first time a strong link between RNANA hybrid formation and DNA replication initiation' remains conjecture.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of origins of replications. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Between the initial submission and this revision, the raised major concerns have not been resolved, and no additional validation has been provided.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript is concluded with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) There are substantial discrepancies between the origins identified here and those reported in previous studies. Given that the other studies precede this manuscript, it is the authors' duty to investigate these differences. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

We agree that orthogonally validation of origins detected by stranded SNS-seq is necessary and we are working on it.

(2) I am concerned that up to 96% percent of all SNS-seq peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Upon request, the authors have performed a control, where randomly placed peaks were run through the same filtering process. Only approximately twice as many experimental peaks passed filtering compared to random peaks. While the authors emphasize reproducibility between replicates, technical artifacts from the protocol would also be reproducible. Moreover, in other SNS-seq studies, for example, Pratto et al. Cell 2021, Fig. 1B, + and − strand peaks always appear closely paired. This pattern contrasts strongly with Fig. 2A in this manuscript.

The size and overlap of peaks depend on the length of the SNS. In our study, the width of the peaks corresponds to the size of the short nascent strands (0.5–2.5 kb) chosen as the starting material, whereas the width of the peaks in Pratto et al., Cell, 2021 are much larger (few kb). This could be due to the longer SNS used in the Pratto et al. study. Consequently, the overlap of the longer SNS is more pronounced since the SNS fibres elongate in both directions: at the 3′ end by DNA polymerase and at the 5′ end by ligation of Okazaki fragments. Additionally, the genomic regions displayed in our Figure 2A and in Pratto et al, Figure 1B are presented at substantially different resolutions, with a roughly ten‑fold difference in scale.

Further, I have some minor concerns that do not affect the main conclusions of the manuscript:

- Fig 2C: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions. This data would be better presented with all regions stretched to the same size. This has not been addressed in the revision.

As the reviewer suggested, we have produced scaled plots of the stranded SNS-seq origins over genic and intergenic regions (see Figure 3, which is attached along with the Reviewer #2 (Recommendations for the authors)). However, we would prefer to keep the unscaled versions in the manuscript and add a note in the text as part of the Version of Record, explaining that the origins are evenly distributed throughout intergenic regions rather than being centred within them.

- Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length. This has not been addressed in the revision.

This observation is correct. By applying filtering and setting the maximum distance between the positive and negative peaks, we are most likely affecting the average length by excluding potentially wider origins.

We'll modify the text as part of the Version of Record.

Are claims well substantiated?:

The identification of origins via SNS-seq appears to be incompletely supported to me.<br /> All downstream analyses depend on the reliability of origin identification.<br /> Impact:

This study has the potential to be valuable for two fields: In research focused on T. brucei as a disease agent, where essential processes that function differently than in mammals are excellent drug targets. Further, this study would impact basic research analyzing DNA replication over the evolutionary tree, where T. brucei can be used as an early-divergent eucaryotic model organism.

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

eLife Assessment

The authors use sequencing of nascent DNA (DNA linked to an RNA primer, "SNS-Seq") to localise DNA replication origins in Trypanosoma brucei, so this work will be of interest to those studying either Kinetoplastids or DNA replication. The paper presents the SNS-seq results for only part of the genome, and there are significant discrepancies between the SNS-Seq results and those from other, previously-published results obtained using other origin mapping methods. The reasons for the differences are unknown and from the data available, it is not possible to assess which origin-mapping method is most suitable for origin mapping in T. brucei. Thus at present, the evidence that origins are distributed as the authors claim - and not where previously mapped - is inadequate.

We would like to clarify a few points regarding our study. Our primary objective was to characterise the topology and genome-wide distribution of short nascent-strand (SNS) enrichments. The stranded SNS-seq approach provides the high strand-specific resolution required to analyse origins. The observation that SNS-seq peaks (potential origins) are most frequently found in intergenic regions is not an artefact of analysing only part of the genome; rather, it is a result of analysing the entire genome.

We agree that orthogonal validation is necessary. However, neither MFA-seq nor TbORC1/CDC6 ChIP-on-chip has yet been experimentally validated as definitive markers of origin activity in T. brucei, nor do they validate each other.

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data.

Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(1) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(2) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping across the whole genome to ensure full understanding and clarity.

Regarding comparisons with previous work:

- Two other attempts to identify origins in T. brucei - ORC1/CDC6 binding sites (ChIP-on-chip, PMID: 22840408) and MFA-seq (PMID: 22840408, 27228154) - were both produced by the McCulloch group. These methods do not validate each other; in fact, MFA-seq origins overlap with only 4.4% of the 953 ORC1/CDC6 sites (PMID: 29491738). Therefore, low overlap between SNS-seq peaks and ORC1/CDC6 sites cannot disqualify our findings. Similar low overlaps are observed in other parasites (PMID: 38441981, PMID: 38038269, PMID: 36808528) and in human cells (PMID: 38567819).

- We also would like to emphasize that the ORC1/CDC6 dataset originally published (PMID: 22840408) is no longer available; only a re-analysis by TritrypDB exists, which differs significantly from the published version (personal communication from Richard McCulloch). While the McCulloch group reported a predominant localization of ORC1/CDC6 sites within SSRs at transcription start and termination regions, our re-analysis indicates that only 10.3% of TbORC1/CDC6-12Myc sites overlapped with 41.8% of SSRs.

- MFA-seq does not map individual origins, it rather detects replicated genomic regions by comparing DNA copy number between S- and G1-phases of the cell cycle (PMID: 36640769; PMID: 37469113; PMID: 36455525). The broad replicated regions (0.1–0.5 Mbp) identified by MFA-seq in T. brucei are likely to contain multiple origins, rather than just one. In that sense we disagree with the McCulloch's group who claimed that there is a single origin per broad peak. Our analysis shows that up to 50% of the origins detected by stranded SNS-seq locate within broad MFA-seq regions. The methodology used by McCulloch’s group to infer single origins from MFA-seq regions has not been published or made available, as well as the precise position of these regions, making direct comparison difficult.

Finally, the genomic features we describe—poly(dA/dT) stretches, G4 structures and nucleosome occupancy patterns—are consistent with origin topology described in other organisms.

On the concern that SNS-seq may map RNA-DNA hybrids rather than replication origins: Isolation and sequencing of short nascent strands (SNS) is a well-established and widely used technique for high-resolution origin mapping. This technique has been employed for decades in various laboratories, with numerous publications documenting its use. We followed the published protocol for SNS isolation (Cayrou et al., Methods, 2012, PMID: 22796403). RNA-DNA hybrids cannot persist through the multiple denaturation steps in our workflow, as they melt at 95°C (Roberts and Crothers, Science, 1992; PMID: 1279808). Even in the unlikely event that some hybrids remained, they would not be incorporated into libraries prepared using a single-stranded DNA protocol and therefore would not be sequenced (see Figure 1B and Methods).

Furthermore, our analysis shows that only a small proportion (1.7%) of previously reported RNA-DNA hybrids overlap with SNS-seq origins. It is important to note that RNA-primed nascent strands naturally form RNA-DNA hybrids during replication initiation, meaning the enrichment of RNA-DNA hybrids near origins is both expected and biologically relevant.

On the claim that our analysis focuses narrowly on inter-CDS regions and ignores other genomic compartments: this is incorrect. We mapped and analyzed stranded SNS-seq data across the entire genome of T. brucei 427 wild-type strain (Müller et al., Nature, 2018; PMID: 30333624), including both core and subtelomeric regions. Our findings indicate that most origins are located in intergenic regions, but all analyses were performed using the full set of detected origins, regardless of location.

We did not ignore transcription start and stop sites (TSS/TTS). The manuscript already includes origin distribution across genomic compartments as defined by TriTrypDB (Fig. 2C) and addresses overlap with TSS, TTS and HT in the section “Spatial coordination between the activity of the origin and transcription”. While this overlap is minimal, we have included metaplots in the revised manuscript for clarity.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of the origins of replication. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript concludes with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

We sincerely thank you for this positive feedback.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

Thank you very much for this remark.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Thank you for appreciating our discussion.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) I do not understand why SNS-seq would create peaks. Replication should originate in one locus, then move outward in both directions until the replication fork moving outward from another origin is encountered. Hence, in an asynchronous population average measurement, I would expect SNS data to be broad regions of + and -, which, taken together, cover the whole genome. Why are there so many regions not covered at all by reads, and why are there such narrow peaks?

Thank you for asking these questions. As you correctly point out, replication forks progress in both directions from their origins and ultimately converge at termination sites. However, the SNS-seq method specifically isolates short nascent strands (SNSs) of 0.5–2.5 kb using a sucrose gradient. These short fragments are generated immediately after origin firing and mark the sites of replication initiation, rather than the entire replicated regions. Consequently: (i) SNS-seq does not capture long replication forks or termination regions, only the immediate vicinity of origins. (ii) The narrow peaks indicate the size of selected SNSs (0.5–2.5 kb) and the fact that many cells initiate replication at the same genomic sites, leading to localized enrichment. (iii) Regions without coverage refer to genomic areas that do not serve as efficient origins in the analyzed cell population. Thus, SNS-seq is designed to map origin positions, but not the entire replicated regions.

(2) I am concerned that up to 96% percent of all peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Specifically, if the authors placed the same number of peaks as was measured randomly in intergenic regions, would 4% of these peaks pass the filtering process by chance?

Maintaining the strandness of the sequenced DNA fibres enabled us to filter the peaks, thereby increasing the probability that the filtered peak pairs corresponded to origins. Two SNS peaks must be oriented in a way that reflects the topology of the SNS strands within an active origin: the upstream peak must be on the minus strand and followed by the downstream peak on the plus strand.

As suggested by the reviewer, we tested whether randomly placed plus and minus peaks could reproduce the number of filter-passing peaks using the same bioinformatics workflow. Only 1–6% of random peaks passed the filters, compared with 4–12% in our experimental data, resulting in about 50% fewer selected regions (origins). Moreover, the “origins” from random peaks showed 0% reproducibility across replicates, whereas the experimental data showed 7–64% reproducibility. These results indicate that the retainee peaks are highly unlikely to arise by chance and support the specificity of our approach. Thank you for this suggestion.

(3) There are 3 previous studies that map origins of replication in T. brucei. Devlin et al. 2016, Tiengwe et al. 2012, and Krasiļņikova et al. 2025 (https://doi.org/10.1038/s41467-025-56087-3), all with a different technique: MFA-seq. All three previous studies mostly agree on the locations and number of origins. The authors compared their results to the first two, but not the last study; they found that their results are vastly different from the previous studies (see Supplementary Figure 8A). In their discussion, the authors defend this discrepancy mostly by stating that the discrepancy between these methods has been observed in other organisms. I believe that, given the situation that the other studies precede this manuscript, it is the authors' duty to investigate the differences more than by merely pointing to other organisms. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

The MFA-seq data for T. brucei were published in two studies by McCulloch’s group: Tiengwe et al. (2012) using TREU927 PCF cells, and Devlin et al. (2016) using PCF and BSF Lister427 cells. In Krasilnikova et al. (2025), previously published MFA-seq data from Devlin et al. were remapped to a new genome assembly without generating new MFA-seq data, which explains why we did not include that comparison.

Clarifying the differences between MFA-seq and our stranded SNS-seq data is essential. MFA-seq and SNS-seq interrogate different aspects of replication. SNS-seq is a widely used, high-resolution method for mapping individual replication origins, whereas MFA-seq detects replicated regions by comparing DNA copy number between S and G1 phases. MFA-seq identified broad replicated regions (0.1–0.5 Mb) that were interpreted by McCulloch’s group as containing a single origin. We disagree with this interpretation and consider that there are multiple origins in each broad peaks; theoretical considerations of replication timing indicate that far more origins are required for complete genome duplication during the short S-phase. Once this assumption is reconsidered, MFA-seq and SNS-seq results become complementary: MFA-seq identifies replicated regions, while SNS-seq pinpoints individual origins within those regions. Our analysis revealed that up to 50% of the origins detected by stranded SNS-seq were located within the broad MFA peaks. This pattern—broad MFA-seq regions containing multiple initiation sites—has also recently been found in Leishmania by McCulloch’s team using nanopore sequencing (PMID: 26481451). Nanopore sequencing showed numerous initiation sites within MFA-seq regions and additional numerous sites outside these regions in asynchronous cells, consistent with what we observed using stranded SNS-seq in T. brucei. We will expand our discussion and conclude that the discrepancy arises from methodological differences and interpretation. The two approaches provide complementary insights into replication dynamics, rather than ‘vastly different’ results.

We recognize the importance of validating our results in future using an alternative mapping method and functional assays. However, it is important to emphasize that stranded SNS-seq is an origin mapping technique with a very high level of resolution. This technique can detect regions between two divergent SNS peaks, which should represent regions of DNA replication initiation. At present, no alternative technique has been developed that can match this level of resolution.

(4) Some patterns that were identified to be associated with origins of replication, such as G-quadruplexes and nucleosomes phasing, are known to be biases of SNS-seq (see Foulk et al. Characterizing and controlling intrinsic biases of lambda exonuclease in nascent strand sequencing reveals phasing between nucleosomes and G-quadruplex motifs around a subset of human replication origins. Genome Res. 2015;25(5):725-735. doi:10.1101/gr.183848.114).

It is important to note that the conditions used in our study differ significantly from those applied in the Foulk et al. Genome Res. 2015. We used SNS isolation and enzymatic treatments as described in previous reports (Cayrou, C. et al. Genome Res, 2015 and Cayrou, C et al. Methods, 2012). Here, we enriched the SNS by size on a sucrose gradient and then treated this SNS-enriched fraction with high amounts of repeated λ-exonuclease treatments (100u for 16h at 37oC - see Methods). In contrast, Foulk et al. used sonicated total genomic DNA for origin mapping, without enrichment of SNS on a sucrose gradient as we did, and then they performed a λ-exonuclease treatment. A previous study (Cayrou, C. et al. Genome Res, 2015, Figure S2, which can be found at https://genome.cshlp.org/content/25/12/1873/suppl/DC1) has shown that complete digestion of G4-rich DNA sequences is achieved under the conditions we used.

Furthermore, the SNS depleted control (without RNA) was included in our experimental approach. This control represents all molecules that are difficult to digest with lambda exonuclease, including G4 structures. Peak calling was performed against this background control, with the aim of removing false positive peaks resulting from undigested DNA structures. We explained better this step in the revised manuscript.

The key benefit of our study is that the orientation of the enrichments (peaks) remains consistent throughout the sequencing process. We identified an enrichment of two divergent strands synthesised on complementary strands containing G4s. These two divergent strands themselves do not, however, contain G4s (see Fig. 8 for the model). Therefore, the enriched molecules detected in our study do not contain G4s. They are complementary to the strands enriched with G4s. This means that the observed enrichment of

G4s cannot be an artefact of the enzymatic treatments used in this study. We added this part in the discussion of the revised manuscript.

We also performed an additional control which is not mentioned in the manuscript. In parallel with replicating cells, we isolated the DNA from the stationary phase of growth, which primarily contains non-replicating cells. Following the three λ-exonuclease treatments, there was insufficient DNA remaining from the stationary phase cells to prepare the libraries for sequencing. This control strongly indicated that there was little to no contaminating DNA present with the SNS molecules after λ-exonuclease enrichment.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Four broad issues need to be addressed.

(1) The authors have attempted to test the overlap between ORC1/CDC6 (an ORC subunit) binding in the genome and SNS-seq. If there were an overlap, this would provide evidence that the SNS-seq signals represent origins. However, the analysis provided is inadequate: merely a statement that "we obtained an overlap of 4.2% between origins and ORC1/CDC6 binding sites within a window of {plus minus}2 kb and 6.2% in the window of {plus minus}3 kb". Nowhere are these data shown or properly discussed:

a) The authors need to provide a diagram showing where in the genome the very small amount of overlapping SNS-seq and ORC1/CDC6 binding occurs, and to clearly show and state how many of the intergenic SNS-seq peaks are sites of ORC1/CDC6 binding. In the absence of such analysis, a key question is unanswered: is there any evidence of ORC1/CDC6 (or ORC more broadly) binding at the SNS-seq signals within the polycistronic transcription units?

In the original version of the manuscript, these data were already presented as percentages in the text and as a metaplot (Supplementary Fig. 8C).

We based our analysis on the set of 350 TbORC1/CDC6 binding sites available on TriTrypDB at the time of analysis. This dataset was a filtered subset of the originally reported TbORC1/CDC6 ChIP‑on‑chip peaks (personal communication, TriTrypDB). Since then, the unfiltered dataset has been made available. We therefore re‑analyzed the overlap using this dataset, to which we applied a filtering that yielded 990 binding sites closely matching the 953 sites reported by the McCulloch group. We need to stress here that the original 953 sites reported by the McCulloch group (Tiengwe et al., 2012 PMID: 22840408), is not available anymore and that the authors:

- do not provide genomic coordinates for the 953 binding sites and

- do not release any scripts or methodology that would allow independent reproduction of the 953 sites.

A similar remark also applies to the MFA-seq data (see below).

To address the reviewer’s request, we have now:

(1) Recalculated the overlap using the updated TbORC1/CDC6 dataset (990 binding sites) from TriTrypDB.

(2) Added the absolute number of overlapping SNS‑seq origins and TbORC1/CDC6 binding sites in the Results section for clarity.

(3) Included the TbORC1/CDC6 binding sites in the chromosomal overview (newly added to Supplementary Fig. 8A), so that their genomic localization relative to SNS‑seq peaks is visually accessible.

(4) Revised the metaplots of TbORC1/CDC6 distribution around SNS‑seq origins using the updated dataset (Supplementary Fig. 8C).

With these improvements, we now find that:

- Within ±2 kb, 12.9% (253) of SNS‑seq origins overlap with 25.6% of TbORC1/CDC6 binding sites.

- Within ±3 kb, 18.8% (370) of SNS‑seq origins overlap with 37.4% of TbORC1/CDC6 binding sites.

The updated metaplot shows a clear depletion of TbORC1/CDC6 signal at the origin center, with modest enrichment ~5 kb upstream and downstream. The underlying reason for this pattern remains unknown, and we agree that additional studies will be needed to understand it.

b) Equally, the authors need to explain what they conclude from this analysis. They make a comparison with T. cruzi ORC1/CDC6 and SNS-seq overlap, which does not illuminate what the data tell us. For instance, if there is no or minimal overlap between ORC1/CDC6 binding and SNS-seq peaks within the polycistronic transcription units, do they conclude that the major SNS-seq signal they detail is evidence for ORC-independent DNA replication? If there is no overlap, what further evidence can they provide that these signals truly are origins?

First, we would like to clarify that, to date, there is no evidence supporting ORC‑independent DNA replication in T. brucei, and—importantly—no published data demonstrating that TbORC1/CDC6 is universally required for DNA replication initiation. Because of this, we consider that it would be inappropriate to conclude that regions lacking detectable TbORC1/CDC6 signal undergo ORC‑independent initiation. We would prefer not to speculate in the absence of supporting evidence and would gratefully consider any reference the reviewer wishes to provide on this subject.

Second, the low overlap between TbORC1/CDC6 binding sites and SNS‑seq origins does not, in our view, invalidate our mapping of replication initiation sites. Multiple factors contribute to this:

(1) Low overlap between ORC1/CDC6 and origin‑mapping techniques has been repeatedly reported across kinetoplastids. For instance, in T. cruzi, 88.2% of origins detected by DNAscent nanopore sequencing showed no overlap with TcORC1/CDC6–Ty1 ChIP signal within ±3 kb, and only 11.7% co‑localized. This is strikingly similar to our observations in T. brucei. Thus, our data are consistent with the broader pattern in trypanosomatids rather than an exception.

(2) The origin topology detected by stranded SNS‑seq is supported by several genomic characteristic found frequently in other eukaryotes, including:

- A highly specific and polarized poly(dA)/poly(dT) sequence environment.

- Strand‑specific G4 structures positioned around origin centers.

- A conserved nucleosome‑depleted region flanked by well‑positioned nucleosomes.

These features are absent from shuffled controls, appear at high significance, and recapitulate hallmark signatures of replication origins in other eukaryotes.

Together, these findings give us confidence that the SNS‑seq peaks represent genuine origins - despite the incomplete overlap with TbORC1/CDC6 binding.

Third, we fully agree with the reviewer that a definitive conclusion would require an additional, independent validation method.

Given the lack of complete ORC subunit datasets and the unusual biology of trypanosomatid replication complexes, we believe that the cautious interpretation above is the most appropriate.

c) The authors state (Discussion): "Validation of origins is generally a difficult task, particularly in trypanosomatids, where proteins involved in the initiation of DNA replication are difficult to determine. Few proteins have been described as potential ORC subunits (reviewed in 61), and none of them have been shown to be a specific marker that indicates the origins." There are two problems with the statement. First, most of the subunits of ORC have now been described in T. brucei; the authors should make this clear. Second, mapping of ORC1/CDC6 localisation, contrary to what the authors state here, shows precise correlation with the peaks of every MFA-seq signal described (see Tiengwe et al, Cell Reports, 2012); thus, ORC1/CDC6 binding provides evidence that MFA-seq is detecting origins, something that cannot be said for SNS-seq. The authors need to correct this misleading paragraph.

As suggested, we have removed the paragraph from the Discussion to avoid confusion. However, we disagree with the reviewer's assessment and clarify below our position regarding the issues raised.

First, we agree that five candidate ORC subunits have now been identified in T. brucei. Our intention was not to suggest the contrary, but rather to emphasize that, although candidate ORC components have been described, direct functional evidence for their roles in replication initiation is still limited. For this reason, we were cautious in referring to any ORC component as a definitive marker of replication origins.

Second, regarding the reviewer’s statement that TbORC1/CDC6 binding “shows precise correlation with the peaks of every MFA‑seq signal”, we respectfully disagree based on several observations:

(1) MFA‑seq does not identify individual origin centers, but rather broad replicated regions that often span hundreds of kilobases. By design, this method cannot define the number or position of discrete origins within each peak. For that reason, MFA-seq regions do not have the resolution required to validate TbORC1/CDC6 binding sites as individual origins.

(2) In the published datasets (Tiengwe et al., Devlin et al.), no metaplots or locus‑wide quantification of the overlap between MFA‑seq peaks and TbORC1/CDC6 binding were provided. The coordinates or the approach used to define the discrete regions that they define as the originsin the MFA‑seq broad peaks have never been described or made available, making it difficult to evaluate the claimed correspondence.

(3) Notably, McCulloch’s group later reported that only 4.4% of the 953 TbORC1/CDC6 sites overlapped with their 42 MFA‑seq “origins”, underscoring that the degree of correspondence is in fact limited (PMID: 29491738).

(4) Finally, as noted in our response to point (1b), low overlap between ORC1/CDC6 binding sites and origin‑mapping techniques is a consistent observation across kinetoplastids, including T. cruzi, where DNAscent‑mapped origins show only ~12% overlap with TcORC1/CDC6 ChIP signals. This suggests that the limited overlap we observe is not unique to our dataset.

For these reasons, we are not convinced that the TbORC1/CDC6 binding sites have been shown to align precisely with MFA seq peaks, nor that these datasets definitively validate origin mapping in T. brucei. Nevertheless, to avoid over‑interpretation and potential confusion, we have removed the paragraph from the Discussion as requested. We hope this clarifies our position and improves the accuracy and neutrality of the manuscript.

(2) Like for ORC1/CDC6 localisation, the authors' evaluation of the relationship between MFA-seq and SNS-seq mapping is inadequate, and the depth of the analysis and discussion needs to be improved:

a) The authors state: "We found 28-42% stranded SNS-seq origins overlapped with early and 43-55% overlapped with late S-phase MFA-seq replicated regions (Supplementary Figure 8B)." This seems important and provides (limited) validation of both datasets, but cannot be discerned from the supplied figure. Please provide a metaplot of the two datasets centred on the MFA-seq loci, including the SNS-seq peak amplitude.

We would like to emphasize that MFA‑seq is not a method designed to map individual origins, and this fundamentally limits the interpretability of metaplots centered on MFA-seq regions. MFA‑seq identifies broad replication‑enriched domains, typically spanning 100–500 kb, within which multiple origins may fire asynchronously across the cell population.

This concern is reinforced by the original MFA‑seq publications (Tiengwe et al., 2012; Devlin et al., 2016), which:

- do not provide positional data for the 42-47 MFA‑inferred origins,

- do not describe the computational method used to derive individual origin coordinates from the broad peaks, and

- do not release any scripts or methodology that would allow independent reproduction of the claimed origin positions.

Because of this, it is not possible to reconstruct or validate how the 42 MFA‑seq “origin” sites were defined, nor to use those coordinates as anchors for metaplot analyses.

Most importantly, we disagree with the underlying assumption that each MFA‑seq peak corresponds to exactly one origin. This assumption runs counter to the principle of the technique, which identifies regions of higher DNA content in replicating cells than in non-replicating cells; it is also contradicted by our stranded SNS‑seq data and by DNA combing measurements:

- SNS‑seq detects multiple discrete origins within the same genomic regions that produce a single broad MFA‑seq peak.

- DNA combing reveals inter‑origin distances of ~36–422 kb (median ~150 kb) (PMID: 26976742), which is far shorter than the ~400–600 kb replication domains identified by MFA‑seq.

- Furthermore, with only 42 origins detected by MFA-seq, it is not possible to achieve complete genome replication in T. brucei during S-phase. DNA combing has found that the average speed of replication forks in the procyclic forms is 1.9 Kb/min. (PMID: 26976742). Dividing the size of the Trypanosoma brucei brucei TREU927 genome (26.1 Mb) by 42 origins (PMID: 22840408) shows that 621 Kb must be replicated during the S phase. Using the calculated average replication speed of 1.9 Kb/min, we can estimate that the replication of 621 Kb would take 327 min (5.45 hours) (621 Kb/1.9 Kb/min = 327 min). However, this exceeds the estimated length of the S-phase in these parasites, which is 2.31 hours (138.6 minutes) (PMID: 32397111, 31811174, 28258618) or less, 1.36 hours (PMID: 2190996, 10574712) in Trypanosoma brucei procyclic forms. Therefore, more than 42 origins are necessary to complete replication during the short S phase.

This makes it unlikely that MFA-seq regions represent single functional origins. For these reasons, a metaplot centered on MFA‑seq “loci” may lead to misinterpretations and would not provide biologically meaningful information.

We hope that the expanded explanation clarifies our interpretation of the relationship between these two complementary, but fundamentally different, methods.

b) The authors state that "Our results showed that the origins are predominantly located in the intergenic regions within the PTUs (Figure 2C)'. This finding cannot be discerned from this figure, which does not show 'strand switch regions' (SSRs; transcription start/stop sites), where MFA-seq predicts all origins to localise. The authors need to acknowledge this difference and must show a comparison of SNS-seq data, including peak amplitude, around all SSRs (whether predicted by MFA-seq to act as origins or not, since all appear to bind ORC1/CDC6).

We have now provided the metaplots showing the overlap between stranded SNS-seq origins and SSRs (see Supplementary Figure 8D). This difference has been acknowledged and discussed in the revised manuscript.

c) Finally, the authors' interpretation that around 30-55% of SNS-seq peaks overlap with MFA-seq 'origins' is highly questionable. MFA-seq peaks are regions of increased DNA content in replicating cells relative to non-replicating cells, and so the entire region under the MFA-seq peak is not necessarily an origin, but is likely to be a more discrete locus (eg, the SSR, where ORC1/CDC6 mainly localises). They should correct the wording and discuss what significance they see in this overlap; for instance, do they think SNS-seq 'clusters' are more pronounced within the MFA-seq peaks and, if so, what might this mean, and why does it not correlate with ORC1/CDC6 localisation?

As the reviewer notes, ‘MFA‑seq peaks are regions of increased DNA content, and so the entire region under the MFA-seq peak is not necessarily an origin but is likely to be a more discrete locus’. This is exactly why MFA‑seq is inappropriate for identifying discrete/individual origins: within these replicated domains, multiple origins can fire, as revealed both by stranded SNS‑seq mapping.

Regarding the overlap between SNS‑seq origins and MFA‑seq peaks, we agree with the reviewer that this overlap should not be interpreted as validating MFA‑seq “origin positions.” Instead, we now describe it more accurately as the proportion of discrete SNS‑seq origins that fall within broader MFA‑seq replication domains. This is expected, because SNS‑seq identifies individual initiation events, whereas MFA‑seq identifies S‑phase replication domains averaged across a population. Our stranded SNS‑seq data do not show enhanced origin accumulation within MFA-seq regions, and we find no correlation with TbORC1/CDC6 positions. This is now discussed.

Regarding SSRs, we do not share the view that they should be considered privileged initiation sites. After remapping the TbORC1/CDC6 ChIP‑on‑chip dataset (see above) to the T. brucei Lister 427–2018 genome (Supplementary Fig. 8A), we observed that TbORC1/CDC6 binding is distributed throughout the chromosomes, not restricted to SSRs. To quantify this, we analyzed the overlap between TbORC1/CDC6 sites and all annotated SSR classes (dSSRs, cSSRs, and head‑to‑tail regions, as defined in Kim et al. 2009). The results show that:

Only 10% of TbORC1/CDC6 binding sites fall within 40% of all SSRs.

At the level of individual SSR types:

- TTS: 3.3% of TTS overlap with 0.3% of TbORC1/CDC6 sites.

- TSS: 67% of TSS overlap with 6.1% of TbORC1/CDC6 sites.

- Head‑to‑tail regions: 54.2% overlap with 3.6% of TbORC1/CDC6 sites.

These analyses demonstrate that most TbORC1/CDC6 sites are not located at SSRs, contradicting the idea that SSRs represent primary or exclusive origin sites.

Author response image 1.

Overlap between TbORC1/CDC6-12Myc binding sites (Tiengwe 2012, Cell Reports) and strand‑switch regions (SSRs). Venn diagram showing the overlap of 990TbORC1/CDC6-12Mycbinding sites (Retrieved from TritrypDB filtered at score 22 to achieve a number of binding sites similar to the one (953 binding sites) published in Tiengwe 2012, Cell Reports) and SSR sites in the genome (Kim 2018, NAR). The intersection shows that 10.3% of Orc1/CDC6 binding sites overlap with 41.8% SSRs. The intersection is subdivided into TSS (orange), TTS in (blue) and HT in (green).

(3) A key objection to the data presentation is the decision to limit SNS-seq mapping to the intergenic regions. In addition to overlooking the SSRs (see above, 2), so-called subtelomeres, which account for nearly 50% of the T. brucei genome and are largely untranscribed, are not shown or discussed at all. Providing this data will improve clarity and also provide a key test of one of the predictions that the authors make: "most origins are localized in actively transcribed regions, which could lead to collisions between DNA replication and the transcription machinery. This spatial coincidence implies that transcription and replication must occur in a highly ordered and cooperative manner in T. brucei."

We do not understand why this reviewer concluded that we took 'the decision to limit the mapping of SNS-seq to intergenic regions'. This is a factual error.

To be clearer,

(2) We now explicitly present the distribution of SNS‑seq origins across core and subtelomeric regions in the revised Figure 2D, making clear that origin mapping was performed genome‑wide.

(2) And that SNS‑seq origins are also present in subtelomeric regions. We have revised the manuscript to avoid any implication that origin firing is restricted only to actively transcribed regions. Our data show that most SNS‑seq origins lie within intergenic regions of PTUs, but a minority are found outside these regions—including subtelomeres and SSRs. The revised text reflects this nuance and highlights that the spatial relationship between transcription and replication is strong but not exclusive.

These additions undoubtedly ensure that the genomic-wide nature of SNS-seq analysis is transparent to the reader and should therefore remove this reviewer's “key objection”.

a) The authors must show SNS-seq mapping to the subtelomeres (in addition to around the SSRs; see comment (2). If no SNS-seq peaks are detected in the subtelomeres, what do the authors conclude about how the genome is duplicated? If SNS-seq peaks are detected in the subtelomeres, do they correspond with the ordered nucleosomes in this part of the genome described by Maree et al (PMID: 28344657); if so, might SNS-seq signal localisation not be directed by transcription but chromatin?

We have now presented the proportion of origins in subtelomeric regions (see Figure 2B).

As illustrated in the metaplots in Author response image 2, the distribution of nucleosomes around the subtelomeric origins is similar to the distribution shown for all origins in the manuscript. We do not see the pattern of nucleosomes as described by Maree et al (PMID: 28344657) over ORC1/CDC6 binding sites in this part of the genome.

Author response image 2.

Metaplots showing the mean nuclesome signal over centred SNS-seq origins in subtelomeric regions. Two replicates from Maree et al 2019 (PMID: 28344657).

We never claimed that transcription directs the localisation of the SNS-seq signal. We did not conduct experiments to address this issue. In contrast, we consider that the organisation of chromatin exerts a significant influence on the selection of active origins.

(4) The major conclusion of the manuscript is that the SNS-seq signal corresponds very precisely to the locations of RNA-DNA hybrids (R-loops). Given all the limitations discussed above, can the authors rule out the possibility that SNS-seq is merely mapping DNA-DNA hybrids and is not, in fact, detecting origins?

a) It is legitimate to speculate about the possibility that the very extensive overlap between SNS-seq and DRIP-seq signals within polycistronic transcription units (between ORFs) might suggest that DRIP-seq data detects nascent strands at replication origins, rather than R-loops at sites of pre-mRNA processing, as previously suggested by Briggs et al (PMID: 30304482). (eg, 'we disclosed for the first time a strong link between R-loop formation and DNA replication initiation'; 'The RNA:DNA hybrids are formed at initiation sites by RNA priming of SNS and Okazaki fragments'). However, the authors should acknowledge that alternative explanations for the localisation and potential functions of inter-CDS R-loops have been suggested,

We do not find extensive overlap between stranded SNS-seq and DRIP-seq signal. We have observed only a minor proportion (1.7%) of the previously reported DRIP-seq signal to overlap with the origins detected by stranded SNS-seq. The RNA-primed SNS must form RNA:DNA hybrids during the initiation of DNA replication, and that an enrichment of these hybrids around the origins is expected. Therefore, we legitimately speculated that this minor proportion of RNA:DNA hybrids enriched around origin centres could be due to the origin activation.

We agree that some of the DRIP-seq signals detected around the origins may be sites of pre-mRNA processing, as previously suggested by Briggs et al. (PMID: 30304482). Since there is no data proving implication of pre-mRNA processing into DNA replication initiation we prefer not to speculate about it.

b) More importantly, the authors should provide experimental evidence that tests such a mechanistic prediction of R-loops and origins: for instance, have they attempted to remove R-loops, eg, by treatment with RNase H, and checked that the SNS-seq signal is unaltered? In the absence of such data, they cannot exclude the possibility that their work has revealed an overlooked problem with SNS-seq (which may not be limited to T. brucei; are matched DRIP-seq and SNS-seq datasets available to correlate these signals in a range of organisms?).

We have not attempted RNase H treatment for a fundamental methodological reason: it seems highly improbable that RNA:DNA hybrids would persist through the multiple denaturation steps inherent to the SNS‑seq enrichment protocol. Published biophysical measurements show that RNA:DNA hybrids melt at ~95 °C (Roberts & Crothers, Science, 1992; PMID: 1279808), which is the temperature repeatedly applied during SNS isolation. Under these conditions, persistent RNA:DNA hybrids cannot remain intact and therefore cannot be responsible for the SNS‑seq peaks detected.

We do not interpret our findings as revealing an “overlooked problem with SNS‑seq.” Instead, we consider that the enrichment of RNA:DNA hybrids around origins observed in DRIP‑seq is biologically meaningful and expected, given that replication initiation involves RNA‑primed nascent strands and that DRIP‑seq detects such structures.

Reviewer #2 (Recommendations for the authors):

I have some minor concerns that do not affect the main conclusions of the manuscript:

(1) Figure 2B: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions.

That is correct. The regions displayed in the heatmaps are genic and intergenic region sorted by size. We did not want to convey with this metaplot that the origins are accumulating at the centres of the intergenic region but mainly that genic regions are mostly devoid of origins and the intergenic regions enriched in origins.

(2) Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length.

This observation is correct. By applying filtering and setting the maximum distance between the positive and negative peaks, we are most likely affecting the average length by excluding origins that are potentially wider. Nevertheless, the violin plot shows that the majority of origins are shorter than 500 nt. In the end, the size of regions detected as the origin is not important. What gives the resolution of stranded-SNS-seq is the ability to identify the centre of the origin between the minus and plus peaks.

(3) Data in the manuscript were sometimes not presented in an easy-to-read manner. In some cases, this was due to benign things, such as missing labels for the mean frequency plots (e.g., Figure 2B, blue and green) or very small fonts for axes (Figure 2B). Sometimes, due to the plot types that were chosen, such as pie-charts (Figure 2C, see https://medium.com/analytics-vidhya/dont-use-pie-charts-in-data-analysis-6c005723e657), stacked bar plots (Figure 6B), or showing cumulative distributions (Figure 5C, and Figure 2D) it makes it difficult to judge the actual distribution.

Wherever possible, the size of the small fonts was increased to the maximum. Missing labels were added to the mean frequency plots. We increased the font size for the axes in the frequency plots.

However, we found cumulative distributions useful. If you have a more specific proposal for replacing cumulative distributions, we would be very grateful to hear it. We also hope that magnifying the figures in TIFF format with a higher resolution will improve visibility.

(4) Figure 2B: This data would be better presented with all regions stretched to the same size (the reason is explained in the public review).

We performed the scaled plots for the stranded SNS-seq origins over the genic and intergenic regions as the reviewer suggested (see Author response image 3), but we prefer to keep the unscaled versions in the manuscript.

Author response image 3.

Distribution of mapped origins in scaled genic and intergenic regions. Scaled heatmaps present the distribution of the mapped origins and shuffled controls within scaled genic and intergenic regions (± 2 kb).

(5) Line 149: "The number of origins in both cells was 148 compared using normalised mapped reads": Supplementary Figure 2D mentions that conditions were subsampled to the same amount. I would mention that explicitly in the main text ("compared using normalized, subsampled mapped reads"), as 'normalizing' would not include 'subsampling' for me. Also, I could not find the methods section that the authors refer to here.

Thanks for the suggestion. We changed the text to make this point clearer. In the methods section, the subsampling process was referred to as 'PCF down-sampling', but we changed now the name to 'Read sub-sampling' to be more consistent in the edited version of the manuscript.

(6) Figure 2C: I struggled to understand what gDNA stands for. Maybe it could be replaced with something like distribution in genome?

Thanks for this suggestion. It is changed to ‘distribution in genomic sequence’.

(7) Figure 5C: I cannot see how a G4 30 kb from an origin could be relevant. This also does not fit the scale of the author's own model at all (Figure 8).

The main goal of Figure 5C was to demonstrate the differences between origins and the nearest G4s compared to the shuffled controls. The graph shows that 50% of the origins have a G4 within 2010 bp, whereas the median for the shuffled control is 4154 bp in the case of non-stabilised G4s. Our model is based on Figure 5D, which illustrates the enrichment of G4s and poly(dA) around the centre of origins.

(8) Figure 6B: could be made supplementary in my opinion. All relevant data is repeated in panel D.

It is true that Figures 6B and 6C contain some repetition. However, we would prefer to keep Figure 6B because it provides a quantification of the six indicated categories, along with the statistical tests. Figure 6B only presents the three categories that changed significantly. Figure 6D shows distribution but does not contain quantified data.

(9) Figure 6D: This plot is repeating a lot, within single figures (Figure 6A, top) but also between figures (e.g., Figure 5D, Figure 4B). I'd prefer it if the initial plots of each figure were expanded a bit (here Figure 6A, top) to include some information from the previous figures. Then all these summary plots could be combined into a single figure at the very end (maybe still as different panels to reduce the number of lines in a single plot). Otherwise, each summary plot repeats the tracks of the previous, which becomes very repetitive.

Our model is based on these summary plots, and we calculated the relative distances between the different elements using them. Two elements were repeated in each plot: the positions of poly(dA) and G4s. These two elements served as reference points to determine the relative positions of the other elements. Following your suggestion would result again in repetitive summary plots at the end, as one combined summary plot would be overloaded with lines and difficult to understand.

(10) Figure 6D & Figure 7C: Both show predicted G4s; however, on the plus strand, one prediction has a two-peaked shape, the other only a single peak. Is this a mistake?

The graphs for the predicted G4s do not have the same shape in the two plots as they were performed in different reference genomes for T. brucei. Figure 6C is in the 427-reference genome as the MNase-seq data set was analysed in this reference genome and we re-did the SNS-seq analysis and the G4 prediction in this reference genome to be able to compare them directly. In Figure 7C we are comparing origins DRIP-seq and predicted G4s, in this case all datasets could be compared in the 427-2018 reference genome.

eLife Assessment

This important work provides a new method to extract cfDNA from residual plasma from heparin separators for molecular testing. The evidence supporting the authors' claims is convincing, although some further metrics should also be evaluated. This finding will be interesting to people working in epigenomics and infectious disease diagnostics.

Reviewer #1 (Public review):

Summary:

The manuscript "Adapting Clinical Chemistry Plasma as a Source for Liquid Biopsies" addresses a timely and practical question: whether residual plasma from heparin separator tubes can serve as a source of cfDNA for molecular profiling. This idea is attractive, since such samples are routinely generated in clinical chemistry labs and would represent a vast and accessible resource for liquid biopsy applications. The preliminary results are encouraging, and likely to benefit the research community.

Comments on revisions:

The concerns raised have been addressed. The heparin separator-based cfDNA method described in this study is likely to benefit the research community. I have no further scientific concerns.

Reviewer #2 (Public review):

Summary:

The authors propose that leftover heparin plasma can serve as a source for cfDNA extraction, which could then be used for downstream genomic analyses such as methylation profiling, CNV detection, metagenomics, and fragmentomics. While the study is potentially of interest, several major limitations reduce its impact; for example, the study does not adequately address key methodological concerns, particularly cfDNA degradation, sequencing depth limitations, statistical rigor, and the breadth of relevant applications.

Strengths:

The paper provides a cheap method to extract cfDNA, which has broad application if the method is solid.

Weaknesses:

(1) The introduction lacks a sufficient review of prior work. The authors do not adequately summarize existing studies on cfDNA extraction, particularly those comparing heparin plasma and EDTA plasma. This omission weakens the rationale for their study and overlooks important context.

(2) The evaluation of cfDNA degradation from heparin plasma is incomplete. The authors did not compare cfDNA integrity with that extracted from EDTA plasma under realistic sample handling conditions. Their analysis (lines 90-93) focuses only on immediate extraction, which is not representative of clinical workflows where delays are common. This is in direct conflict with findings from Barra et al. (2025, LabMed), who showed that cfDNA from heparin plasma is substantially more degraded than that from EDTA plasma. A systematic comparison of cfDNA yields and fragment sizes under delayed extraction conditions would be necessary to validate the feasibility of their proposed approach.

(3) The comparison of methylation profiles suffers from the same limitation. The authors do not account for cfDNA degradation and the resulting reduced input material, which in turn affects sequencing depth and data quality. As shown by Barra et al., quantifying cfDNA yield and displaying these data in a figure would strengthen the analysis. Moreover, the statistical method applied is inappropriate: the authors use Pearson correlation when Spearman correlation would be more robust to outliers and thus more suitable for methylation and other genomic comparisons.

(4) The CNV analysis also raises concerns. With low-coverage WGS (~5X) from heparin-derived cfDNA, only large CNVs (>100 kb) are reliably detectable. The authors used a 500 kb bin size for CNV calling, but they did not acknowledge this as a limitation. Evaluating CNV detection at multiple bin sizes (e.g., 1 kb, 10 kb, 50 kb, 100 kb, 250 kb) would provide a more complete picture. In addition, Figure 3 presents CNV results from only one sample, which risks bias. Similar bias would exist for illustrations of CNVs from other samples in the supplementary figures provided by the authors. Again, Spearman correlation should be applied in Figure 3c, where clear outliers are visible.

(5) It is important to point out that depth-based CNV calling is just one of the CNV calling methods. Other CNV calling software using SNVs, pair-reads, split-reads, and coverage depth for calling CNV, such as the software Conserting, would be severely affected by the low-quality WGS data. The authors need to evaluate at least two different software with specific algorithms for CNV calling based on current WGS data.

(6) The authors omit an important application of cfDNA: somatic mutation detection. Degraded cfDNA and reduced sequencing depth could substantially impact SNV calling accuracy in terms of both recall and precision. Assessing this aspect with their current dataset would provide a more comprehensive evaluation of heparin plasma-derived cfDNA for genomic analyses.

Comments on revisions:

As suggested previously, the Pearson correlation analysis tends to be overstated; please replace it with Spearman correlation in the whole manuscript. Currently, the authors include both of them in the abstract, method, results, and graphics, all of which are required to be updated to only use Spearman correlation results.

I don't have other concerns about the manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript "Adapting Clinical Chemistry Plasma as a Source for Liquid Biopsies" addresses a timely and practical question: whether residual plasma from heparin separator tubes can serve as a source of cfDNA for molecular profiling. This idea is attractive, since such samples are routinely generated in clinical chemistry labs and would represent a vast and accessible resource for liquid biopsy applications. The preliminary results are encouraging, but in its current form, the study feels incomplete and requires additional work.

We thank the reviewer for the encouragement and for recognizing the potential of clinical chemistry plasma as an accessible source for cfDNA-based analyses. To address concerns about incompleteness, we conducted additional controlled experiments and a more thorough literature review.

My major concerns/suggestions are as follows:

(1) Context and literature

The introduction provides only limited background on prior attempts to use heparinized plasma for cfDNA work. It is well known that heparin can inhibit PCR and sequencing library preparation, which has historically discouraged its use. The authors should summarize the relevant literature more comprehensively and explain clearly why this approach has not been widely adopted until now, and how their work differs from or overcomes these earlier challenges.

Thank you, we agree that the review of prior work requires expansion. In the revised manuscript, we expanded the introduction to focus on prior studies and their gaps (lines 53-80).

(2) Genome-wide coverage

The analyses focus on correlations in methylation patterns and fragmentation metrics, but there is no evaluation of sequencing coverage across the genome. For both WGS and WMS, it would be important to demonstrate whether cfDNA from heparin plasma provides unbiased coverage, or whether certain genomic regions are systematically under-represented. A comparison against coverage profiles from cell-derived DNA (e.g., PBMC genomic DNA) would help to put the results in context and assess whether the material is suitable for whole-genome applications.

Thank you for raising this point. We agree that genome-wide coverage distributions should be evaluated alongside correlations in methylation and fragmentation metrics when assessing the effects of sample tube types.

To address this, we pooled the five healthy subjects in the Tube Comparison Study by tube type to generate two high-depth reference BAMs (EDTA vs. heparin separator). We calculated the mean depth per 1Mb bin across Chr1-22 and normalized with z-score. Overall, the heparin separator samples showed coverage profiles comparable to the matched EDTA samples (Pearson’s r = 0.9988, Spearman’s ρ = 0.9994). The figure has now been added as Supplementary Figure 1.

Also appreciate the suggestion to compare against gDNA. However, cfDNA and gDNA are expected to exhibit different coverage patterns because cfDNA undergoes non-random fragmentation during its generation and degradation, which makes a direct cfDNA–gDNA comparison difficult to interpret in terms of tube-related bias.

(3) Viral detection sensitivity

The study shows strong concordance in viral detection between EDTA and heparin samples, but the sensitivity analysis is lacking. For clinical relevance, it is critical to demonstrate how well heparin-derived plasma performs in low viral load cases. A quantitative comparison of viral read counts and genome coverage across tube types would strengthen the conclusions.

We agree that evaluating low viral loads is important for test development. While our goal is to evaluate the repurposing of residual plasma from the heparin separator, rather than to establish the analytical sensitivity, we recruited additional paired cases (n=4) together with viral reads below 10 RPM from existing cases (n=12) and examined the correlation of viral read counts between EDTA and heparin separators in this subset. As shown in Author response image 1, viral RPM is strongly correlated between tube types (Pearson’s r = 0.93, P < 0.0001), supporting that the heparin-derived plasma yields quantitatively consistent viral reads relative to EDTA samples. We have updated our sample sheet in Supplementary Table 1 and Fig. 3 accordingly.

Author response image 1.

Viral load correlation in cases below 10 RPM

Reviewer #2 (Public review):

Summary:

The authors propose that leftover heparin plasma can serve as a source for cfDNA extraction, which could then be used for downstream genomic analyses such as methylation profiling, CNV detection, metagenomics, and fragmentomics. While the study is potentially of interest, several major limitations reduce its impact; for example, the study does not adequately address key methodological concerns, particularly cfDNA degradation, sequencing depth limitations, statistical rigor, and the breadth of relevant applications.

We thank the reviewer for the insightful comments. In the revised manuscript, we added controlled experiments specifically designed to address the concerns regarding cfDNA degradation. We have also addressed other concerns in the responses below.

Strengths:

The paper provides a cheap method to extract cfDNA, which has broad application if the method is solid.

We thank the reviewer for the encouraging comment.

Weaknesses:

(1) The introduction lacks a sufficient review of prior work. The authors do not adequately summarize existing studies on cfDNA extraction, particularly those comparing heparin plasma and EDTA plasma. This omission weakens the rationale for their study and overlooks important context.

Thank you for this important point. We have expanded the introduction to include a thorough review of relevant prior studies (lines 53-80).

(2) The evaluation of cfDNA degradation from heparin plasma is incomplete. The authors did not compare cfDNA integrity with that extracted from EDTA plasma under realistic sample handling conditions. Their analysis (lines 90-93) focuses only on immediate extraction, which is not representative of clinical workflows where delays are common. This is in direct conflict with findings from Barra et al. (2025, LabMed), who showed that cfDNA from heparin plasma is substantially more degraded than that from EDTA plasma. A systematic comparison of cfDNA yields and fragment sizes under delayed extraction conditions would be necessary to validate the feasibility of their proposed approach.

The concern about degradation is very reasonable based on the literature. In the revised manuscript, we added a controlled experiment mimicking the real-world clinical specimens unprocessed at room temperature.

In the controlled experiment with delayed processing, paired EDTA and heparin separator tubes from the same blood draw from 6 volunteers were processed with the first soft spin (1600g 10min) after room temperature or 4°C delays (0, 1, 3, and 24 hours) to simulate the real-world delayed processing at the inpatient hospital setting, and then the original tubes were kept in 4°C for a week before the second spin (16000g 10min) to simulate the delayed processing at the research laboratory (Fig. 2). This simulation cannot mimic the outpatient or remote clinic setting that requires transportation. Therefore, we noted this caveat in the Discussion and Abstract.

From our results, EDTA samples remained largely stable across all test settings (Author response image 2). In contrast, heparin separator tubes held at room temperature showed a clear time-dependent shift in fragmentation, with the most pronounced degradation at 24 hours. Importantly, heparin separator samples processed within a short pre-centrifugation window (for example, within 3 hours) and maintained refrigerated thereafter showed only minimal changes relative to the time 0 controls (Author response image 3). We have updated the Discussion to emphasize this short window plus refrigeration condition as a practical boundary for fragmentomics in heparin separator tubes.

We addressed the work of Barra et al. (2025, LabMed) in the introduction. In that study, whole blood in heparin tubes was first soft spun and then incubated at 37°C for 24 hours, leading to severe DNA fragmentation. Our data agrees: two matched 37°C, 24-hour pairs of samples produced similar severe fragmentation in heparinized blood (Author response image 4). However, this is not representative of routine (Stanford/UCSF) clinical transport and processing. We revised the manuscript to emphasize that heparin separator tubes are most suitable for downstream cfDNA fragmentomic analyses when the pre-centrifugation interval is minimized and samples are maintained refrigerated before processing whenever feasible.

Author response image 2.

Size distribution and end motif rank concordance in EDTA tubes across conditions. Left panels show fragment size distributions. The right panels show the corresponding scatter plots comparing end-motif abundance rankings between conditions. E0, EDTA processed immediately; E4T24, EDTA incubated at 4°C for 24 h; ERT24, EDTA incubated at room temperature for 24 h.

Author response image 3.

Size distribution and end motif rank concordance in Heparin separators across conditions. Left panels show fragment size distributions. The right panels show scatter plots comparing end-motif abundance rankings between conditions. H0, heparin processed immediately; H4T1/H4T3/H4T24, heparin incubated at 4°C for 1, 3, or 24 h; HRT1/HRT2/HRT3/HRT24, heparin incubated at room temperature for 1, 2, 3, or 24 h.

Author response image 4.

Size distribution and end motif rank concordance in extreme incubation conditions. Left panels show fragment size distributions. The right panels show scatter plots comparing end-motif abundance rankings between conditions. H0, heparin processed immediately; H37T24, heparin incubated at 37°C for 24 h.

(3) The comparison of methylation profiles suffers from the same limitation. The authors do not account for cfDNA degradation and the resulting reduced input material, which in turn affects sequencing depth and data quality. As shown by Barra et al., quantifying cfDNA yield and displaying these data in a figure would strengthen the analysis. Moreover, the statistical method applied is inappropriate: the authors use Pearson correlation when Spearman correlation would be more robust to outliers and thus more suitable for methylation and other genomic comparisons.

We appreciate the reasonable concerns regarding cfDNA degradation and agree that the methylation profile is not a metric for degradation. This point regarding measuring degradation is addressed with new experiments and in our above response to comment (2). We appreciate the suggestion to use Spearman correlation, and we have now incorporated Spearman’s ρ into the updated figures.

(4) The CNV analysis also raises concerns. With low-coverage WGS (~5X) from heparin-derived cfDNA, only large CNVs (>100 kb) are reliably detectable. The authors used a 500 kb bin size for CNV calling, but they did not acknowledge this as a limitation. Evaluating CNV detection at multiple bin sizes (e.g., 1 kb, 10 kb, 50 kb, 100 kb, 250 kb) would provide a more complete picture. In addition, Figure 3 presents CNV results from only one sample, which risks bias. Similar bias would exist for illustrations of CNVs from other samples in the supplementary figures provided by the authors. Again, Spearman correlation should be applied in Figure 3c, where clear outliers are visible.

We appreciate the reviewer’s constructive comments regarding the CNV analysis. We added an analysis using 50kb as the bin size (data uploaded to Zenodo). Across matched CNV-positive samples, the CNV patterns remained consistent across tube types, while the expected higher noise was observed. We did not extend the bin size to 1-10kb because at ~5x coverage, such resolution would mainly be noise, rendering the results uninterpretable for CNV calling.We agree that illustrative examples alone are insufficient and that quantitative measures are required. To address this concern, we evaluated concordance across all paired cases by measuring the copy ratio and calculating the Spearman correlation (Fig. 4b). CNV-positive samples had high concordance (n = 6, Spearman’s ρ=0.72-0.96) between tube types and were used primarily for interpretation. Low correlations in CNV-negative samples are not unexpected and were not used for interpretation. In these samples, log2 ratios across all bins cluster tightly around zero in both tube types. Correlation coefficients are highly sensitive to minor fluctuations, thus not informative of biological concordance.

(5) It is important to point out that depth-based CNV calling is just one of the CNV calling methods. Other CNV calling software using SNVs, pair-reads, split-reads, and coverage depth for calling CNV, such as the software Conserting, would be severely affected by the low-quality WGS data. The authors need to evaluate at least two different software with specific algorithms for CNV calling based on current WGS data.

We appreciate this suggestion. We used another popular and independent CNV caller, CNVkit, in addition to ichorCNA. Although both methods use sequencing depth, they differ in their segmentation algorithm. ichorCNA uses a hidden Markov model-based segmentation optimized for low-pass cfDNA WGS, whereas CNVkit uses circular binary segmentation by default and works well with targeted panels. The CNVkit results are also consistent across different tube types. We have added the CNVkit results to Supplementary Fig. 3.

(6) The authors omit an important application of cfDNA: somatic mutation detection. Degraded cfDNA and reduced sequencing depth could substantially impact SNV calling accuracy in terms of both recall and precision. Assessing this aspect with their current dataset would provide a more comprehensive evaluation of heparin plasma-derived cfDNA for genomic analyses.

We thank the reviewer for highlighting somatic SNV detection as an important cfDNA application. Robust SNV benchmarking typically requires larger plasma input and substantially deeper, targeted sequencing than is feasible with remnant chemistry specimens. In routine workflows, chemistry testing leaves only ~0.5–2 mL residual plasma per tube, which limits the achievable depth for sensitive SNV calling. We have added this limitation to the Abstract and the Discussion (lines 281-285) and clarified that our goal is to repurpose heparin separator residual plasma as a complementary resource to expand biobanking, rather than to replace collection protocols optimized for mutation testing.

Reviewer #2 (Recommendations for the authors):

The manuscript does not seem to have been edited thoroughly prior to submission. For example, at lines 94-97, the line spacing is double, which is apparently different from the other surrounding lines. In addition, Figure 5a contains a wrong label of "|y=x" at its top. Figure 5b strongly suggests that Spearman, but not Pearson correlation, should be appropriate for the analysis.

We thank the reviewer for carefully noting these formatting and labeling issues. Corrections for all points are made in the revised version.

eLife Assessment

Ge et al here report a structural study of the native tripartite multidrug efflux pump complexes from Escherichia coli that identifies a novel accessory subunit, YbjP, the structure of the native TolC-YbjP-AcrABZ complex, as well as structures of the AcrB protein in L, T, and O conformations. The strength of the structural data is compelling, and the importance of the findings is potentially fundamental. In the revised manuscript, the authors have included additional analysis and made comparisons with pre-existing data which has helped place the data and its impact in the proper context.

Reviewer #1 (Public review):

Summary:

This manuscript investigates the biological mechanism underlying the assembly and transport of the AcrAB-TolC efflux pump complex. By combining endogenous protein purification with cryo-EM analysis, the authors show that the AcrB trimer adopts three distinct conformations simultaneously and identify a previously uncharacterized lipoprotein, YbjP, as a potential additional component of the complex. The work aims to advance our understanding of the AcrAB-TolC efflux system in near-native conditions and may have broader implications for elucidating its physiological mechanism.

Strengths:

Overall, the manuscript is clearly presented, and several of the datasets are of high quality. The use of natively isolated complex is a major strength, as it minimizes artifacts associated with reconstituted systems and enables the discovery of a novel subunit. The authors also distinguish two major assemblies-the TolC-YbjP sub-complex and the complete pump-which appear to correspond to the closed and open channel states, respectively. The conceptual advance is potentially meaningful, and the findings could be of broad interest to the field.

Weaknesses:

(1) As the identification of YbjP is a key contribution of this work, a deeper comparison with functional "anchor" proteins in other efflux pumps is needed. Including an additional supplementary figure illustrating these structural comparisons would be valuable.

(2) The observation of the LTO states in the presence of TolC represents an important extension of previous findings. A more detailed discussion comparing these LTO states to those reported in earlier structural and biochemical studies would improve the clarity and significance of this point.

Comments on revisions:

In the revision, the authors have addressed the above concerns to improve this study.

Reviewer #2 (Public review):

Summary:

This manuscript reports the high-resolution cryo-EM structures of the endogenous TolC-YbjP-AcrABZ complex and a TolC-YbjP subcomplex from E. coli, identifying a novel accessory subunit. This work is an impressive effort that provides valuable structural insights into this native complex.

Strengths:

(1) The study successfully determines the structure of the complete, endogenously purified complex, marking a significant achievement.<br /> (2) The identification of a previously unknown accessory subunit is an important finding.<br /> (3) The use of cryo-EM to resolve the complex, including potential post-translational modifications such as N-palmitoyl and S-diacylglycerol, is a notable highlight.

Weaknesses:

(1) Clarity and Interpretation: Several points need clarification. Additionally, the description of the sample preparation method, which is a key strength, is currently misplaced and should be introduced earlier.<br /> (2) Data Presentation: The manuscript would benefit significantly from improved figures.<br /> (3) Supporting Evidence: The inclusion of the protein purification profile as a supplementary figure is essential. Furthermore, a discussion comparing the endogenous AcrB structure to those obtained in other systems (e.g., liposomes) and commenting on observed lipid densities would strengthen the overall analysis.

Comments on revisions:

In the revision, all my concerns have been addressed.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript investigates the biological mechanism underlying the assembly and transport of the AcrAB-TolC efflux pump complex. By combining endogenous protein purification with cryo-EM analysis, the authors show that the AcrB trimer adopts three distinct conformations simultaneously and identify a previously uncharacterized lipoprotein, YbjP, as a potential additional component of the complex. The work aims to advance our understanding of the AcrAB-TolC efflux system in near-native conditions and may have broader implications for elucidating its physiological mechanism.

Strengths:

Overall, the manuscript is clearly presented, and several of the datasets are of high quality. The use of natively isolated complexes is a major strength, as it minimizes artifacts associated with reconstituted systems and enables the discovery of a novel subunit. The authors also distinguish two major assemblies-the TolC-YbjP sub-complex and the complete pump-which appear to correspond to the closed and open channel states, respectively. The conceptual advance is potentially meaningful, and the findings could be of broad interest to the field.

Weaknesses:

(1) As the identification of YbjP is a key contribution of this work, a deeper comparison with functional "anchor" proteins in other efflux pumps is needed. Including an additional Supplementary Figure illustrating these structural comparisons would be valuable.

We have expanded the comparative analysis between YbjP and established anchoring or accessory components in other efflux pumps, and we have added Supplementary Figure S3 to illustrate these structural relationships.

(2) The observation of the LTO states in the presence of TolC represents an important extension of previous findings. A more detailed discussion comparing these LTO states to those reported in earlier structural and biochemical studies would improve the clarity and significance of this point.

In the revised manuscript we have expanded our discussion of the LTO conformations, including a direct comparison with previously reported structural and biochemical observations, to better contextualize the significance of our findings.

Reviewer #2 (Public review):

Summary:

This manuscript reports the high-resolution cryo-EM structures of the endogenous TolC-YbjP-AcrABZ complex and a TolC-YbjP subcomplex from E. coli, identifying a novel accessory subunit. This work is an impressive effort that provides valuable structural insights into this native complex.

Strengths:

(1) The study successfully determines the structure of the complete, endogenously purified complex, marking a significant achievement.

(2) The identification of a previously unknown accessory subunit is an important finding.

(3) The use of cryo-EM to resolve the complex, including potential post-translational modifications such as N-palmitoyl and S-diacylglycerol, is a notable highlight.

Weaknesses:

(1) Clarity and Interpretation: Several points need clarification. Additionally, the description of the sample preparation method, which is a key strength, is currently misplaced and should be introduced earlier.

We have reorganized the text to introduce the sample preparation strategy earlier and clarify the points that may cause ambiguity.

(2) Data Presentation: The manuscript would benefit significantly from improved figures.

We agree and have revised the figures to improve clarity, consistency, and readability. Additional schematic illustrations have been included.

(3) Supporting Evidence: The inclusion of the protein purification profile as a supplementary figure is essential. Furthermore, a discussion comparing the endogenous AcrB structure to those obtained in other systems (e.g., liposomes) and commenting on observed lipid densities would strengthen the overall analysis.

We appreciate these suggestions. We added the purification profile to Supplementary Figure S1 and expanded the comparison between our endogenous AcrB structure and previously reported structures from reconstituted systems, including a more detailed discussion of lipid densities.

Reviewer #3 (Public review):

Summary:

The manuscript "Structural mechanisms of pump assembly and drug transport in the AcrAB-TolC efflux system" by Ge et al. describes the identification of a previously uncharacterized lipoprotein, YbjP, as a novel partner of the well-studied Enterobacterial tripartite efflux pump AcrAB-TolC. The authors present cryo-electron microscopy structures of the TolC-YbjP subcomplex and the complete AcrABZ-TolC-YbjP assembly. While the identification and structural characterization of YbjP are potentially novel, the stated focus of the manuscript-mechanisms of pump assembly and drug transport - is not sufficiently addressed. The manuscript requires reframing to emphasize the principal novelty associated with YbjP and significant development of the other aspects, especially the claimed novelty of the AcrB drug-efflux cycle.

Strengths:

The reported association of YbjP with AcrAB-TolC is novel; however, a recent deposition of a preceding and much more detailed manuscript to the BioRxiv server (Horne et al., https://doi.org/10.1101/2025.03.19.644130) removes much of the immediate novelty.

Weaknesses:

While the identification of YbjP is novel, the authors do not appear to acknowledge the precedence of another work (Horne et al., 2025), and it is not cited within the correct context in the manuscript.

We thank the reviewer for raising this important point regarding the independent nature of our work.

Our study indeed progressed independently. The process began with our purification of an endogenous protein sample containing the AcrAB-TolC efflux pump. During our cryo-EM analysis, we observed an unassigned density in the map, for which we built a preliminary main-chain model. A subsequent search of structural databases, including AlphaFold predictions, allowed us to identify this density as the protein YbjP. It was only after this identification that we became aware of the related preprint by Horne et al. on BioRxiv (Posted March 19, 2025).

Therefore, our structural determination of YbjP was conducted entirely independently. We fully acknowledge and respect the work by Horne et al. and have already cited their preprint in our manuscript. While their detailed structural data, maps, and coordinates were not publicly available as of March 13, 2026, we have described their findings appropriately. We agree that our manuscript can better reflect this context and will carefully check for any missing citations to ensure that their contribution is properly and clearly acknowledged.

We also believe that the two studies are mutually complementary and collectively reinforce the emerging understanding of YbjP.

Several results presented in the TolC-YbjP section do not represent new findings regarding TolC structure itself.

We agree that the TolC features we describe are consistent with previously reported structural characteristics. However, these observations could only be confirmed in the context of the newly determined TolC–YbjP subcomplex, which was not available prior to this study. We have clarified this point in the revision to avoid overstating novelty.

The structure and gating behaviour of TolC should be more thoroughly introduced in the Introduction, including prior work describing channel opening and conformational transitions.

We appreciate this suggestion and agree that a more comprehensive overview of TolC gating and conformational transitions will strengthen the Introduction. We have revised the text to incorporate relevant prior structural and functional studies.

The current manuscript does not discuss the mechanistic role of helices H3/H4 and H7/H8 in channel dilation, despite implying that YbjP binding may influence these features.

Thank you for this comment. The primary novel contributions of this manuscript are the identification of YbjP and the structural characterization of AcrB in three distinct states. The discussion of the dilation mechanism, while included because we observed the closed TolC-YbjP state, is a secondary point. In the revised manuscript, we have expanded this discussion as suggested.

Only the original closed TolC structure is cited, and the manuscript does not address prior mutational studies involving the D396 region, though this residue is specifically highlighted in the presented structures.

We appreciate the reviewer drawing attention to this oversight. We have added citations to the relevant mutational and mechanistic studies, including those involving the D396 region, and more clearly discussed these findings in relation to our structural observations.

The manuscript provides only a general structural alignment between the closed TolC-YbjP subcomplex and the open TolC observed in the full pump assembly. However, multiple open, closed, and intermediate conformations of AcrAB-TolC have already been reported. Thus, YbjP alone cannot be assumed to account for TolC channel gating. A systematic comparison with existing structures is necessary to determine whether YbjP contributes any distinct allosteric modulation.

We agree with the reviewer’s assessment and appreciate the constructive suggestion. In our revised manuscript, we have expanded the structural comparison to include previously reported open, closed, and intermediate AcrAB–TolC conformations. This expanded analysis will more clearly position our findings within the existing structural framework.

The analysis of AcrB peristaltic action is superficial, poorly substantiated and importantly, not novel. Several references to the ATP-synthase cycle have been provided, but this has been widely established already some 20 years ago - e.g. https://www.science.org/doi/10.1126/science.1131542.

We thank the reviewer for this comment. We fully acknowledge the foundational studies that established the AcrB functional cycle and its analogy to the ATP-synthase mechanism. While previous work indeed defined the LTO (Loose, Tight, Open) cycle of AcrB, those structures were obtained using AcrB in isolation. In contrast, our endogenous sample, which includes the native constraints of AcrA from above and the presence of AcrZ, reveals conformational changes in the transmembrane and porter domains that differ from those previously reported. We interpret these differences as reflecting a more physiologically relevant mechanism. In our revision, we provided a detailed discussion to contextualize these distinctions within the existing literature.

The most significant limitation of the study is the absence of functional characterization of YbjP in vivo or in vitro. While the structural association between YbjP and TolC is interesting, the biological role of YbjP remains unclear.

To explore the potential physiological role of YbjP, we compared the viability of a ΔybjP mutant in the E. coli C600 background with that of the wild-type C600 strain under ciprofloxacin (CIP) stress. However, we did not observe a detectable difference in survival between the two strains under the tested conditions. This result is consistent with the assay reported in the preprint mentioned by the reviewer, although the stress conditions used in that study differ from ours.

Author response image 1.

To further address this point, we have added a new Supplementary Figure S3 comparing outer membrane proteins with structural and functional similarities to TolC. As shown in this analysis, many such proteins contain an extracellular loop that appears to help anchor or stabilize them within the outer membrane. Notably, TolC lacks such a loop, whereas YbjP contains a corresponding loop region, suggesting that YbjP may potentially play a role in stabilizing or positioning TolC in the outer membrane.

While our current experiments did not reveal a clear phenotype under CIP stress, the structural observations still suggest that YbjP may have a physiological role. We have therefore expanded the Discussion to more carefully consider possible functional implications of YbjP and to explicitly acknowledge the limitations of the present study regarding its physiological characterization.

Moreover, the manuscript does not examine structural differences between the presented complex and previously solved AcrAB-TolC or MexAB-OprM assemblies that might support a mechanistic model.

We thank the reviewer for this suggestion. We now provide a more detailed comparative analysis with previously reported AcrAB–TolC and MexAB–OprM structures, highlighting both similarities and key differences.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) To address the probable role of YbjP, performing 3D variability analysis on the sub-complex and the complete complex would help clarify whether YbjP participates in channel opening and closing.

YbjP does not participate in the opening or closing of the TolC channel. Indeed, the structure of TolC shows no conformational changes upon YbjP binding when compared to the free, closed form of TolC. The structural transition between the closed and open states of TolC has been thoroughly reviewed by Alav et al. (Chem. Rev. 2021).

Although the particles for the two reconstructions were obtained from the same dataset, inspection of the raw micrographs and the corresponding 2D class averages clearly shows that the particles fall into two distinct populations: one containing only the TolC–YbjP sub-complex and the other containing the full AcrABZ–TolC–YbjP assembly. In other words, the particles correspond to two different complexes, distinguished by the absence or presence of the AcrABZ components, rather than representing two conformational states of a single complex.

Three-dimensional variability analysis (3DVA) is most appropriate for analyzing structural heterogeneity arising from continuous or discrete conformational changes within the same macromolecular assembly. Because the heterogeneity in our dataset primarily reflects compositional differences between two assemblies rather than conformational variability within a single complex, we believe that applying 3DVA would not be appropriate for this dataset.

(2) In addition to the above points, a few minor revisions would improve clarity and readability. Some of the representative density maps in the supplementary figures could be refined for clarity. Adjusting formatting elements (e.g., dashed line thickness) may improve visual presentation.

Supplementary Figures S2, S5, and S6 have been redrawn to reduce the excessive thickness of the density map representations for better visualization.

Reviewer #2 (Recommendations for the authors):

In this manuscript, Xiaofei and colleagues report the high-resolution cryo-EM structure of the TolC-YbjP-AcrABZ complex, as well as the structure of a subcomplex containing only TolC and YbjP. Additionally, they identify a previously unidentified accessory subunit that plays a role in the function of this complex. Overall, this represents an impressive effort in determining the complete endogenous complex from E. coli and performing systematic analyses. I have a few questions regarding the manuscript:

(1) The authors use the term "native" several times (e.g., lines 24, 73, 157, 256) to refer to the complex reported here. This may cause confusion, given the use of detergent to extract endogenous complexes from E. coli. They should consider excluding the possibility that the subcomplex was formed during the purification process. The term "endogenous" should suffice in this context.

We have replaced “native” with “endogenous”.

(2) Lines 26-28: The phrase "its protomers" may lead to ambiguity, as it could refer to either YbjP or TolC.

The sentence has been updated to “…bridging the TolC protomers at their equatorial domain.”

(3) Lines 50-51: The text suggests that the assembly of AcrA and AcrB triggers TolC's transition from a closed to an open conformation. Please clarify this point.

The introduction (lines 50-51) has been expanded to describe the assembly of TolC and AcrAB, as well as the gating transition between the closed and open states of TolC.

(4) Lines 57-59: Using cryo-EM may get the low-to-medium resolution map, but not using low-to-medium resolution cryo-EM.

The sentence has been changed to … prior studies using crystallography and cryo-EM have revealed low-to-medium resolution snapshots of the assembled pump.

(5) Line 73: The authors should consider briefly introducing how they prepared the samples for cryo-EM structural studies, as this is a highlight of the manuscript.

A detailed, multi-step purification protocol has been added as Supplementary Figure S1A to illustrate the sample preparation procedure.

(6) Lines 77-82: The authors should label these structural features in the corresponding figures for easier reference, particularly clarifying which part refers to the "equatorial domain."

We have labeled these structural features in the corresponding figures for clarity, and specifically indicated which region corresponds to the equatorial domain.

(7) Lines 92-93: The first α-helix of TolC is unclear; the authors should indicate the corresponding residues of this helix in the main text. Additionally, it would be beneficial to illustrate the interface in a figure for easier access.

We have specified the residues corresponding to the participating α-helix of TolC in the main text and illustrated the interaction interface in a figure (Figure 1F) for better visualization.

(8) Lines 99-100: Did the authors observe additional density for N-palmitoyl and S-diacylglycerol modifications in their cryo-EM density map? If so, they should highlight this in a figure to demonstrate the importance of these modifications.

The N-palmitoyl and S-diacylglycerol modifications are embedded in the outer membrane but lack a consistent location within it. As a result, they were averaged out during cryo-EM reconstruction and are not visible in our final map.

(9) Line 122: Please indicate the 33 nm height in the figure.

The 33 nm height is composed of a 14 nm TolC channel, a 14 nm periplasmic portion of AcrAB, and a 5 nm transmembrane portion of AcrB, which has been added to the right side of Figure 2B.

(10) Lines 123-124: This sentence feels out of place. It would be more appropriate to move it to another location, such as the beginning of the Results section, to introduce how the samples were prepared.

This sentence has been moved to the section “Structure of a TolC–YbjP closed-state complex” to describe the sample preparation.

(11) Lines 127-128: This section needs to be rewritten for improved clarity.

This sentence has been rewritten as “This tripartite architecture is stabilized by three distinct sets of interfaces: (i) contacts between the AcrB trimer and the basal regions of AcrA, (ii) extensive AcrA–AcrA lateral interactions within the hexameric ring, and (iii) tip-to-tip junctions formed between the upper AcrA α-helical hairpin and the periplasmic entrance of TolC (Figure 2D).”

(12) Line 141: Please define terms like DN, DC, PN, and PC upon their first use.

DN and DC (denoting the N- and C-terminal subdomains of the docking domain), PN and PC (named for the N- and C-terminal subdomains of the periplasmic (porter) domain) have been defined where they first appear in the text.

(13) The lα helix of AcrB is at least partially buried in the membrane (Liu H. et al, PNAS 2025). The authors should consider including this information in their figures, particularly Figure 2B and Figure 5. As the complex is endogenously purified, are there any differences in AcrB compared to those observed in liposomes, SMALP, or vesicles? Did the authors observe significant lipid densities?

A structural comparison of the AcrB holocomplex with an AcrB structure determined in the native membrane environment (PDB: 9DXN) has been added as Supplementary Figure S8D. In the transmembrane region of AcrB, some sausage-like densities were observed; however, lipid molecules were not modelled in the study.

(14) The protein purification profile should be included, at least as a supplementary figure.

The protein purification profile has been added to Supplementary Figure S1A.

Reviewer #3 (Recommendations for the authors):

(1) The identification and structural characterization of YbjP as a novel TolC-associated lipoprotein is potentially interesting, and the cryo-EM structures of the TolC-YbjP subcomplex and the complete pump assembly represent a solid starting point. However, the manuscript currently does not sufficiently support the broader mechanistic conclusions implied by the title regarding pump assembly and drug transport. To strengthen the work, the manuscript would benefit from being refocused to highlight the novelty of YbjP, while also providing a clearer mechanistic rationale for its functional role.

We thank the reviewer for this helpful comment. We have revised the manuscript to better highlight the novel features of YbjP and provide a clearer mechanistic explanation for its function.

Most Gram-negative TolC homologs, including P. aeruginosa OprM and E. coli CusC, carry native lipid anchors that attach them to the outer membrane. However, E. coli TolC lacks this N-terminal lipidation site. We propose that YbjP, a dually lipidated protein modified with N-palmitoyl and S-diacylglycerol groups, tethers TolC to the outer membrane and functionally replaces the intrinsic lipid anchors found in other outer membrane factors.

To support this mechanism, we have added Supplementary Figure S3, which compares the anchoring domains of six representative outer membrane components of efflux pumps.

(2) The structural features and gating dynamics of TolC should be more thoroughly introduced, including prior work describing channel dilation and helix movements (e.g., PMID: 18406332; PMID: 21245342), and the manuscript should discuss how YbjP may influence these known conformational transitions. The relevance of the D396 region should also be considered in the context of previous mutational analyses (e.g., PMID: 32850959).

All citations mentioned have been added. Indeed, the structure of TolC shows no conformational changes upon YbjP binding when compared to the free, closed form of TolC.

(3) Structural interpretation of the YbjP-containing complexes needs to be strengthened by comparison with the extensive library of available AcrAB-TolC structures in open, closed, and intermediate states (e.g., PMID: 28355133; PMID: 24747401; PMID: 34506732). Such analysis is necessary to determine whether YbjP contributes any distinct allosteric or conformational effects.

YbjP binds to the equatorial domain of TolC, distant from the tip of its coiled-coil helices. This binding therefore does not interfere with TolC’s functional role, but rather helps anchor TolC within the outer membrane in the correct orientation.

(4) The speculations regarding the peristaltic nature of AcrB cycling as currently presented in the text and Figure 4 lack novelty and currently reiterate well-established AcrB L/T/O states without offering insight into how YbjP might influence long-range communication within the complex.

We thank the reviewer for this valuable comment. We agree that the functional rotation mechanism of AcrB with loose, tight and open states has been well documented in previous work.

In our endogenous intact complex, however, we identified substantial conformational changes in both the porter and transmembrane domains of AcrB that were not observed in earlier isolated structures. To highlight these differences, we have added Supplementary Figure S8 to compare our AcrB structure with all previously reported conformational states.

On the basis of these structural observations, we have proposed a distinct drug efflux mechanism, which is now described in detail in the revised manuscript.

(5) Specific clarification is needed regarding the proposed pathway by which YbjP could modulate AcrA or AcrB, given the spatial separation observed in the structures.

YbjP binds to the equatorial domain of TolC, which has no effect on AcrA or AcrB.

(6) The manuscript currently lacks functional validation of YbjP, either in vivo or in vitro. Incorporating even basic assays to test YbjP's contribution to efflux function, pump assembly, or antibiotic resistance would significantly enhance the conclusions.

To explore the potential physiological role of YbjP, we compared the viability of a ΔybjP mutant in the E. coli C600 background with that of the wild-type C600 strain under ciprofloxacin (CIP) stress. However, we did not observe a detectable difference in survival between the two strains under the tested conditions. This result is consistent with the assay reported in the preprint mentioned by the reviewer, although the stress conditions used in that study differ from ours. (See Author response image 1).

To further address this point, we have added a new Supplementary Figure (Fig. S3) comparing outer membrane proteins with structural and functional similarities to TolC. As shown in this analysis, many such proteins contain an extracellular N-terminal loop that appears to help anchor or stabilize them within the outer membrane. Notably, TolC lacks such a loop, whereas YbjP contains a corresponding loop region, suggesting that YbjP may potentially play a role in stabilizing or positioning TolC in the outer membrane.

While our current experiments did not reveal a clear phenotype under CIP stress, the structural observations still suggest that YbjP may have a physiological role. We have therefore expanded the Discussion to more carefully consider possible functional implications of YbjP and to explicitly acknowledge the limitations of the present study regarding its physiological characterization.

(7) The relationship to the prior BioRxiv work by Horne et al. (March 19, 2025) should be discussed more directly, particularly because it reports the same YbjP-TolC association across two different efflux systems and includes higher-resolution structures and functional evidence. The current citation should be revised to accurately acknowledge the precedence and overlap in findings.

We thank the reviewer for this important suggestion. We have adjusted the citation to earlier in the manuscript to properly acknowledge the work by Horne et al.

We fully agree that a direct comparison between our structures and those reported by Horne et al. would be highly valuable. However, although nearly a year has passed since the preprint was posted, their atomic coordinates have not been released in the Protein Data Bank. No detailed structural coordinates or models are provided in the preprint itself, which prevents us from performing a meaningful, structure-based comparison with our own data at this stage.

(8) The references used to support statements on allosteric pump activation (e.g., lines 182-183) should be updated to include more relevant full-complex studies (e.g., PMID: 28355133; PMID: 33009415; PMID: 33909410), and the manuscript should more clearly articulate any proposed mechanism for signal transmission involving YbjP.

The citations have been added.

YbjP does not participate in the opening or closing of the TolC channel. Indeed, the structure of TolC shows no conformational changes upon YbjP binding when compared to the free, closed form of TolC.

(9) Overall, while the structural identification of YbjP is noteworthy, additional functional data and more rigorous structural comparison are needed to substantiate the proposed model of pump assembly and drug transport. Reframing the manuscript to emphasize the novelty of YbjP and clarifying its potential mechanistic role would strengthen the work significantly.

We refer the reviewer to our earlier response for additional functional data. We have added Supplementary Figure S8 to compare our AcrB structure with all previously reported conformational states.

eLife Assessment

This important study examined age-related changes in cerebellar function by testing a large sample of younger and older adults, including 30 over 80 years old, on motor and cognitive tasks linked to the cerebellum and conducting structural imaging. Their findings show that cerebellar-dependent functions are mostly maintained or even enhanced across the lifespan, with cerebellar-mediated motor abilities remaining intact despite degeneration, in contrast to non-cerebellar measures. Overall, the authors provide compelling evidence in support of preserved cerebellar function with age. These results highlight the resilience and redundancy of cerebellar circuits and offer key insights into aging and motor behavior.

Reviewer #1 (Public review):

Summary:

Witte et al. examined whether canonical behavioral functions attributed to the cerebellum decline with age. To test this, they recruited younger, old, and older-old adults in a comprehensive battery of tasks previously identified as cerebellar-dependent in the literature. Remarkably, they found that cerebellar function is largely preserved across the lifespan-and in some cases even enhanced. Structural imaging confirmed that their older adult cohort was representative in terms of both cerebellar gray- and white-matter volume. Overall, this is an important study with strong theoretical implications and compelling evidence supporting the motor reserve hypothesis, demonstrating that cerebellar-dependent measures remain largely intact with aging.

Strengths:

(1) Relatively large sample size.

(2) Most comprehensive behavioral battery to date assessing cerebellar-dependent behavior.

(3) Structural MRI confirmation of age-related decline in cerebellar gray and white matter, ensuring representativeness of the sample.

Weaknesses:

The absence of a voxel-based morphometry (VBM) analysis limits the anatomical and functional specificity of the conclusions. Such an analysis would help identify which functions are truly cerebellar-dependent, rather than relying primarily on inferences drawn from prior neuropsychological literature. Notably, the authors have undertaken this analysis in a separate manuscript.

As acknowledged in the Discussion, the classification of tasks as "cerebellar-dependent" versus "general" remains somewhat ambiguous. Some measures labeled as "general" may still engage cerebellar processes. Moreover, analyses in the authors' forthcoming manuscript show weak structure-behavior correlations, casting further doubt on how clearly cerebellar-specific functions can be distinguished from more general processes.

Reviewer #2 (Public review):

Summary:

The authors are investigating cerebellar-mediated motor behaviors in a large sample of adults, including 30 individuals over the age of 80 (a great strength of this work). They employed a large battery of motor tasks that are tied to cerebellar function, in addition to a cognitive task and motor tasks that are more general. They also evaluated cerebellar structure. Across their behavioral metrics, they found that even with cerebellar degeneration, cerebellar-mediated motor behavior remained intact relative to young adults. However, this was not the case for measures not directly tied to cerebellar function. The authors suggest that these functions are preserved and speak to the resiliency and redundancy of function in the cerebellum. They also speculate that cerebellar circuits may be especially good for preserving function in the face of structural change. The tasks are described very well, and their implementation is also well-done with consideration for rigor in the data collection and processing. The inclusion of Bayesian estimates is also particularly useful, given the theoretically important lack of age differences reported. This work is methodologically rigorous with respect to the behavior, and certainly thought-provoking.

Strengths:

The methodological rigor, inclusion of Bayesian statistics, and the larger sample of individuals over the age of 80 in particular are all great strengths of this work. Further, as noted in the text, the fact that all participants completed the full testing battery is of great benefit. Please note, upon my second review the strengths remain. This is a really wonderful investigation and amazingly comprehensive from a behavioral perspective given the numerous tasks and domains that were considered.

Weaknesses:

The suggestion of cerebellar reserve, given that at the group level there is a lack of difference for cerebellar specific behavioral component,s could be more robustly tested. That is, the authors suggest that this is a reserve given that volume of cerebellar gray matter is smaller in the two older groups, though behavior is preserved. This implies volume and behavior are seemingly dissociated. However, there is seemingly a great deal of behavioral variability within each group and likewise with respect to cerebellar volume. Is poorer behavior associated with smaller volume? If so, this would suggest still that volume and behavior are linked; but, rather than being age that is critical it is volume. On the flip side, a lack of associations between behavior and volume would be quite compelling with respect to reserve. More generally, as explicated in the recommendations, there are analyses that could be conducted that, in my opinio,n would more robustly support their arguments given the data that they have available.

The authors have done wonderful work to address the comments from the initial feedback/reviews. While I may ultimately disagree with the approach of including the imaging data in another manuscript, that is at the same time, a reasonable decision. This, however, does not change the impression that the paper would be stronger with the inclusion of the volumetric imaging data. I can understand why it may be published separately - it would be a very long paper to include both. At the same time the assertions made here, which are largely nicely supported by the preprint, would ultimately strengthen this work. The behavior certainly stands on its own as an excellent and needed investigation; together, both pieces make for a truly excellent contribution to the literature.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Witte et al. examined whether canonical behavioral functions attributed to the cerebellum decline with age. To test this, they recruited younger, old, and older-old adults in a comprehensive battery of tasks previously identified as cerebellar-dependent in the literature. Remarkably, they found that cerebellar function is largely preserved across the lifespan-and in some cases even enhanced. Structural imaging confirmed that their older adult cohort was representative in terms of both cerebellar gray- and white-matter volume. Overall, this is an important study with strong theoretical implications and convincing evidence supporting the motor reserve hypothesis, demonstrating that cerebellar-dependent measures remain largely intact with aging.

Strengths:

(1) Relatively large sample size.

(2) Most comprehensive behavioral battery to date assessing cerebellar-dependent behavior.

(3) Structural MRI confirmation of age-related decline in cerebellar gray and white matter, ensuring representativeness of the sample.

Weaknesses:

(1) Although the authors note this was outside the study's scope, the absence of a voxel-based morphometry (VBM) analysis limits anatomical and functional specificity. Such an analysis would clarify which functions are cerebellar-dependent rather than solely inferring this from prior neuropsychological literature.

(2) As acknowledged in the Discussion, task classification (cerebellar-dependent vs. general measures) remains somewhat ambiguous. Some "general" measures may still rely on cerebellar processes based on the paper's own criteria - for example, tasks in which individuals with cerebellar degeneration show impairments.

(3) Cerebellar-dependent and general measures may inherently differ in measurement noise, potentially biasing results toward detecting effects in general measures but not in cerebellar-dependent ones.

We appreciate Reviewer #1's positive assessment of the study, including the acknowledgment of our large sample size, comprehensive behavioral battery, and verification of cerebellar atrophy using MRI. We address the concerns raised as follows:

(1) Voxel-based morphometry (VBM) and anatomical specificity

We agree that VBM would strengthen anatomical specificity. As noted in our response to private comments, we have carried out these analyses as part of a separate dedicated study, now available as a preprint (“Aging is associated with uniform structural decline across cerebellar regions while preserving topological organization and showing no relation with sensorimotor function”, https://doi.org/10.64898/2026.02.13.705695). This work investigates region-level cerebellar aging and its relationship with behavior in detail, including both anatomical and functional parcellations. In short, the preprint demonstrates the absence of structure-function relationship between cerebellar regions (from either anatomical or functional atlases) and cerebellar function. Given the scope of the present manuscript, which focuses primarily on behavioral evidence for cerebellar preservation, we chose not to expand this paper further with VBM results.

(2) Task classification and cerebellar involvement

We clarified in the revised manuscript that even “general” measures likely involve cerebellar processing to some extent. We have strengthened the discussion explaining that these measures do not primarily depend on cerebellar function, in contrast to the cerebellar-specific metrics derived from established models (e.g., clock variance in rhythmic tapping). We now explicitly caution against interpreting these general measures as cerebellar-independent.

(3) Measurement noise and differential sensitivity

To address the reviewer’s concern that measurement noise may differ between task categories, we now report split-half reliabilities for all measures in the Supplement. These data demonstrate no systematic reliability disadvantage for cerebellar-specific tasks that could explain the pattern of results.

Reviewer #2 (Public review):

Summary:

The authors are investigating cerebellar-mediated motor behaviors in a large sample of adults, including 30 individuals over the age of 80 (a great strength of this work). They employed a large battery of motor tasks that are tied to cerebellar function, in addition to a cognitive task and motor tasks that are more general. They also evaluated cerebellar structure. Across their behavioral metrics, they found that even with cerebellar degeneration, cerebellar-mediated motor behavior remained intact relative to young adults. However, this was not the case for measures not directly tied to cerebellar function. The authors suggest that these functions are preserved and speak to the resiliency and redundancy of function in the cerebellum. They also speculate that cerebellar circuits may be especially good for preserving function in the face of structural change. The tasks are described very well, and their implementation is also well-done with consideration for rigor in the data collection and processing. The inclusion of Bayesian estimates is also particularly useful, given the theoretically important lack of age differences reported. This work is methodologically rigorous with respect to the behavior, and certainly thought-provoking.

Strengths:

The methodological rigor, inclusion of Bayesian statistics, and the larger sample of individuals over the age of 80 in particular are all great strengths of this work. Further, as noted in the text, the fact that all participants completed the full testing battery is of great benefit.

Weaknesses:

The suggestion of cerebellar reserve, given that at the group level there is a lack of difference for cerebellar-specific behavioral components, could be more robustly tested. That is, the authors suggest that this is a reserve given that the volume of cerebellar gray matter is smaller in the two older groups, though behavior is preserved. This implies volume and behavior are seemingly dissociated. However, there is seemingly a great deal of behavioral variability within each group and likewise with respect to cerebellar volume. Is poorer behavior associated with smaller volume? If so, this would still suggest that volume and behavior are linked, but rather than being age that is critical, it is volume. On the flip side, a lack of associations between behavior and volume would be quite compelling with respect to reserve. More generally, as explicated in the recommendations, there are analyses that could be conducted that, in my opinion, would more robustly support their arguments given the data that they have available. This is a well-executed and thought-provoking investigation, but there is also room for a bit more discussion.

We appreciate Reviewer’s recognition of the methodological rigor of the study. The public review focuses on the structure-function relationship for the cerebellum. Given that the volume of the cerebellum is smaller in older adults but that the identified cerebellar function are maintained, we conclude that there is no structure-function relationship. We agree with the reviewer that this could be tested further by looking at different parcellations of the cerebellum and demonstrating the absence of association between smaller regions of the cerebellum and the investigated cerebellar function. We agree with the reviewer that this is interesting but believe that this goes beyond the scope of this already extensive paper. For this reason, detailed analyses of the structure-function relationship are available in the preprint version of another paper entitled “Aging is associated with uniform structural decline across cerebellar regions while preserving topological organization and showing no relation with sensorimotor function”, (https://doi.org/10.64898/2026.02.13.705695). In this preprint, across multiple anatomical and functional parcellations, we found no meaningful association between cerebellar structure and cerebellar-specific behavioral measures.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Prefacing these suggestions, I want to commend the authors for undertaking this Herculean effort, recruiting such a large sample and administering an extensive battery of tasks. This is an impressively comprehensive study!

(1) Lesion-symptom mapping. The authors state that lesion-symptom mapping was beyond the scope of the study, but it is unclear why such an analysis could not be performed. Including it would strengthen inferences linking cerebellar structure to behavioral outcomes and help differentiate cerebellar-specific from general performance measures.

(2) Inter-measure correlations. For cerebellar-dependent tasks, did the authors examine correlations among behavioral measures? If cerebellar aging effects are relatively uniform across the cerebellar cortex, performance across tasks engaging distinct cerebellar regions should, in theory, covary. Similar pairwise correlations for general measures could provide a useful comparison.

1 + 2: We fully agree with this two points; however, we decided to address this analysis in a separate paper. In the current manuscript, our primary focus was on the behavioral aspects, as these are already quite extensive on their own. In our subsequent work, we conducted an in-depth investigation into the relationship between cerebellar-specific measures and cerebellar structure across distinct cerebellar regions (including anatomical regions and functionally defined regions according to the atlas of Nettekoven et al., 2024). We found that aging does not affect the cerebellum uniformly, but that some anatomical regions exhibit stronger age effects. For the functionally defined regions the age effects were uniformly though. There was no relation between behavioral cerebellar-specific measures and regional gray matter structure.

In this second paper we also analyzed inter-measure correlations between behavioral cerebellar-specific measures. We did not find any correlations between cerebellar outcomes of different tasks, which indeed could indicate that the different tasks engage distinct cerebellar regions. In addition, we did not find any relation between cerebellar outcomes and anatomically or functionally defined cerebellar regions.

You can find a preprint of the second manuscript entitled “Aging is associated with uniform structural decline across cerebellar regions while preserving topological organization and showing no relation with sensorimotor function” here: https://doi.org/10.64898/2026.02.13.705695

(3) Measurement sensitivity. Could differences in age effects reflect varying measurement noise between cerebellar-specific and general measures? For instance, even among younger participants, cerebellar-related measures (e.g., slope in mental rotation) might exhibit greater variability - given that they depend on more conditions, each with its own noise - than general metrics (e.g., baseline motor variability or choice reaction time estimated from a single condition). This could affect sensitivity to detect age-related change and bias results toward finding effects in general rather than cerebellar-specific measures.

To address this concern, we computed split-half reliability for both cerebellar-specific and general sensorimotor measures and added these estimates to the supplementary materials. As can be seen from Author response table 1, there is no consistent pattern of lower reliability for cerebellar-specific measures that could plausibly account for the absence of age-related effects.

Author response table 1.

Split-half reliabilities

(4) Task dependence on the cerebellum. It is difficult to argue that measures such as reach accuracy, choice reaction time, or rhythm deviation are non-cerebellar. Ataxia certainly impacts reach accuracy. Although patient evidence is mixed - and even when there is a lack of dissociation (e.g., prolonged choice reaction times in both cerebellar and PD groups) - this does not preclude cerebellar involvement in these measures. Indeed, as the authors stated, claims of cerebellar independence should therefore be made cautiously (can be addressed by VBM in comment 1).

In the paper we tried to emphasize that the general sensorimotor measures still involve cerebellar functions, as this is the case with many movement-related measures. However we theorized that they do not primarily depend on cerebellar function. For example rhythm deviation in the finger tapping task is influenced by cerebellar timing mechanisms as well as motor execution noise, attention, etc. While the cerebellar-specific measure from this task, which is the clock variance, has been shown to extract the contribution of cerebellar-dependent timing mechanisms to this task (Ivry & Keele, 1989).

On p.37, we added the following paragraph:

“Similarly, it is important to recognize that general sensorimotor performance is not independent of cerebellar processing. Many broad measures, such as movement accuracy, reaction time, likely reflect contributions from many different brain regions including the cerebellum. As a result, age‑related differences in general sensorimotor performance may emerge from multiple interacting systems rather than cerebellar function alone.”

(5) Interpreting preserved or enhanced function. The finding of preserved - or even enhanced - performance in older adults is compelling. The authors interpret this as evidence for cerebellar reserve or compensation for cortical decline. An alternative explanation is that cerebellar structures simply decline more slowly than cortical ones, as their gray-matter data suggest; so rather than cerebellar activity revving up, it may remain the same: For example, following up on several of the authors' prior papers, Cisneros et al. (2024) reported enhanced implicit recalibration with age, potentially reflecting greater reliance on cerebellar forward models as sensory (especially proprioceptive) signals degrade. However, this may reflect reweighting rather than compensation - where cerebellar contributions are not enhanced, but rather preserved as other systems decline more rapidly. It would be valuable for the authors to clarify whether they view their findings as evidence of reweighting (slower decline) or compensation (increased contribution).

We completely agree with this additional interpretation and added a small section to the discussion about it. However, based on the structural cerebellar measures that we have, it is difficult to state whether the reweighting or compensation theory would be more plausible. In either way, both are in line with the cerebellar reserve theory

Added to discussion (P. 35):

Importantly, the relative preservation of cerebellar structure compared to other systems may itself contribute to the maintained cerebellar function observed in older age. Even if structural decline is present, the fact that it progresses more slowly than in many cortical and subcortical regions suggests that a form of structural reserve remains available in the cerebellum. This structural reserve could underlie the continued efficiency of cerebellar circuits and support their capacity to sustain motor functions across aging.

(6) Mental rotation and the continuity hypothesis. The age-related decline in mental rotation performance, if cerebellar-dependent (see McDougle et al., 2022; note minor inconsistency in citation format throughout the paper), supports emerging theories that the cerebellum supports continuous mental simulations in both cognition and action, whether it's forward model simulation or interval-based timing in the motor control domain or mental rotation/intuitive physics in the cognitive domain (Tsay & Ivry, 2025). Given that mental rotation showed the strongest age effect, it would be fascinating to examine whether this correlates with structural loss in Crus I/II, regions most implicated in higher-order cognitive functions - related to Comment 1 above. Even on a crude level, without correlating with behaviour, do the authors have a map for which areas show greater degeneration than others?

This is also something we did in the other paper mentioned before (Figure 5 of the new preprint). At a first glimpse, the mental rotation outcomes show a strong positive correlation with Crus I and a negative correlation with Crus II, however none of these were significant and the fact that their sign is opposite suggest that these might be random. Indeed, in the preprint, we also compare age-related changes in grey matter volumes for different anatomical and functional cerebellar regions (Figure 1).

The inconsistencies in citation format have been fixed as well.

(7) Continuous age analyses. An exploratory analysis correlating age (as a continuous variable) with each dependent measure might provide greater sensitivity than categorical group comparisons, revealing more graded relationships between age and performance.

Our experiment was not designed to perform such analysis. Testing for group differences provides more power than testing for correlations. For this reason, given that our clearly separated age groups did not show any behavioral differences, we do not expect such an analysis to provide substantial additional insight. Given that the paper is already very extensive, we haven’t performed this additional analysis.

Congratulations on this comprehensive piece of work!

Thank you for your kind words

Reviewer #2 (Recommendations for the authors):

In the introduction, the authors note that the current literature on the cerebellum in aging has evidence from "studies that relied on single-task paradigms", including a citation to an eye-blink conditioning study. They then note "instead of capturing a broader range of specific cerebellar functions". What do they mean by this? Eye-blink conditioning, for example, when administered in a delay paradigm, is tied directly to the cerebellum and is arguably a cerebellar function or learning paradigm. Some clarity about his point is needed.

The meaning of this is that most previous studies examining cerebellar function in older adults relied on a single task, or on tasks that were functionally very similar, such as balance and gait, to assess performance. In contrast, our study incorporated multiple tasks targeting different sensorimotor skills, allowing us to identify broader patterns in cerebellar sensorimotor performance in older adults.

To make this clearer, we have rephrased the sentence (p.4):

“However, much of the evidence supporting this theory comes from studies that narrowly focused on a single task (Boisgontier & Nougier, 2013; Miller et al., 2013; Woodruff-Pak et al., 2001) or on assessments within similar cerebellar domains such as balance and gait (Droby et al., 2021; Rosano et al., 2007), instead of capturing a broader range of specific cerebellar functions.”

The authors note that many cerebellar tasks that are impaired in patients are preserved in older adults. The authors, however, seem to ignore delay eyeblink conditioning. Gerwig and colleagues (2010, Behav Brain Res) have shown that this is impacted in patients, and it is also robustly impacted in aging. Older adults still learn, but the age effects are highly replicable. A clear discussion of eye-blink conditioning and how it fits into this framework, and with your findings here, would be really helpful. It seems like a notable oversight not to have it discussed, given the age effects in this context, even if it was not included as a measure.

Eye blink conditioning is an interesting example that seems to contradict our theory: eye-blink conditioning is both affected by age and dependent on the cerebellum. However, while age-related changes in cerebellar structure evolve continuously with age, changes in eye-blink conditioning performance remains unchanged between 40 and 80 years old. Therefore, eye-blink conditioning suggest that age-related changes in cerebellar structure are not related to possible age-related changes in function. This discussion was already included in the manuscript on p. 36, which reads as:

“Similarly, no eye-blink conditioning task was included, as it is heavily influenced by cognitive factors such as awareness and arousal, and fear conditioning (LaBar et al., 2004). Previous work has shown that many variables, such as blink reaction time and motor components of the eyeblink reflex, introduce substantial variability in responses at older age (Woodruff-Pak & Jaeger, 1998). In contrast, this study found that only performance on the rhythmic finger-tapping task, similar to what we included in our battery, emerged as a significant predictor of age-related differences in eye-blink conditioning. Furthermore, age-related differences appeared to plateau after early adulthood, with no significant variation in the percentage of correct responses between ages 40 and 80 (Woodruff-Pak & Jaeger, 1998). Practically, the extended duration of the training protocol also makes this task unsuitable for inclusion in a test battery (Winton et al., 2025).”

This approach also does not consider variability within older adults. That is, on average, they may do better than patients. But, there are also individual differences in cerebellar metrics (structure, for example) within an older adult sample that are a critical consideration here. When looking at the behavioral plots that include the individual data points (which is a great addition and very helpful), it is clear that variability is prevalent. As noted below, it may still be that cerebellar metrics are associated with behavior, given the high degree of variability within the groups across aging.

We agree with the reviewer that variability is prevalent, as it is in any experiment. In our latest preprint entitled “Aging is associated with uniform structural decline across cerebellar regions while preserving topological organization and showing no relation with sensorimotor function” (https://doi.org/10.64898/2026.02.13.705695), we investigated whether variability in cerebellar structure could predict variability in cerebellar functions. Across all our tasks, we did not find such association, independently of whether we defined cerebellar regions based on an anatomical atlas or a functional one.

The use of 23 as the cut-off for MOCA scores is rather low. What was the justification for this within the literature? The authors note wanting to ensure task instructions and those with symptoms of potential MCI, but often 26 is used as a minimum score (with 25 and below being potential MCI).

In the methods, we refer to the study of Carson et al. (2018) that recommends a cutoff score of 23/30 instead of 26/30 as it shows overall better diagnostic accuracy. We selected this cutoff to emphasize that our sample was not restricted to only the highest‑performing older adults. However, we agree that this is not sufficiently explained in the text, so we briefly clarified this (p.5):

“We assessed cognitive functioning in both older and older‑old participants using the Montreal Cognitive Assessment (MoCA). A minimum score of 23 out of 30 was required for inclusion, following the recommendation by Carson et al. (2018), who demonstrated that this reduced cutoff yields fewer false positives and provides better overall diagnostic accuracy than the original 26/30 threshold. We adopted this criterion to ensure that our sample was not limited to only the highest‑performing older adults.”

The authors note that the timing of the visits was adapted based on participant availability. It would be helpful to report the mean length of time between sessions, as well as the range.

We added this to the method section (p.6):

“There was no fixed interval between the two behavioral sessions. Ideally, both were scheduled within one week, but in practice, the timing was adapted to participants’ availability. Across all participants, this resulted in a mean inter-session interval of 7.40 days (± 9.03; range = 0-63 days). The average interval between the behavioral sessions and the MRI scanning was 6.86 days (± 8.90; range = 0-83 days).”

The authors have anatomically defined cerebellar parcellations but have looked solely at total volume measures. What is the rationale for this? If there are differential impacts on cerebellar volume with age (Han et al., 2022; Bernard & Seidler, 2013), there may also be positive associations with behavior in regions that are less negatively impacted by volume. This would be consistent with the idea of reserve. One interesting set of correlations that could be considered is with respect to anterior lobules (I-IV and V) relative to the secondary motor representation in VIIIa and VIIIb, such that the latter may show a more robust association with behavior in the positive direction if volume in these regions is less impacted by aging.

As mentioned in response to one comment from the other reviewer, we investigated this question in our latest preprint (https://doi.org/10.64898/2026.02.13.705695). In this analysis, we did not find any relation between cerebellar outcomes and anatomical or functional cerebellar regions.

We consider this to be beyond the scope of the present paper, which focuses on the behavioral performances. The total cerebellar volume was added to show that the subject sample we used did actually exhibit atrophy in the cerebellum, but the purpose of the paper was not to focus on the link between structure and function.

With respect to timing, I recognize that the clock variance is insignificant based on p=.06. However, this is a relatively "close" result. I am very much of the mindset that things are significant or not. Inclusion of Bayesian analyses helps this, but I don't find this particularly convincing. The larger sample of individuals over age 80 is certainly a strength, and I'm not especially concerned about power. But I do wonder about overinterpretation. I would also emphasize the large degree of variability here in the oldest sample. This raises questions about associations with cerebellar metrics. This argument for relative preservation/reserve may be strengthened by looking at individual differences in structure relative to behavior. That is, in areas of the cerebellum where structure is less impacted by aging (as this is not entirely uniform) does this volume predict better behavior in this sample?

As noted earlier, the relationship between structure and function is examined in our other paper (https://doi.org/10.64898/2026.02.13.705695). Unfortunately, we were unable to include the 80+ group in that analysis because MRI data was available for only 20 older‑old participants and correlations/regression with 20 people are vastly underpowered.

We also want to point out that the almost significant difference highlighted by the reviewer between age groups actually goes in the direction of the older participants performing better than the young participants.

The note about the amount of variance in the older-old participants is fair, though.

The comparison with the Cam-CAN data set seems to be largely qualitative. Why did the authors not make a direct comparison to determine relative similarity in their sample compared to Cam-CAN? This would be a bit more compelling, though I suspect the differences are not statistically reliable (they note the oldest-old in the Leuven sample have a slightly larger volume). I do realize there are sample size differences, but a matched random sub-sample could also be created out of Cam-CAN. Why did they not compute the quadratic model in the Leuven sample as well?

A quadratic model was not considered very meaningful in the Leuven sample because age was not measured as a continuous variable but categorized into three discrete age groups (which provides more power to look at age-related differences). Our goal was not to determine whether absolute cerebellar volumes matched across datasets, for example, by creating comparable age groups in the Cam‑CAN dataset, but rather to assess whether the pattern of age‑related effects in our sample aligned with those seen in a larger dataset. In our opinion, the current approach sufficiently demonstrates that the age‑related trends we observe are consistent with those reported in Cam‑CAN.

The analysis of relative cerebellar gray and white matter is quite interesting. However, what about regional patterns to this? It would be particularly interesting to know if some regions are more or less impacted or preserved relative to the cortex. The data are seemingly available based on the processing approach (at least for gray matter). Was a similar analysis also computed in Cam-CAN? Replicating this in an independent sample would also be of interest.

We agree with the reviewer that this is indeed interesting for further analyses on this dataset. However, it falls beyond the scope of the present paper. Our preprint (https://doi.org/10.64898/2026.02.13.705695) looks at regional patterns for the cerebellum. Other papers have compared age-related decline in different cortical and subcortical regions as discussed on p.35 of our discussion:

“Given that the cerebellum exhibited a relatively less pronounced structural decline compared to other brain regions as shown here and in another previous study (Taki et al., 2011), it seems more plausible that the cerebellum might compensate for deficits caused by structural changes in other areas rather than vice-versa. Age-related gray and white matter degeneration is usually faster in frontotemporal regions and subcortical regions, including the hippocampus, amygdala and thalamus than in the cerebellum (Fjell et al., 2013; Giorgio et al., 2010; Neufeld et al., 2022). Although this does not directly indicate functional implications, it suggests that cortical regions are less likely to compensate for cerebellar loss when they exhibit more severe degeneration.”

The authors argue for cerebellar reserve and present compelling behavioral data in support of this with their many tasks. In instances where they look at largely cerebellar-mediated measures, they demonstrate that older adults and the >80 year old group show relatively intact behavior, even those in the group for total cerebellar gray matter volume (and white matter) is significantly smaller than in young adults. As noted, the behavioral data are very compelling, and as an individual who looks at aging populations in their research, seeing areas and domains of preservation is always interesting and useful. This pattern certainly may be consistent with cerebellar reserve. However, it would be more compelling if the authors also looked at these behaviors with respect to cerebellar volume. That is, there is still a great deal of variability in behavior in the older and >80 samples (though also in the young adults) that may still be associated with cerebellar volume. Poorer performance may be present in those with smaller volumes. This would also be somewhat consistent with the notion that these tasks are those that are derived from work in cerebellar degeneration samples. Associations between behavior and cerebellar measures would speak to this. If there are no associations with volume, this would be particularly interesting and compelling in the context of reserve. Alternatively, if there are differential impacts on cerebellar volume with age (Han et al., 2022; Bernard & Seidler, 2013), there may also be positive associations with behavior in regions that are less negatively impacted by volume. This would be consistent with the idea of reserve. One interesting set of correlations that could be considered is with respect to anterior lobules (I-IV and V) relative to the secondary motor representation in VIIIa and VIIIb, such that the latter may show a more robust association with behavior in the positive direction if volume in these regions is less impacted by aging. Not all individuals completed the scan (due to safety and comfort considerations), which would limit statistical power potentially, but this could be conducted in the subset of individuals that have both sets of data.

This point overlaps with the issues raised by the other reviewer in comments 1 and 2, which highlights the importance of this point. Yet, we decided to address this analysis in a separate paper. In the current manuscript, our primary focus was on the behavioral aspects, as these are already quite extensive on their own. In our subsequent work (https://doi.org/10.64898/2026.02.13.705695), we conducted an in-depth investigation into the relationship between cerebellar-specific measures and cerebellar structure across distinct cerebellar regions (including anatomical regions and functionally defined regions according to the atlas of Nettekoven et al., 2024). We found that aging does not affect the cerebellum uniformly, but that some anatomical regions exhibit stronger age effects. For the functionally defined regions the age effects were uniform though. There was no relation between behavioral cerebellar-specific measures and anatomical or functional cerebellar regions.

Some of the assertions the authors make in the discussion about the cerebellum have less pronounced structural decline relative to other brain regions would benefit from being tempered. They used relative measures here, and this is certainly interesting. But, how do other regions stack up? What would the hippocampus look like if such a measure were used? And as noted, does this pattern replicate in the CAM-CAN sample? Further, the authors cite Jernigan et al. (2001) in arguing that cerebellar changes are smaller than those in other brain regions, when in looking at their tables, in fact, the gray matter reductions of the cerebellum are comparable to those of the prefrontal cortex and second only to those of the hippocampus.

We agree with the reviewer that this is an interesting question but this question needs to be addressed in a separate paper. We also remove the citation to the Jernigan paper.

eLife Assessment

This valuable article provides a convincing and very detailed model of the process regulating the assembly of the spore coat in the model spore-forming bacterium Bacillus subtilis. It focuses on SafA, a morphogenetic coat protein involved in the assembly of the spore coat inner layer, deciphering the contributions of disulfide bond formation and crosslinking reactions catalyzed by a transglutaminase. The process had been studied with a combination of genetics and microscopy, but this is the first complete assessment incorporating detailed biochemical approaches.

Reviewer #1 (Public review):

This is an important article, which represents the culmination of 25 years of research on the spore coat protein, SafA. Reading this paper is not necessarily easy because it requires time, patience, and attention to detail, but it is truly rewarding. The attentive reader will certainly appreciate the description of a biochemical tour de force, providing convincing experimental evidence for every aspect of a step-by-step inner coat assembly model. It was previously known that SafA was a coat morphogenetic protein responsible for the assembly of the inner layer of the spore coat in Bacillus subtilis, and SafA was already viewed as a hub that directly or indirectly recruited several dozens of coat proteins to the spore envelope. It was also known that there were isoforms of SafA (the most important being the C30 form), and SafA was a substrate of Tgl, a transglutaminase involved in crosslinking some of the coat proteins, especially those found in the inner coat. Several studies have combined genetics and various types of microscopy approaches, including fluorescence microscopy, to decipher the mechanism of coat assembly, but the current study brings top-notch biochemistry into the picture and, therefore, is able to go much further into the molecular characterization of this important mechanism. It should be noted that spore coat assembly is a notoriously difficult process to study biochemically. It was also suspected to be a complex mechanism, because coat assembly is a protracted process involving at least 80 different proteins, whose production is controlled both temporally and spatially, but the current paper manages to connect specific chemical reactions to well-known stages of spore formation. The authors did so by generating several constructs with specific substitutions of Cys and Lys residues, interfering with the completion of disulfide bond formation and crosslinking events, thus determining the order of events and the structural consequences when one of these steps is impaired. Importantly, their conclusions are consistent with previous work. In the updated model, self-assembly of SafA is the first step, promoted by disulfide bond formation between C30 complexes. This is followed by recruitment of inner coat proteins and, finally, transglutamination to stabilize the scaffold structure (referred to as a "spotwelding activity".

The work is extremely thorough. I did not identify any weaknesses and could not think of any experiment that would have been omitted.

Reviewer #2 (Public review):

Summary:

The authors assemble a variety of information from biochemical experiments on oligomeric and higher-order assembly of the spore coat protein SafA, which functions as a hub in spore coat development. Together, the data indicate a robust process of assembly, guided initially by an organized process of disulfide bond formation and ultimately leading to cross-linking by the enzyme Tgl. Interestingly, neither process is strictly necessary for the formation of highly assembled oligomeric forms of SafA, but instead, these processes are mutually supportive in creating a strong, intercrosslinked assembly. Given this lead-up, it is somewhat disappointing to find that the cross-linking defective SafA mutants do not exhibit any obvious defects in sporulation in vivo, and one is left with the conclusion that this stage of spore coat assembly is accomplished by multiple independent co-occurring activities. The information is sufficient to support a detailed model for SafA assembly, which is significant in that it helps to explain the process of building a critically important hub-scaffold for spore coat development.

Strengths:

The main body of experiments supports a detailed model for the assembly of SafA monomers into spore coat superstructures. This is interesting because it shows how a protein can be used as both a scaffold and a hub in contributing to the assembly of a super-resilient biological material.

Weaknesses:

(1) The weak sporulation phenotype of the crosslinking mutants diminishes the significance of the mechanism that is described.

(2) The narrative flow of the originally submitted manuscript could be improved by removing some unnecessary and confusing figures on peripheral subjects and rearranging some of the latter figures to arrive at a conclusion that focuses more on SafA assembly.

(3) The original manuscript appears to have a labeling error in the supplementary figures, but a correctly labeled version of the figures would not support one of the manuscript's claims.

Reviewer #3 (Public review):

The manuscript by Amara et al. provides novel mechanistic insight into how SafA, a spore coat morphogenetic protein, self-assembles and is later crosslinked by the Tgl transglutaminase during spore coat assembly. Through rigorous, carefully executed biochemical analyses of SafA's oligomerization and crosslinking states, the authors demonstrate that SafA forms dimers that promote disulfide bond formation between two cysteine pairs found in its C30 region; this disulfide bond-mediated crosslinking promotes, but is not essential for, Tgl-mediated crosslinking of lysine residues within SafA. Specifically, one pair in its N-terminal C30 region promotes the formation of higher-order oligomers, while the second pair in its C-terminus C30 region promotes its ability to form a tetramer. Mutation of both cysteine pairs prevents higher-order SafA structures and reduces the efficiency of Tgl-mediated crosslinking via lysines in close proximity to the cysteines. They further show that disulfide bond formation promotes, but is not essential for, SafA to self-assemble into structures ~1200 kDa via SAXS analyses and kinetic analyses of Tgl-mediated crosslinking of purified SafA in vitro.

Major Comments:

(1) While the authors' detailed and thorough biochemical analyses advance our understanding of how SafA forms higher-order structures in the presence and absence of Tgl, they could broaden the significance of their findings with additional functional analyses of their mutants in B. subtilis. Figure 8 shows that loss of Tgl and SafA disulfide bond formation renders SafA more extractable (presumably leading to a less resilient spore coat), and FRAP analyses indicate that SafA in ∆tgl sporulating cells is more mobile than in its lysine crosslinked form. Some ideas that the authors could test to try and identify additional functions for the Cys and Lys residues in SafA:<br /> - Analyze the Cys mutants in the FRAP assay?<br /> - Does loss of SafA-mediated crosslinking via the Cys and/or Lys mutations affect its localization to the forespore or the recruitment of its client proteins like GerQ?<br /> - Have the authors tested higher concentrations of lysozyme? Or chloroform?

(2) While the authors show in supplementary data that the safA point mutants they generated do not affect spore germination in the single condition tested, the Rudner group previously showed that SafA plays a role in spore germination by affecting CwlJ localization to the forespore. Perhaps the authors might see a more significant phenotype on spore germination with their Cys and Lys mutants if they tried to complement a ∆safA∆sleB double mutant with mutant safA constructs? For the germination assays, it was unclear to me whether the authors used heat activation prior to inducing spore germination.

(3) Have the authors looked at whether the Cys or Lys mutations affect the sensitivity of spores to oxidative insults, especially since the Cys residues might temper the effects of oxidizing agents?

(4) Did the authors test the effect of single Cys mutations on disulfide bond formation, since intermolecular disulfide bond formation might still be possible even if one of the Cys residues has been changed?

(5) Finally, I was unsure how many times each experiment was replicated and how many experiments had been conducted in total.

eLife Assessment

This valuable study aims to determine mechanisms underlying breast cancer initiation and tumour progression. The manuscript includes a solid set of transcriptomic and proteomic datasets from tumour samples and examines mitochondrial function within the tumours. While the underlying mechanisms linking expression changes to functional effects remain speculative. This paper provides a resource for researchers working on breast cancer and/or HER2-driven bioenergetics changes.

Reviewer #1 (Public review):

Summary:

In this manuscript, Frangos at al. used a transcriptomic and proteomic approach to characterise changes in HER2-driven mammary tumours compared to healthy mammary tissue in mice. They observed that mitochondrial genes, including OXPHOS regulators, were among the most down-regulated genes and proteins in their datasets. Surprisingly, these were associated with higher mitochondrial respiration, in response to a variety of carbon sources. In addition, there seems to be a reduction in mitochondrial fusion and an increase in fission in tumour tissues compared to healthy tissues.

Strengths:

The data are clearly presented and described.

The author reported very similar trends in proteomic and transcriptomic data. Such approaches are essential to have a better understanding of the changes in cancer cell metabolism associated with tumorigenesis.

The authors provided a direct link between HER2 inhibition and OXPHOS, strengthening the mechanistic aspect of the work.

Weaknesses:

The manuscript would have benefited from more ex-vivo approaches to further dissect mechanistic links and resolve the contradiction of elevated respiration with reduced expression of most associated proteins (but these points are clearly articulated in the discussion).

The results presented support the authors' conclusions, and limitations are addressed in the discussion. This work will likely impact the progression of the field, and the provided data will benefit the scientific community.

Comments on revisions:

The authors addressed all my concerns.

Reviewer #2 (Public review):

Frangos et al present a set of studies aiming to determine mechanisms underlying initiation and tumour progression. Overall, this work provides some useful datasets, further establishing mitochondrial dysfunction during the cellular transformation process.

A key strength is the coordinated analysis of transcriptomics and proteomics from tumour samples derived from a Neu-dependent mouse model for breast cancer. This analysis provides rigorous datasets that show robust patterns, including down-regulation across many components of mitochondrial OXPHOS that were generally consistent at both the mRNA and protein level. Parallel analysis of corresponding tumour samples thereby clearly shows the opposite trend of increased mitochondrial function, which is unexpected. As such, this work further establishes altered mitochondrial phenotypes in tumour contexts and further illustrates that mitochondrial function is not necessarily always tightly correlated with mitochondrial gene expression patterns.

Several key weaknesses remain. It remains unclear how increased mitochondrial function is being sustained despite wide decreases in mRNA and protein levels of OXPHOS components. In terms of mechanism, the study confirmed that pharmacologic EGFR inhibition decreases OXPHOS in a EGFR-dependent breast cancer line. However, it remains unclear if the cell culture system recapitulates other key observations of the tumour model (namely decreased expression with increased function).

Therefore, the mechanistic basis of increased mitochondrial function in light of decreased mitochondrial content remains speculative, as does the role of these changes for tumour initiation or progression.

Comments on revisions:

We agree with the overall findings of the study and appreciate that the claims in text and title have been appropriately toned down.

As additional suggestions eg for presentation, many of the graphics/labels are still too small to be useful. It would be interesting to see if this cell line is similar to the tumours in terms of all the phenotypes. The lapatinib experiment was good. I wonder how quick this drug affects the mitochondria. Also it would be interesting to see if these cells have higher OXPHOS than other non-transformed breast epithelial cells.

The WB on oxphos components is good with ab110413 but this looks like many subunits are detected so this should be made clear.

Author response:

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

Reviewer #1 (Public review):

Comments on revisions: The authors addressed all my concerns.

We thank you for the positive review and feedback throughout the review process.

Reviewer #2 (Public review):

Comments on revisions: We agree with the overall findings of the study and appreciate that the claims in text and title have been appropriately toned down. As additional suggestions e.g. for presentation, many of the graphics/labels are still too small to be useful. It would be interesting to see if this cell line is similar to the tumours in terms of all the phenotypes. The lapatinib experiment was good. I wonder how quick this drug affects the mitochondria. Also it would be interesting to see if these cells have higher OXPHOS than other non-transformed breast epithelial cells. The WB on oxphos components is good with ab110413 but this looks like many subunits are detected so this should be made clear.

Thank you for these suggestions.

We have clarified in the Methods section (lines 475–476) the specific OXPHOS subunits detected using the Ab110413 antibody cocktail.

With respect to lapatinib, prior work has shown that lapatinib can alter the phosphoproteome within minutes to hours (PMID:22964224). In our experiments, however, NF639 cells were exposed to lapatinib for 24 hours - a timeframe in which transcriptional and translational remodeling are also expected to occur. Therefore, we cannot distinguish whether the observed suppression of OXPHOS reflects acute signaling effects or downstream changes in gene and protein abundance. Importantly, the purpose of this experiment was proof-of-principle: to determine whether HER2 signaling contributes to respiratory competency in a cell line derived from the same transgenic model as the intact tumor slices used in this study. Thus, while defining the precise kinetics of inhibition or comparing to benign/non-transformed cells would be interesting, these were not the primary objectives of the added experiments.

We have increased figure label sizes across all main figures.

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Frangos et al. used a transcriptomic and proteomic approach to characterise changes in HER2-driven mammary tumours compared to healthy mammary tissue in mice. They observed that mitochondrial genes, including OXPHOS regulators, were among the most down-regulated genes and proteins in their datasets. Surprisingly, these were associated with higher mitochondrial respiration, in response to a variety of carbon sources. In addition, there seems to be a reduction in mitochondrial fusion and an increase in fission in tumours compared to healthy tissues.

Strengths:

The data are clearly presented and described.

The author reported very similar trends in proteomic and transcriptomic data. Such approaches are essential to have a better understanding of the changes in cancer cell metabolism associated with tumourigenesis.

Weaknesses:

(1) This study, despite being a useful resource (assuming all the data will be publicly available and not only upon request) is mainly descriptive and correlative and lacks mechanistic links.

We appreciate this point. While the primary goal of our study was to assess mitochondrial adaptations with HER2-driven tumorigenesis, we agree strengthening the mechanistic interpretation would improve the impact of the data. To address this, we have provided experiments demonstrating HER2 inhibition in NF639 cells with lapatinib supresses respiratory capacity, directly supporting the interpretation that HER2 activity regulates respiratory function (Figure 10). We have expanded the discussion appropriately (lines 378-394). Both raw RNA-seq and proteomic data were deposited through GEO and the PRIDE repositories (accession numbers included in Data Availability Statement).

(2) It would be important to determine the cellular composition of the tumour and healthy tissue used. Do the changes described here apply to cancer cells only or do other cell types contribute to this?

We thank the reviewer for this suggestion; we have added experiments that have directly addressed this concern.

Cell type composition analysis by immunofluorescence was added (Figure 6) where we quantified epithelial, mesenchymal, endothelial, immune and stromal populations in our benign mammary tissue and tumor samples. We found no major shift in the dominant cell types that would confound transcriptomic data in whole tissues.

We integrated immunofluorescence data with a publicly available scRNA-seq dataset from human breast tumors which allowed us to estimate cell-type-specific expression of OXPHOS genes in our own samples. Despite the possibility of species differences, this is the only dataset of its kind, and we used this to generate an estimate of cell type weighted OXPHOS mRNA expression (Figure 6). This revealed that epithelial cells are likely the dominant contributors to OXPHOS gene expression for CIIV. All calculations are delineated in the Methods section.

(3) Are the changes in metabolic gene expression a consequence of HER2 signalling activation? Ex-vivo experiments could be performed to perturb this pathway and determine cause-effects.

Thank you for this suggestion – we have included an experiment directly testing this concept. We assessed mitochondrial respiration in NF639 HER2-driven mammary tumor epithelial cells in the presence or absence of the well-described dual tyrosine kinase inhibitor lapatinib. Lapatinib reduced basal, CI-linked and CI+II linked respiration without compromising mitochondrial integrity or coupling, demonstrating that HER2 activation regulates respiration in our model. This data is presented in Figure 10, and a new section has been added to the discussion describing the implications of this finding in the context of the current literature (lines 378-394).

(4) The data of fission/fusion seem quite preliminary and the gene/protein expression changes are not so clear cut to be a convincing explanation that this is the main reason for the increased mitochondria respiration in tumours.

We agree mitochondrial morphology and dynamics alone cannot fully account for the observed respiratory phenotype – this was emphasized in the discussion but has since been further clarified (lines 365-377). We retained the TEM and dynamics gene/protein data because they do support morphological differences consistent with enhanced fission. However, we have revised the tone of our interpretation to more explicitly acknowledge that these findings are correlative, and the updated discussion now emphasizes that the increased respiratory capacity in tumors is likely driven by multiple converging mechanisms.

Reviewer #2 (Public review):

Frangos et al present a set of studies aiming to determine mechanisms underlying initiation and tumour progression. Overall, this work provides some useful insights into the involvement of mitochondrial dysfunction during the cellular transformation process. This body of work could be improved in several possible directions to establish more mechanistic connections.

(5) The interesting point of the paper: the contrast between suppressed ETC components and activated OXPHOS function is perplexing and should be resolved. It is still unclear if activated mitochondrial function triggers gene down-regulation vs compensatory functional changes (as the title suggests). Have the authors considered reversing the HER2-derived signals e.g. with PI3K-AKT-MTOR or ERK inhibitors to potentially separate the expression vs. functional phenotypes? The root of the OXPHOS component down-regulation should also be traced further, e.g. by probing into levels of core mitochondrial biogenesis factors. Are transcript levels of factors encoded by mtDNA also decreased?

We appreciate this insight and agree that the discordance between mitochondrial content and function is fascinating and have addressed the concerns above in the following manner:

- We have altered the title – we agree we cannot definitively say that the enhanced respiratory capacity observed is compensatory.

- We have added experiments in NF639 cells in the presence of lapatinib, a tyrosine kinase inhibitor to interrogate whether HER2 is necessary for our functional outcome of interest – the enhanced respiratory capacity in the tumors. Lapatinib significantly suppressed respiration (Figure 10) demonstrating HER2 signaling directly regulates mitochondrial respiration.

- We have expanded the discussion to provide further comment on potential explanations for increased respiratory function and low mitochondrial content.

(6) The second interesting aspect of this study is the implication of mitochondrial activation in tumours, despite the downregulation of expression signatures, suggestive of a positive role for mitochondria in this tumour model. To address if this is correlative or causal, have the authors considered testing an OXPHOS inhibitor for suppression of tumorigenesis?

Previous studies have eloquently highlighted that directly or indirectly inhibiting mitochondria can supress growth in HER2-driven breast cancer (PMID:31690671) or alternatively, amplification of mt-HER2 enhances tumorigenesis (PMID: 38291340). In many solid tumors, this is the concept of preclinical and clinical studies using IACS-010759 or similar inhibitors of OXPHOS which do suppress growth but have significant off target effects in healthy tissues (PMID: 36658425, 3580228We have expanded the discussion to ensure the reader is aware of these previous contributions and highlighted the importance of future work delineating the role of enhanced respiratory function in HER2-driven mammary cancer (lines 378-394).

(7) A number of issues concerning animal/ tumour variability and further pathway dissection could be explored with in vitro approaches. Have the authors considered deriving tumourderived cell cultures, which could enable further confirmations, mechanistic drug studies and additional imaging approaches? Culture systems would allow alternative assessment of mitochondrial function such as Seahorse or flow cytometry (mitochondrial potential and ROS levels).

We thank the reviewer for this suggestion – we have addressed this in part by using the NF639 HER2driven tumor epithelial line which demonstrated that HER2 regulates our observed respiratory response. Unfortunately, the addition of tumor derived cell cultures was not feasible or within the scope of our study. Animal and tumor variability has been clarified in the Methods section (lines 424-429). Mitochondrial respiration experiments were performed in paired tissue (benign and tumor from same mouse). Transcriptomic, proteomic and histological analyses were performed on tumors and benign samples from different mice due to tissue limitations.

(8) The study could be greatly improved with further confirmatory studies, eg immunoblotting for mitochondrial components with parallel blots for phospho-signalling in the same samples. It would be interesting if trends could be maintained in tumour-derived cell cultures. It is notable that OXPHOS protein/transcript changes are more consistent (Figure 5, Supplementary Figure 4) than mitochondrial dynamics /mitophagy factors (Figure 8). Core regulatory factors in these pathways should be confirmed by conventional immunoblotting.

We thank the reviewer for this thoughtful comment. While we agree that additional confirmatory studies can be valuable, due to tissue quantity constraints and the number of assays required for our multi-omics analysis, extensive additional blots were not feasible. However, we had sufficient protein to provide select OXPHOS proteins to verify the proteomic data (now provided in S-Fig.4H). Furthermore, we have plotted the fold change of genes and proteins detected in both datasets and added this to Figure 4 (4A, B), further highlighting the consistency between our transcriptomic and proteomic findings. We believe that the highly consistent and concordant nature of our datasets collectively provides strong support for our central objective - determining whether mitochondrial content and respiratory function correlate in HER2-driven mammary tumors. The reproducibility of OXPHOS-related changes reinforces the robustness of our observations. We also appreciate the reviewer’s insight that OXPHOS alterations appear particularly consistent. In response, we have edited the discussion to further emphasize this point, especially in relation to the distinctive pattern observed for Complex V, which showed greater preservation relative to Complexes I–IV across several methods (lines 348-364). We comment on how this stoichiometric shift may contribute to intrinsic respiratory activation despite reduced mitochondrial content.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Further Minor points.

(9) It would be helpful to know further details regarding the source of the tumour samples, particularly for the proteomics (N=5) and transcriptomics (N=6) datasets, since the exact timepoint of tissue harvest and number of tumours/mouse varied, according to the methods section. Were all samples from the omics studies from different mice (ie 11 mice)? B4 and B6 seem like outliers in mitochondrial transcriptomes. Are these directly paired eg with T4 and T6? Are the side-by-side pairs of Ben and Tum samples for blots in Figure 1 and Supplementary Figure 1 from the same mouse.

This has been clarified in the Methods section (lines 424-429). Mitochondrial respiration experiments were performed in paired tissue (benign and tumor from same mouse). Transcriptomic, proteomic and histological analyses were performed on tumors and benign samples from different mice due to tissue limitations.

(10) Further references and details are needed to support the methodology of the mitochondrial function tests (eg. nutrients vs pairing with complexes). What was the time point of nutrient supplementation? It would seem that the lipid substrates should take longer to activate OXPHOS than pyruvate/malate or succinate. Is this the case? Is there speculation as to why succinate supplementation is much more active than pyruvate+malate? What is +MD in Figure 6? The rationale for pooling data for Figure 7A is unclear since the categories appear to overlap: (pyruvate, malate, ADP) vs. (palmitoyl-carnitine, malate, ADP).

Thank you for this comment. We have expanded the methods (lines 515-531) to provide additional detail on the mitochondrial respiration protocol. Briefly, permeabilized tissues were exposed to substrates delivered at supraphysiological concentrations in a sequential protocol lasting ~30–60 minutes. Under these conditions, mitochondrial respiration reflects the maximal capacity to utilize each substrate rather than the physiological time course of substrate mobilization or uptake that would occur in vivo with the influence of blood flow and transport/substrate availability limitations.

(11) Many of the figures were blurry (Figure 1F, 2B) or had labels that were too small to be effective (Figures 1G, H, 2D-G, 3E-G, 5E-I, 7C, 8B).

The font size of figure labels has been increased where possible and all figures have been exported to maximize resolution.

eLife Assessment

This important study addresses the contribution of pericytes to the organization and permeability control of the zebrafish blood-brain barrier (BBB). By analyzing pdgfrb mutant zebrafish that lack brain pericytes, the authors reveal that the resulting cerebrovascular network is abnormally patterned. Remarkably, however, the barrier retains its restrictive permeability during larval and juvenile stages. More pronounced vascular defects become evident in adults, where localized BBB leakage coincides with hemorrhages and aneurysm formation. Based on convincing and beautifully documented imaging data, the authors argue that, unlike what has been reported in rodent systems, pdgfrb-dependent pericytes are not essential for maintaining BBB integrity in the zebrafish brain.

Reviewer #1 (Public review):

Summary:

The study investigates the role of vascular mural cells, specifically pericytes and vascular smooth muscle cells (vSMCs), in maintaining blood-brain barrier (BBB) integrity and regulating vascular patterning. Analyzing zebrafish pdgfrb mutants that lack brain pericytes and vSMCs, the show that mural cell deficiency does not impair BBB establishment or maintenance during larval and early juvenile stages. However mural cells seem to be crucial for preventing vascular aneurysms and hemorrhage in adulthood as focal leakage, basement membrane disruption and increased caveolae formation are observed in adult zebrafish at aneurysm hotspots. The authors challenge the paradigm that mural cells are essential for BBB regulation in early development while highlighting their importance for long-term vascular stability.

Strengths:

Previous studies have established that the zebrafish BBB shares molecular and morphological homology with e.g. the mammalian BBB and therefore represents a suitable model. By examining mural cell roles across different life stages-from larval to adult zebrafish-the study provides an unprecedented comprehensive developmental analysis of brain vascular development and of how mural cells influence BBB integrity and vascular stability over time. The use of live imaging, whole-brain clearing, and electron microscopy offers high-resolution insights into cerebrovascular patterning, aneurysm development, and structural changes in endothelial cells and basement membranes. By analyzing "leakage hotspots" and their association with structural endothelial defects in adults the presented findings add novel insights into how mural cell loss may lead to vascular instability.

Reviewer #2 (Public review):

Summary:

The authors generated a zebrafish mutant of the pdgfrb gene. The presented analyses and data confirm previous studies demonstrating that Pdgfrb signaling is necessary for mural cell development in zebrafish. In addition, the data support previously published studies in zebrafish showing that mural cell deficiency leads to hemorrhages later in life. The authors presented quantified data on vessel density and branching, assessed tracer extravasation, and investigated the vasculature of adult mice using electron microscopy.

Strengths:

The strength of this article is that it provides independent confirmation of the important role of Pdgfrb signaling for the development of mural cells in the zebrafish brain. In addition, it confirms previous literature on zebrafish that provides evidence that, in the absence of pericytes/VSMC, hemorrhages appear (Wang et al, 2014, PMID: 24306108 and Ando et al 2021, PMID: 3431092)".

The Reviewing Editor has carefully reviewed the revised manuscript and is fully satisfied with the authors' revisions.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study investigates the role of vascular mural cells, specifically pericytes and vascular smooth muscle cells (vSMCs), in maintaining blood-brain barrier (BBB) integrity and regulating vascular patterning. Analyzing zebrafish pdgfrb mutants that lack brain pericytes and vSMCs, they show that mural cell deficiency does not impair BBB establishment or maintenance during larval and early juvenile stages. However, mural cells seem to be crucial for preventing vascular aneurysms and hemorrhage in adulthood as focal leakage, basement membrane disruption, and increased caveolae formation are observed in adult zebrafish at aneurysm hotspots. The authors challenge the paradigm that mural cells are essential for BBB regulation in early development while highlighting their importance for long-term vascular stability.

Strengths:

Previous studies have established that the zebrafish BBB shares molecular and morphological homology with e.g. the mammalian BBB and therefore represents a suitable model. By examining mural cell roles across different life stages - from larval to adult zebrafish - the study provides an unprecedented comprehensive developmental analysis of brain vascular development and of how mural cells influence BBB integrity and vascular stability over time. The use of live imaging, whole-brain clearing, and electron microscopy offers high-resolution insights into cerebrovascular patterning, aneurysm development, and structural changes in endothelial cells and basement membranes. By analyzing "leakage hotspots" and their association with structural endothelial defects in adults the presented findings add novel insights into how mural cell loss may lead to vascular instability.

Weaknesses:

The study uses quantitative tracer assays with multiple molecular weight dyes to evaluate blood-brain barrier (BBB) permeability. The study normalizes the intensity of tracer signals (e.g., 10 kDa, 70 kDa dextrans) in the brain parenchyma to the vascular signal of a 2000 kDa dextran tracer (assumed to remain within vessels). Intensity normalization is used to control for variations in tracer injection efficiency or vascular density. This method doesn't directly assess the absolute amount of tracer present in the parenchyma, potentially underestimating leakage severity. As the lack of BBB impairment is a "negative" finding, more rigorous controls or other methods might be needed to corroborate it.

In response to these and comments from other reviewers, we have now performed further carefully controlled analysis to test leakage of tracers using molecular weights ranging from 1 to 2000 kDa. We have performed additional normalisation approaches (new data in Fig. 2a–d) imaging tracer extravasation together with vascular reporters (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916) and used this transgenic reporter for normalisation (as suggested by Reviewer #2). The results of these experiments all supported our initial conclusions (revised Extended Data Fig. 3a–d) further validating the reliability of our method. Furthermore, as suggested by the reviewer analysis of the raw tracer intensity amounts in the parenchyma were also performed with no normalization at all (see Author response image 1). This also supports our conclusion that the BBB is intact in young animals. Finally, we now use our methods to demonstrate that we can detect an immature leaky BBB at 3 dpf and a mature functional BBB at 7 dpf (Fig. 2e-f), a suitable positive control to show that our methods and analyses are reliable.

Author response image 1.

Raw intensity values from the parenchyma confirm findings in Figure 2 and Extended Data Figure 3.a–d, Raw mean fluorescence intensity values of extravasated tracers in the midbrain.(a–b) show unnormalized values corresponding to Extended Data Fig. 3a–d, and (c–d) show unnormalized values corresponding to Fig. 1a–d. Unpaired t-tests for 70 and 10 kDa at 14 dpf in (a–b), for 10 kD at 7 dpf, and for 70 kDa at 14 dpf in (c–d). Mann-Whitney tests for 70 and 10 kDa at 7 dpf in (a–b), for 70 kDa at 7 dpf, and for 10 kDa at 14 dpf (c–d), due to non-normal distribution. These data were all generated in genotype blind assays, display variance in signal that is generated between embryos due to injection differences and show no difference between the genotypes analysed in BBB integrity. Comparison of this to normalised data using 2000 kDa tracer or kdrl expression in endothelial cells (Fig. 2 and Extended Data Fig. 3) confirms that normalisation improves the analysis, effectively controlling for embryo-to-embryo differences in delivery of tracer and imaging.

Reviewer #2 (Public review):

Summary:

The authors generated a zebrafish mutant of the pdgfrb gene. The presented analyses and data confirm previous studies demonstrating that Pdgfrb signaling is necessary for mural cell development in zebrafish. In addition, the data support previously published studies in zebrafish showing that mural cell deficiency leads to hemorrhages later in life. The authors presented quantified data on vessel density and branching, assessed tracer extravasation, and investigated the vasculature of adult mice using electron microscopy.

Strengths:

The strength of this article is that it provides independent confirmation of the important role of Pdgfrb signaling for the development of mural cells in the zebrafish brain. In addition, it confirms previous literature on zebrafish that provides evidence that, in the absence of pericytes/VSMC, hemorrhages appear (Wang et al, 2014, PMID: 24306108 and Ando et al 2021, PMID: 3431092). The study by Ando et al, 2021 did not report experiments assessing BBB leakage in pdgfrb mutants but in the review article by Ando et al (PMID: 34685412) it is stated that "indicating that endothelial cells can produce basic barrier integrity without pericytes in zebrafish."

We thank the reviewer for their comments and pointing out literature that we had not cited (this has been corrected in our revised manuscript).

As noted by other reviewers, our study goes beyond simply confirming previous literature. The quoted section by the reviewer from Ando et al 2021 regarding intact barrier integrity in pdgfrb mutants is a conclusion based on apparent lack of haemorrhages in pdgfrb mutants[1]. Our work shows haemorrhages in older animals and as such is in line with these previously published results, but it also extends previous work, for the first time reporting detailed functional analysis to assess BBB integrity. Our study uses definitive tracer assays (now including extensive revisions) to identify intact the BBB in pdgfrb mutants in live animals. This has not been previously described and is important because it offers a new perspective on the evolutionary conservation (or otherwise) of pericyte control of BBB function. Furthermore, our study investigates the nature of hotspot leakage and haemorrhages in more detail than in previous work.

Weaknesses:

(1) The authors should avoid using violin plots, which show distribution. Instead, they should replace all violin plots in the figures with graphs showing individual data points and standard deviation. For Figure 2f specifically, the standard deviation in the analyzed cohort should be shown.

This is a good point and we have replaced the violin plots with individual data points and shown all data as mean±SEM.

(2) The authors have not shown the reduced PDGFRB protein or the effect of mutation on mRNA level in their zebrafish mutant.

Our pdgfrb^uq30bh mutant allele introduces a mutation predicted to generate a truncated protein very similar to previously validated alleles (see detail in revised Extended Data Fig. 1a and methods). Our pdgfrb^uq30bh mutant also phenocopies previous pdgfrb mutants (sa16389 and um148 alleles)[2,3], displaying mural cell loss with multiple markers (Fig. 1a, new data in Extended Data Fig. 1b–c, Fig. 3b–c; Extended Data Fig. 4c–d) and the same typical morphological defects and survival rates (new data in Extended Data Fig. 1d–f). Thus our mutant phenocopy gives confidence it is most likely a null allele, in line with previous papers studying presumed null alleles[1].

We believe this provides sufficient confidence in this allele of pdgfrb. Moreover, considering that our manuscript focusses on loss of mural cells and we show definitively that this mutant has robust loss of mural cells in the brain, our mutant is suitable for this study.

(3) Statistical data analysis: Did the authors perform analyses to investigate whether the data has a normal distribution (e.g., Figures 1d, e)?

We thank the reviewer for raising this and apologise for this oversight. All data have now been assessed for normality using Shapiro-Wilk test and further statistical analyses have been performed accordingly. The specific quantifications referred to by the reviewer in Extended Data Fig. 3a–d (previously Fig. 1d-e), have normal distribution except for quantification measuring 70 kDa extravasation at 7 dpf, therefore Mann-Whitney test has been used for this comparison. Further information can be found in figure legends and methods.

(4) Analysis of tracer extravasation. The use of 2000 kDa dextran intensity as an internal reference is problematic because the authors have not provided data demonstrating that the 2000 kDa dextran signal remains consistent across the entire vasculature. The authors have not provided data demonstrating that the 2000 kDa dextran signal in vessels exhibits acceptable variance across the vasculature to serve as a reliable internal reference. The variability of this signal within a single animal remains unknown. The presented data do not address this aspect.

We thank the reviewer for their comment and agree that analysis was needed for showing 2000 kDa dextran as a reliable normalization signal.

We now show the data in the following Figures that demonstrate the consistency of signal throughout the vasculature using this 2000-kDa tracer: Extended Data Fig. 2b, Extended Data Fig. 3a and c, Extended Data Fig. 5a, Extended Data Fig. 6. In fact, we observe that this 2000 kDa tracer provides a very reliable marker of large and small calibre vessels in larval, juvenile and adult animals, even in fixed and cleared whole tissues and animals (e.g. Extended Data Fig. 2d-e, Extended Data Fig. 5 and 6).

Our further experiments and analysis support the use of this tracer as an ideal way to normalise for variation between animals and coupled with improved masking of vessels using transgenic labels (e.g. Extended Data Fig. 2b) we can quantify across whole vascular networks to reduce the concern about variation within individual animals. We also find 2000 kDa shows negligible leakage through the brain vessels Extended Data Fig. 2b–c (new data) at 2 hours post-injection (hpi) and provided images in Extended Data Fig. 6b–b′′ showing detectable signals even at 6 hpi. Finally, results generated with this approach, normalisation to transgenic markers or even raw parenchymal values of tracer intensity, generate the same conclusions. In addition, we point the reviewer to a recent pre-print that further validates this method from our team[4].

Overall, we find the use of this tracer an ideal way to normalise for differences in injection volumes between animals and we recommend the use of this method to other groups assessing BBB leakage in zebrafish.

Additionally, it's intriguing that the signal intensity in the parenchyma of the tested tracers presents a substantial range, varying by 20-30% in the analysed cohort (Figure 1g, Extended Figure 1e). Such large variability raises the question of its origin. Could it be a consequence of the normalization to 2000 kDa dextran intensity which differs between different fish? Or is it due to the differences in the parenchymal signal intensity while the baseline 2000 kDa intensity is stable? Or is the situation mixed?

This is a good point raised by the reviewer.

To address this, we have used the following approaches:

(1) We provide additional experiments and normalisation methods that support the utility of our tracer studies (new data in Fig 2a–f and Extended Data Fig. 2b–c), discussed in detail below.

(2) We provide graphs of the raw parenchymal distribution of tracer not normalised at all (also requested by reviewer 1). This is provided in Author response image 1 and further supports all our conclusions, showing that our normalisation methods generate meaningful data.

Overall, the range of parenchymal intensity that we see after tracer injection and live imaging shows variations introduced during microinjection. However, these ranges are in-line with previous publications using similar methods (see studies by O’Brown et al 2019 and 2023)[5,6], allow reliable statistical comparisons to be drawn between control and mutants and allow us to detect both immature and functional BBB states during zebrafish development (new data in Fig. 2e-f).

Of note, the variability we see is likely introduced during the injection process into tiny larval blood vessels and is the reason why we perform normalization of parenchymal tracers to a vascular dextran signal that doesn’t leak from brain vessels. In our studies, 2000-kDa dextran has been co-injected with the smaller size tracers, therefore any potential differences in injection volumes as well as imaging conditions (however consistent) should be reduced by this method.

An alternative and potentially more effective approach would be to cross the pdgfrb mutant line with a line where endothelial cells are genetically labeled to define vessels (e.g. the line kdrl used in acquiring data presented in Figure 2a). Non-injected controls could then be used as a baseline to assess tracer extravasation into the parenchyma.

We thank the reviewer for this suggestion.

In response, we have performed new tracer leakage experiments at 7 and 14 dpf in siblings and pdgfrb mutants and quantified parenchymal tracer extravasation by normalizing to vascular reporters (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916). The results were in-line with the previously presented and independent experiments and showed indistinguishable phenotypes between siblings and pdgfrb mutants (new data, Fig. 2a–d). We also used uninjected controls to assess baseline and saw consistent values approaching zero in these images and did not include this in the revised paper.

Furthermore, we have also used this approach in wild-type larvae at 3 dpf (immature BBB) and 7 dpf (functional BBB)[5]. We detected significantly higher parenchymal extravasation of 10 and 70 kDa tracers at 3 dpf compared to 7dpf, demonstrating that our method can detect leakage (new data, Fig. 2e–f).

We believe that both normalization approaches have advantages (as discussed above), therefore showing the same results with these two different approaches has further strengthened our findings.

How is the data presented in Figure 3e generated? How was the dextran intensity calculated? It looks like the authors have used the kdrl line to define vessels. Was the 2000 kDa still used as in previous figures? If not, please describe this in the Materials and Methods section.

We have moved this data to Fig. 4e (previously Fig. 3e).

Previously, we had plotted raw data due to the nature of the experiment being conducted on a vibratome sectioned tissue. The 2000 kDa tracer was not used. In response to this query and to be consistent with the new approach suggested by the reviewer, we have revised the quantification by normalizing the 10 kDa tracer extravasation to Tg(kdrl:Hsa.HRAS-mCherry)^s916) for this and the new experiments on juveniles (Fig. 5h–i). Please see the corresponding figure legends or revised methods (lines 464–472).

(5) The authors state that both controls and mutants show extravasation of 1 kDa NHS-ester into the parenchyma. However, the presented images do not illustrate this; it is not obvious from these images (Extended Data Figure 1c). Additionally, the presented quantification data (Extended Data Figure 1e) do not show that, at 7 dpf, the vasculature is permeable to this tracer. Note that the range of signal intensity of the 1 kDa NHS-ester is similar to the 70 kDa dextran (Figure 1g and Extended Figure 1e). Would one expect an increase in the ratio in case of extravasation, considering that the 2000 kDa dextran has the same intensity in all experiments? Please explain.

We thank the reviewer for raising this important point.

To clarify, we have never claimed that “2000-kDa dextran has the same intensity in all experiments”. On the contrary, vascular 2000 kDa normalization has been used to account for potential differences caused by injection, as stated in the submitted supplementary materials and now made more clear in the revision.

In response to this query, we conducted more detailed analysis on tracer extravasation patterns based on molecular weight (new data, Extended Data Fig 2b–c). This analysis showed that 1- and 10-kDa tracers have much higher extravasation rate compared to 70- and 2000-kDa tracers. Interestingly, we did not find a significant difference between 1 and 10 kDa extravasation. Therefore, in the revised manuscript we used only 10 kDa in further experiments and have removed 1 kDa from the figures.

To assess the tracers individually (new data in Extended Data Fig. 2c), parenchymal extravasation of individual tracers was normalised to their own vascular signal (eg. Mean intensity of 10 kDa in midbrain/mean intensity of 10 kDa in vasculature), to account for potential differences in injection volume. This provides a suitable method to assess leakage in wild-type animals and is now in line with how previous studies have analysed such tracer injections[5,6]. Please see revised figure legends and supplementary materials for details.

(6) The study would be strengthened by a more detailed temporal analysis of the phenotype. When do the aneurysms appear? Is there an additional loss of VSMC?

We thank the reviewer for this suggestion, and we have now performed staged imaging of the pdgfrb mutants and siblings between 7 and 21 dpf using TgBAC(acta2:EGFP)^uq17bh transgene (new data, Fig. 3b-c; Extended Data Fig. 4a–d). Consistent with previous results, acta2:EGFP-positive cells surrounding the middle mesencephalic central arteries (MMCtA) were missing in pdgfrb mutants. At 21 dpf, we have also observed a mild dilation of these vessels, likely the earliest changes to generate aneurysms (new data, Fig. 3c).

To extend the number of stages analysed in this study, we have also performed new tracer leakage experiments in juveniles (30 dpf) and found that aneurysms can be detected at this age when the 10 kDa tracer is used (new data in Fig. 5b–b′). Consistent with the adult stage phenotype, aneurysms were limited to the larger calibre vessels (arteries) in the brain. We have also observed hotspots, and upon quantification, we found fewer numbers in juveniles compared to adults, suggesting that severity of aneurysms and hotspots increase with age.

Taken together, our results show that the aneurysms in pdgfrb mutants start appearing at late larval/early juvenile stages (~21 dpf) with observable dilations. By 30 dpf, aneurysms accompanied by small numbers of hotspots are observed, which exhibits significantly increased numbers by adulthood. This also correlates with reduced development and survival rate of pdgfrb mutants after 30 dpf (new data, Extended Data Fig. 1d–e).

(7) The authors intended to analyze the BBB at later stages (line 128), but there is not a significant time difference between 2 months (Figure 2) and 3 months (Figure 3) considering that zebrafish live on average 3 years. Therefore, the selection of only two time-points, 2 and 3 months, to analyze BBB changes does not provide a comprehensive overview of temporal changes throughout the zebrafish's lifespan. How long do the pdgfb mutants live?

Respectfully, zebrafish transition from juvenile stages to adulthood between 2 and 3 months and there are many significant differences in the physiology of this organism at these two ages. At 2 months, zebrafish are still juveniles undergoing metamorphosis with rapid growth and ongoing skeletal and vascular development. By 3 months, they are sexually mature adults and have much more developed cranioskeletal and vascular systems. Having said that, we take the reviewers important point that further temporal resolution would improve the study.

We have performed new experiments in 1-month-old animals and provided comprehensive analysis of the vascular phenotypes occurring in pdgfrb mutants. These were very informative experiments analysing leakage using 10-kDa tracer injections and have significantly improved the study. We had previously provided experiments at 5-month-old adults as well (previously Fig. 4a–b and Extended Data Fig. 4a) and so now the study includes larval stages (7, 14 dpf), juveniles at 1 and 2 months and adults at 3 and 5 months. While the additional timepoints did not offer up any new conclusions, they significantly enhanced the body of work overall.

Of further note, we provided survival data up to 90 dpf where survival of the pdgfrb mutants is significantly reduced compared to siblings (Extended Data Fig. 1e). We believe this is associated with the severity of the aneurysms and haemorrhages which probably lead to lethality in these mutants.

(8) Why is there a difference in tracer permeability between 2 and 3 months (Figures 2 and 3)? Are hemorrhages not detected in 2-month-old zebrafish?

In response to this and other queries, we have added new additional experiments that provide more detailed temporal analysis on tracer accumulation (new data in Fig. 5b–c, Fig. 5f–g).

In short, we do not see obvious haemorrhages in 1- or 2-month fish at a gross level during dissections (not shown). We find that using 10-kDa tracer, we can detect small hotspots at aneurysms as early as 1 month, likely representing the earliest loss of integrity. We do not see obvious hotspots in 2-month-old animals when we use the 70-kDa tracer, this suggests to us that it is less sensitive for hotspot detection (in line with new Extended Data Fig. 2c). Finally, we find that the number of hotspots increases dramatically from Juvenile to Adult stages in our datasets, which we take as indicative of a progressive phenotype.

Overall, tracer size matters for detecting hotspots and they become more apparent in older animals - we have added a note in the main text to cover these points (lines 200–205)

(9) Figure 3: The capillary bed should be presented in magnified images as it is not clearly visible. Figure 3e shows that in the pdgfb mutant the dextran intensity is higher also in regions 6-10. How do the authors explain this?

We thank the reviewer for raising this important point.

Firstly, we now include enlarged views of the capillary beds for this experiment (Fig. 4d′) and new experiments mentioned below.

Secondly, in relation to why there is higher tracer in lateral locations and not just medial sites of haemorrhage, we believe that this is most likely due to the progressive spread of tracer from the medial hotspots. To test if this is likely, we performed additional experiments and tested tracer accumulation at 2 different timepoints in brains collected at 0.5 or 6 hpi (new data in Fig. 5f–g, Extended Data Fig. 6a–b′′). Tracer accumulation at 0.5 hpi was very minimal and was primarily limited to hotspots and nearby regions new data in (Fig. 5h), whereas a higher tracer accumulation in brains was observed across medial to lateral regions at 6 hpi (new data in Fig. 5i) in pdgfrb mutants. Comparing the data in Figure 4 (2 hpi) and new data in Figure 5i (6 hpi), the 10 kDa-tracer appears to have spread to more lateral locations given the increased time allowed post injection.

We cannot formally exclude the possibility that tracer leakage does occur slower through capillaries than at major hotspots, which might fit with the proposed model of slow leakage via increased EC transcytosis[7-9]. However, considering that we cannot detect increased tracer accumulation in pdgfrb mutants that lack aneurysms and haemorrhages at 7 and 14 dpf, such a scenario would require capillary transcytosis to be active at later juvenile and adult stages but not in larval and late larval animals. Thus, we believe the most plausible explanation is that aneurysm/haemorrhage associated leakage is the primary cause of the vascular integrity defects in zebrafish pdgfrb mutants.

We have added discussions addressing this in the revised manuscript (lines 220–230, 300–302).

(10) In general, the manuscript would benefit from a more detailed description of the performed experiments. How long did the tracer circulate in the experiments presented in Figures 2, 3, and 4?

We thank the reviewer for this suggestion and have now ensured that this is clearly described for in figure legends and methods (lines 391–395).

(11) How do the authors explain the poor signal of the 70 kDa dextran from the vasculature of 5-month-old zebrafish presented in Extended Data Figure 3?

We agree that the dextran signal was reduced compared to the other experiments in that Figure. This is likely due to sample preparation and clearing causing reduced fluorescence. Upon consideration of the presented data and the additional experiments using 10 kDa tracers providing further validations for our claims, we decided to remove this data from the paper.

(12) The study would benefit from a clear separation of the phenotypes caused by the loss of VSMC. The title eludes that also capillaries present hemorrhages which is not the case. How do vascular mural cells differ from mural cells? Are there any other mural cells?

We take the reviewers point and have now updated the title as "Mural cells protect the adult brain from haemorrhage but do not control the blood-brain barrier in developing zebrafish."

(13) I have a few comments about how the authors have interpreted the literature and why, in my opinion, they should revise their strong statements (e.g., the last sentence in the abstract).

Scientists have their own insights and interpretations of data. However, when citing published data, it should be clearly indicated whether the statement is a direct quote from the original publication or an interpretation. In the current manuscript, the authors have not correctly cited the data presented in the two published papers (references 5 and 6). These papers do not propose a model where pericytes suppress "adsorptive transcytosis" (lines 73-76). While increased transcytosis is observed in pericyte-deficient mice, the specific type of vesicular transport that is increased or induced remains unknown.

Similarly, lines 151-152 refer to references 5 and 6 and use the term "adsorptive transcytosis," but the authors of both papers did not use this term. Attributing this term to the original authors is inaccurate. Additionally, lines 152-153 do not accurately represent the findings of references 5 and 6. These papers do not state that there is an induction of "caveolae" in endothelial cells in pericyte-deficient mice. In the absence of pericytes, many vesicles can be observed in endothelial cells, but these vesicles are relatively large. It is more likely that there is some form of uncontrolled transcytosis, perhaps micropinocytosis. Please refer to the original papers accurately.

We thank the reviewer for these comments. We take the point and have rewritten the manuscript carefully to improve accuracy and avoid misrepresenting any previous claims made in specific papers.

Also, the authors have missed the fact that in mice, the extent of pericyte loss correlates with the extent of BBB leakage. To a certain extent, the remaining pericytes, can compensate for the loss by making longer processes and so ensure the full longitudinal coverage of the endothelium. This was shown in the initial work of Armulik et al (reference 5) and later in other studies.

We certainly did not miss this important point (as we are also working with these mouse models) and we now include reference to this in our expanded discussion. Of note, we do think it would be worthwhile assessing if the extent of BBB leakage and pericyte coverage also correlates with the presence of microhaemorrhages in these hypomorphic mouse models, although this is more challenging to do in mice than in zebrafish.

The bold assertion on lines 183 -187 that a lack of specific BBB phenotype in pdgfrb zebrafish mutant invalidates mouse model findings is unfounded. Despite the notion that zebrafish endothelium possesses a BBB, I present a few examples highlighting the differences in brain vascular development and why the authors' expectation of a straightforward extrapolation of mouse BBB phenotypes to zebrafish is untenable.

In mice Pdgfrb knockout is lethal, but in zebrafish, this is not the case. In marked contrast to mice, however, zebrafish pdgfrb null mutants reach adulthood despite extensive cerebral vascular anomalies and hemorrhage. Following the authors' argumentation about the unlikely divergence of zebrafish and mice evolution, does it mean that the described mouse phenotype warrants a revisit and that the Pdgfrb knockout in mice perhaps is not lethal? Another example where the role of a gene product is not one-to-one, which relates to pericyte development, is Notch3. Notch3-null mice do not show significant changes in pericyte numbers or distribution, suggesting a less prominent role in pericyte development compared to zebrafish.

Although many aspects of development are conserved between species, there are significant differences during brain vascular development between zebrafish and mice. These differences could reveal why the BBB is not impaired in zebrafish pdgfrb mutants. There is a difference in the temporal aspect when various cellular players emerge. The timing of microglia colonization in the brain differs. In mice, microglia colonization starts before the first vessel sprouts enter the brain, while in zebrafish, microglia enter after. Additionally, microglia in zebrafish and mice have a different ontogeny. In mice, astrocytes specialize postnatally and form astrocyte endfeet postnatally. In zebrafish, radial glia/astrocytes form at 48 hpf, and as early as 3 dpf, gfap+ cells have a close relationship with blood vessels. Thus, these radial glia/astrocyte-like cells could play an important role in BBB induction in zebrafish. It's worth noting that in Drosophila, the blood-brain barrier is located in glial cells. While speculative, these cells might still play a role in zebrafish, while the role of pericytes does not seem to be crucial. Pericytes enter the brain and contact with developing vasculature (endothelium) relatively late in zebrafish (60 hpf). In mice, the situation is different, as there is no such lag between endothelium and pericyte entry into the brain. I suggest that the authors approach the observed data with curiosity and ask: Why are these differences present? Are all aspects of the BBB induced by neural tissue in zebrafish? What is the contribution of microglia and astrocytes?"

Another interesting aspect to consider is the endothelial-pericyte ratio and longitudinal coverage of pericytes in the zebrafish brain, and how this relates to what is observed in mice. How similar is the zebrafish vasculature to the mouse vasculature when it comes to the average length of pericytes in the zebrafish brain? Does the longitudinal coverage of pericytes in the zebrafish brain reach nearly 100%, as it does in mice?

Based on the preceding arguments, it is recommended that the authors present a balanced discussion that provides insightful discussion and situates their work within a broader framework.

Overall, we agree with most of the points made by the reviewer above. As we have now extended the format of this paper to be a full article, we have space to provide an extended discussion and introduction. We now try to capture many of the points made by the reviewer and we think that this has significantly improved the paper. We thank the reviewer for this contribution.

We do want to point out that we did not state that our findings using zebrafish pdgfrb mutants invalidate mouse model findings. We suggest that a deeper analysis to understand the nature of the hotspots in mural cell deficient mammalian models could be very interesting in light of the zebrafish observations. We hope that the revised discussion better reflects this.

Reviewer #3 (Public review):

This manuscript examines the role of pdgfrb-positive pericytes in the establishment and maintenance of the blood-brain barrier (BBB) in the zebrafish. Previous studies in PDGFB- or PDGFRB-deficient mice have suggested that loss of pericytes results in disruption of the BBB. The authors show that zebrafish pdgfrb mutant larvae have an intact BBB and that pdgfrb mutant adult fish show large vessel defects and hemorrhage but do not exhibit substantial leakage from brain capillaries, suggesting loss of pericytes is not sufficient to "open" the BBB. The authors use beautiful and compelling images and rigorous quantification to back up most of their conclusions. The imaging of the adult brain is particularly nice. The authors rigorously document the lack of BBB leakage in pdgfrbuq30bh mutant larvae and large vessel phenotypes (eg, enlargement and rupture) in pdgfrbuq30bh mutant adults. A few points would help the authors to further strengthen their findings contradicting the current dogma from rodent models.

We appreciate the reviewer's comments on the manuscript overall and agree that addressing the raised points was needed to strengthen our findings. We have addressed the main points below and believe that this revision greatly improves this study.

Major point:

The authors document pericyte loss using a single TgBAC(pdgfrb:egfp)ncv22 transgenic line driven by the promoter of the same gene mutated in their pdgfrbuq30bh mutants. Given their findings on the consequences of pericyte loss directly contradict current dogma from rodent studies, it would be useful to further validate the absence of brain pericytes in these mutants using one of several other transgenic lines marking pericytes currently available in the zebrafish. This could be done using pdgfrb crispants, which the authors show nicely phenocopy the germline mutants, at least in larvae. This would help nail down the absence of any currently identifiable pericyte population or sub-population in the loss of pdgfrb animals and substantially strengthen the authors' conclusions.

We thank the reviewer and agree that examination of pdgfrb^uq30bh mutants using another transgenic line labelling pericytes would further validate the absence of brain pericytes. We generated a transgenic line, TgBAC(abcc9:abcc9-T2A-mCherry)^uom139, to visualise pericytes and validated the absence of brain pericytes in the pdgfrb mutants (revised Extended Data Fig. 1b). The loss of brain pericytes matched our findings using TgBAC(pdgfrb:egfp)^uq15bh line as well as previously published data by Ando et al 2016-2021, where the brain pericytes except for metencephalic artery were missing[2,3].

Other issues:

The authors should provide more information about the pdgfrbuq30bh mutant and how it was generated (including a diagram in a supplemental figure would be useful).

We thank the reviewer for this suggestion. In addition to the explanations provided in supplementary materials, we have added a schematic, provided sanger sequencing results showing the mutation as well as predicted effect of the mutation on the protein domains (Extended Data Fig. 1a).

It would be helpful to show some data on whether mutants show morphological phenotypes or developmental delay at 7 and 14 dpf, to provide some context to better assess the reduced branching and vessel length vascular phenotypes (see Figures 1c-e).

We thank the reviewer for this suggestion. We have provided further details on body length and survival of the pdgfrb mutants until 90 dpf. As reported by Ando et al 2021, we did not observe any distinguishing feature until about 30 dpf[1,3]. The adult anatomy of our mutant allele matches that of previously described null mutants and is now shown (Extended Data Fig. 1f).

If available, it would be helpful to have a positive control for the tracer leakage experiments - a genetic manipulation that does cause disruption of the BBB and leakage at 2 hours post-tracer injection (see Figures 1f and g).

We thank the reviewer for this suggestion and agree that a positive control would validate reliability of our method. We have performed new experiments at 3 dpf when BBB integrity is not yet established and at 7 dpf when BBB is functional in zebrafish[5], testing both 10 and 70 kDa tracers (new data in Fig. 2e–f). We detected significantly higher tracer accumulation at 3 dpf, showing that our methods can detect tracer leakage in the brain.

Quantification of the findings in Figure 4c, d would be useful, as would the use of germline fish for these experiments if these are now available. If this is not possible, it would be helpful to document that the crispants used in these experiments lack pdgfrb:egfp pericytes at adult stages (this is only shown for 5 dpf larvae, in Extended Data Figure 4b).

We thank the reviewer for this comment. Using TgBAC(pdgfrb:egfp)^uq15bh line, we have imaged coronal brain sections collected from 10-week old pdgfrb crispants and uninjected siblings (age-matched animals used in Fig. 5d–e, previously Fig. 4c–d). We have now included data showing that adult pdgfrb crispants lack brain mural cells, phenocopying pdgfrb^uq30bh mutants (new data, Extended Data Fig. 6f). These particular crispants are very reliable in our hands and nicely reproduce stable mutant phenotypes, giving us confidence to use the faster F0 approach in this experiment.

Adult mutants clearly show less dye leakage in the more superficial capillary regions than WT siblings, but dextran intensity is a bit higher, although this could well be diffusion from more central brain regions where overt hemorrhage is occurring. Along similar lines though, the authors' TEM data in Extended Data Figure 4d hints that there may be more caveolae in mutant brain capillaries, although the N number was lower here than for the measurements from TEM of larger central vessels (Figure 4g). It would be useful to carry out additional measurements to increase the N number in Figure 4d to see whether the difference between wild-type sibling and mutant capillary caveolae numbers remains as not significant.

We thank the reviewer for these raising important points and suggestions.

Firstly, in relation to signal in capillary regions and likely diffusion from hotspots, please see the response to reviewer 3 point 9 above.

Secondly, we have imaged and analysed more capillaries in both pdgfrb mutants and siblings (Extended Data Fig. 7a–b, previously Extended Data Fig. 4d). The results showed no significant difference between these groups, suggesting that capillary EC transcytosis is unchanged in our pdgfrb mutants.

It might be helpful to include some orienting labels and/or additional descriptions in the figure legends to help readers who are not used to looking at zebrafish brain vessels have an easier time figuring out what they are looking at and where it is in the brain.

We thank the reviewer for this suggestion and agree that adding further information in the figure legends and illustrations about orientation would make it easier for readers. In addition to the information provided in the figure legends in the submitted version, we have added an illustration, more labels on the revised figures, extended the descriptions in figure legends, main text and methods.

We have added a schematic depicting the tracer leakage assay workflow, orientation of live imaging and analysed region of interest (Extended Data Fig. 1a–b).

All figure legends have been updated with the anatomical position and microscopy view.

Additional labels on figures have been added to understand the referenced vessel names (new data in Fig. 3c and Extended Data Fig. 4a–b′).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The study uses the intensity of tracer signals within the vessels to analyze BBB permeability, potentially underestimating leakage severity. The dye intensity is measured 2 hours after injection, however, other studies have already observed leakage after 30 Minutes, by imaging directly in the brain parenchyma. The overall intensity should also decrease through leakage from the other vessels of the body, e.g. in the trunk and tail. Probably the loss of intra-vascular dye intensity from leakage in barrier-free vessels is already so high (after 2 hours) that the smaller amount of leakage across the BBB cannot be observed.

We thank the reviewer for this comment and suggestion. We agree that small sized tracers leak from vasculature, particularly through fenestrated vessels in the trunk and tail. We have based our timing on previous studies and our own experience. In zebrafish, the study by O’Brown et al 2019 also used 2 hpi[5] for detection of leakage in mfsd2aa mutants, which also has been proposed to regulate BBB integrity by controlling EC transcytosis. Therefore, we believe that performing experiments at 2 hpi is appropriate to investigate roles of pericytes in BBB integrity. Our data would suggest that this timing works.

In response to this and other comments, we performed further experiments and analyses to test leakage of tracers testing molecular weights ranging from 1 to 2000 kDa individually. We showed that these tracers can reliably be detected in brain parenchyma and vasculature when imaged at 2 hpi. In another study, we showed that medium size tracers such as 40 kDa Dextran can be reliably detected in the vasculature in similar timepoints[10]. Considering we have performed experiments using 10 and 70 kDa tracers do detect parenchymal tracer accumulation and tracer still within the vessels, we believe this timepoint is appropriate for assessing BBB integrity in zebrafish.

In addition to these experiments, see our tracer leakage experiments in 1-month-old animals, at 0.5 and 6 hpi to test leakage pattern described above (Fig. 5 and Extended Data Fig. 6).

Therefore, the authors will need to validate their method of choice, showing an impairment of the BBB, caused by other agents (known to affect the BBB), and at 48hpf, when the BBB is not tightened yet. One example for BBB impairment can be found in O'Brown et al (2019), eLife 8e47326. doi: 10.7554/eLife.47326

We thank the reviewer for this suggestion. As shown by O’Brown et al 2019, we have performed experiments at 3 dpf when BBB integrity is not mature and at 7 dpf when BBB is functional[5], testing both 10 and 70 kDa tracers. We detected significantly higher tracer accumulation at 3 dpf, showing our new additional method (see below) can detect tracer leakage in the brain (new data in Fig. 2e–f).

Ideally, the authors would also supplement the method with additional approaches in the younger developmental stages to validate their findings.

The validation of the method and the findings is particularly important for the claims of lack of BBB impairment in the absence of mural cells, as this is a "negative" finding.

In response to this and comments from other reviewers, we performed additional tracer leakage experiments (new data in Fig. 2a–d) where we imaged 10 and 70 kDa tracers with a vascular reporter (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916) and used this reporter for normalisation. Both this approach as well as the experiments provided in the first submission (updated as Extended Data Fig. 3a–d) showed that pdgfrb mutants at 7 and 14 dpf have indistinguishable BBB integrity compared to siblings. See also Author response image 1 that further addresses this.

I also strongly suggest to rephrase and downtown the claim that vascular mural cells do not control the blood-brain barrier in developing zebrafish.

As a negative finding cannot be proven completely and lots of the previously shown effects on murine BBB impairment are rather weak (when caused by single agents such as Claudin5 deficiency or Sphingosine-phosphate receptor1 knockout), it might be important to only claim that in zebrafish no strong impairment (as observed in the mural cell-deficient mouse) could be observed. Or rephrase it to "no impairment as severe as/comparable to ... could be observed" and then provide an impairment control for the developmental stages.

We thank the reviewer for this comment and agree that negative findings are very challenging to prove. However, we find no evidence of leakage of the BBB in animals lacking mural cells at 7 and 14 dpf and believe that our data is robust on this point. As such, we believe we show that a vertebrate with a largely conserved EC BBB, can have intact barrier function in the absence of mural cells.

We have as suggested revised our claims throughout the manuscript to provide more further nuanced discussion of this, but we do not want to water down our claims too much as we believe they are important. We hope that the reviewer will appreciate our carefully worded and expanded discussion section.

Additional items of interest to the readers and therefore suggestions to improve the manuscript could be

(1) To include more molecular analysis: while the study identifies caveolae induction and basement membrane thickening as potential contributors to focal leakage, the exact molecular mechanisms linking mural cell loss to these structural changes are not deeply investigated.

(2) Also, the study primarily associates BBB disruption in the adult with aneurysms. Therefore other subtle or diffuse changes to BBB permeability that might occur even without overt vascular lesions are potentially underrepresented.

However, following up experimentally on these might exceed the scope of the manuscript.

We thank the reviewer for these suggestions and agree with both points. However, as stated by the reviewer, these experiments are beyond the scope of the manuscript and represent future directions for our lab and others.

Reviewer #2 (Recommendations for the authors):

(1) Mouse genes should be written as follows: Pdgfb, Pdgfrb and be in italics. See line line 70: it should be written "Pdgfb and Pdgfrb (italics)" and not "PdgfB and Pdgfrβ".

We have updated the text according to the reviewer’s suggestion.

(2) Please state the age of the fish analyzed in Figure 1f and 1g.

We have moved this data to Extended Fig. 3a–d (previously Fig. 1f-g) and have placed age information on the images and in the figure legends.

(3) Is the reduced vascular complexity in pdgfb mutant due to reduced angiogenesis or due to excessive pruning?

This is a good question, and we do not know at this stage. We have unpublished data that suggest pericytes secrete angiogenic growth factors, but this question warrants a thorough investigation that we believe is beyond the scope of this current study.

(4) Please check that the figure legends state the correct number of fish analysed. For example, Figure 1 d, e N=8 but there seem to be 9 data points per group - 14dpf.

We apologise for this mistake and thank the reviewer for raising this. We have updated the graphs and figure legends accordingly.

(5) Please indicate in the figures the genotypes (wt, het) of a sibling presented alongside a pdgfb mutant.

Wild-type and heterozygous mutants are commonly used together in zebrafish research as a collective control group termed siblings. Since we didn’t see any difference between wild-type and pdgfrbuq30bh/- groups in any experiments, we reported these groups together. This is now stated in the supplementary materials.

One exception to this was examination of the growth and survival rates where we show the genotypes separately (new data in Extended Data Fig. 1b-f).

(6) Please explain clearly what region is shown in Figure 2B. I do not understand the explanation "approximate location of dotted line". Is the image in the panel "a" top view of a brain?

We have moved this data to Fig. 3a′ (previously Fig. 2b) and replaced the dotted line in Figure 3a (previously Fig. 2a) with a white box indicating the location of the restricted region in the whole brain image.

We have revised the text as below:

“Subset of z-slices from the whole brain imaging in (a) and (b) (white boxes) indicating mural cell loss and abnormal capillary network patterning. 100-μm-thick maximum intensity projections (MIP) were generated using the continuation of the left middle mesencephalic central artery (MMCtA, arrow) as an anatomical landmark.”

In addition, we have updated all our figure legends clearly stating the view and anatomical position of the imaged sample.

(7) Figure 2e: Note that- the dotted areas do not correspond to the areas magnified. Please adjust.

We have moved this data to Extended Data Fig. 5a (previously Fig. 2e–e′) and updated the location of the white box in 5a shown in enlarged view in 5a′.

(8) Lines 112 and 114 - Should the indicated figure be Figure 2b-d and Figure 2c-d, respectively, and not Figure 1?

We thank the reviewer for pointing out this mistake. All the figure legends are now referred to appropriately in the revised manuscript.

(9) Data presented in Figure 2 and Figure 3 can be consolidated and presented as one Figure.

We thank the reviewer for this suggestion. After addition of new data and revising the manuscript we have decided to keep these data presented separately.

(10) Note that Figure 2a,b shows 5-month-old fish, not 2-month-old fish. Additionally, Extended Data Figure 3 shows 5-month-old fish, not 3-month-old fish.

The stages noted by the reviewer were correctly indicated.

(11) Figure 2d: Please clarify the definition of a "large vessel".

We have observed normal morphology in capillaries and noted aneurysms and hotspots in large calibre vessels such as arteries, which become more severe over time. We have revised this across the manuscript accordingly.

(12) Figure 4a, b: Please explain how the hotspots of leakage were defined based on the extravasated tracer.

Hotspots of leakage are scored when fluorescent tracer aggregates are clearly observed outside the vessels. Vessel borders were defined using the transgenic lines (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916). We have added a clear description in the methods section (lines 473–475).

Figure 4c: Why were Pdgfrb crispants used and not the mutant line?

They were used as pdgfrb crispants phenocopy the lack of brain mural cells (Extended Data Fig. 5e, previously Extended Data Fig. 4b) and mutant phenotype reliably and for practical reasons, because they allow faster experiments and reduce fish usage.

Figure 4e: The magnification of the electron microscopy images does not make it possible to clearly identify caveolae. What was the magnification of the collected images for caveolae analysis? How did the authors ensure that they quantified only caveolae and not other types of vesicles?

Respectfully, we disagree that the magnification is insufficient as our images were captured and analysed consistent with previous ultrastructural descriptions[11,12]. We based our quantification of caveolae on the size of vesicles observed and define them as circular profiles of less than 100 nm in diameter and were scored as luminal or abluminal based on proximity to each surface membrane (within 500 nm of each surface or in a thin-walled vessel the caveolae closest to each surface) (lines 398–409). Importantly, comparable analyses at similar magnifications have been independently validated in multiple caveola-deficient zebrafish genetic models[4,13]. Interestingly given the reviewers comments above, we do see increased vesicular structures that are larger than caveolae, but we only provide quantification of the caveolae here.

Reviewer #3 (Recommendations for the authors):

Congratulations to the authors on their really beautiful imaging and rigorous quantitative documentation of phenotypes - this is a really nicely done study, and could be very important to the field with just a few additional experiments to buttress the key conclusions.

We thank the reviewer for their kind comments.

In addition to the comments noted in the public review, I would only point out that there are two mislabeled call-outs in the text (Lines 112 and 114; says Figure 1, should say Figure 2).

We thank the reviewer for this point and have now revised the text accordingly.

(1) Ando, K., Ishii, T. & Fukuhara, S. Zebrafish Vascular Mural Cell Biology: Recent Advances, Development, and Functions. Life (Basel) 11 (2021). https://doi.org/10.3390/life11101041

(2) Ando, K. et al. Clarification of mural cell coverage of vascular endothelial cells by live imaging of zebrafish. Development 143, 1328-1339 (2016). https://doi.org/10.1242/dev.132654

(3) Ando, K. et al. Conserved and context-dependent roles for pdgfrb signaling during zebrafish vascular mural cell development. Dev Biol 479, 11-22 (2021). https://doi.org/10.1016/j.ydbio.2021.06.010

(4) Lim, Y. W. et al. Trans-Endothelial Trafficking in Zebrafish: Nanobio Interactions of Polyethylene Glycol-Based Nanoparticles in Live Vasculature. ACS Nano (2026). https://doi.org/10.1021/acsnano.5c21042

(5) O'Brown, N. M., Megason, S. G. & Gu, C. Suppression of transcytosis regulates zebrafish blood-brain barrier function. Elife 8 (2019). https://doi.org/10.7554/eLife.47326

(6) O'Brown, N. M. et al. The secreted neuronal signal Spock1 promotes blood-brain barrier development. Dev Cell 58, 1534-1547 e1536 (2023). https://doi.org/10.1016/j.devcel.2023.06.005

(7) Armulik, A. et al. Pericytes regulate the blood-brain barrier. Nature 468, 557-561 (2010). https://doi.org/10.1038/nature09522

(8) Daneman, R., Zhou, L., Kebede, A. A. & Barres, B. A. Pericytes are required for blood-brain barrier integrity during embryogenesis. Nature 468, 562-566 (2010). https://doi.org/10.1038/nature09513

(9) Mae, M. A. et al. Single-Cell Analysis of Blood-Brain Barrier Response to Pericyte Loss. Circ Res 128, e46-e62 (2021). https://doi.org/10.1161/CIRCRESAHA.120.317473

(10) Lim, Y.-W. et al. A Standardized Protocol to Investigate Trans- Endothelial Trafficking in Zebrafish: Nano-bio Interactions of PEG-based Nanoparticles in Live Vasculature. bioRxiv, 2025.2007.2023.666282 (2025). https://doi.org/10.1101/2025.07.23.666282

(11) Parton, R. G. & Simons, K. The multiple faces of caveolae. Nat Rev Mol Cell Biol 8, 185-194 (2007). https://doi.org/10.1038/nrm2122

(12) Parton, R. G. & del Pozo, M. A. Caveolae as plasma membrane sensors, protectors and organizers. Nat Rev Mol Cell Biol 14, 98-112 (2013). https://doi.org/10.1038/nrm3512

(13) Lim, Y. W. et al. Caveolae Protect Notochord Cells against Catastrophic Mechanical Failure during Development. Curr Biol 27, 1968-1981 e1967 (2017). https://doi.org/10.1016/j.cub.2017.05.06

eLife Assessment

The authors aim to understand why Kupffer cells (KCs) die in metabolic-associated steatotic liver disease (MASLD). This is a valuable study using in vitro studies and an in vivo genetic mouse model, suggesting that increased glycolysis contributes to KC death in MASLD. The data presented are now convincing and adequately revised. This work will be of interest to researchers in the immunology and metabolism fields.

Reviewer #3 (Public review):

This manuscript provides novel insights into altered glucose metabolism and KC status during early MASLD. The authors propose that hyperactivated glycolysis drives a spatially patterned KC depletion that is more pronounced than the loss of hepatocytes or hepatic stellate cells. This concept significantly enhances our understanding of early MASLD progression and KC metabolic phenotype.

Through a combination of TUNEL staining and MS-based metabolomic analyses of KCs from HFHC-fed mice, the authors show increased KC apoptosis alongside dysregulation of glycolysis and the pentose phosphate pathway. Using in vitro culture systems and KC-specific ablation of Chil1, a regulator of glycolytic flux, they further show that elevated glycolysis can promote KC apoptosis.

However, it remains unclear whether the observed metabolic dysregulation directly causes KC death or whether secondary factors, such as low-grade inflammation or macrophage activation, also contribute significantly. Nonetheless, the results, particularly those derived from the Chil1-ablated model, point to a new potential target for the early prevention of KC death during MASLD progression.

The manuscript is clearly written and thoughtfully addresses key limitations in the field, especially the focus on glycolytic intermediates rather than fatty acid oxidation. The authors acknowledge the missing mechanistic link between increased glycolysis and KC death. A few things require clarification.

Strengths:

• The study presents the novel observation of profound metabolic dysregulation in KCs during early MASLD and identifies these cells as undergoing apoptosis. The finding that Chil1 ablation aggravates this phenotype opens new avenues for exploring therapeutic strategies to mitigate or reverse MASLD progression.

• The authors provide a comprehensive metabolic profile of KCs following HFHC diet exposure, including quantification of individual metabolites. They further delineate alterations in glycolysis and the pentose phosphate pathway in Chil1-deficient cells, substantiating enhanced glycolytic flux through 13C-glucose tracing experiments.

• The data underscore the critical importance of maintaining balanced glucose metabolism in both in vitro and in vivo contexts to prevent KC apoptosis, emphasizing the high metabolic specialization of these cells.

• The observed increase in KC death in Chil1-deficient KCs demonstrates their dependence on tightly regulated glycolysis, particularly under pathological conditions such as early MASLD.

Weaknesses:

• The TUNEL staining in the overview in Figure 2 is not convincing. Typically the signal overlaps with DAPI, which is mostly not the case in the figures shown.

• The mechanistic link between elevated glycolytic flux and KC death remains unclear.

• Figure S5: shows deltadelta CT values, not relative values. What are the housekeeping genes? There should be at least 2, and they should not have metabolically related functions such as Gapdh.

• Figure 1C: shows WT and KO gating side by side

• The following point has not been answered: "While BMDMs from Chil1 knockout mice are used to demonstrate enhanced glycolytic flux, it remains unclear whether Chil1 deficiency affects macrophage differentiation itself." Expression of certain genes that indicate function does not show whether BMDMs isolated from these KO mice are fully differentiated. Here, counting BM input/ BMDM output, flow cytometry on BMDMs, morphology etc. should be tested.

Reviewer #4 (Public review):

Summary:

In this study, He et al. investigate the mechanisms underlying Kupffer cell (KC) loss during metabolic stress. It has long been observed that embryonically derived KCs decline in obesity and liver disease, a loss that is compensated by monocyte recruitment, although the underlying mechanisms remain unclear. The authors propose that metabolic reprogramming, particularly excessive glycolysis, drives KC death. Using an original murine genetic model to modulate glycolysis, they further demonstrate that enhanced glycolytic activity exacerbates KC damage.

Strengths:

Overall, the study is extremely clearly presented, with a convincing and simple message destined to a vast audience.

Weaknesses:

This manuscript has already undergone one round of revisions in which I was not involved. The authors have tried to address several points raised by the previous reviewers, notably regarding the unexpectedly high level of TUNEL staining observed in KCs. However, I share these concerns expressed by the three reviewers that the reported levels remain difficult to reconcile with the biology. A TUNEL positivity rate of ~60% at week 16 of the HFHC diet would imply massive KC death, which should have led to a near-complete depletion of the KC population, something that is not observed. While I agree that the KC compartment is clearly affected under this dietary challenge, I would strongly encourage the authors to carefully rule out potential technical biases that could account for this implausibly high rate of cell death.

Considering the new in-vivo experiment with 2-DG, it is definitely convincing and clearly adds some value to the full study.

So the full story deserves publication.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to investigate the mechanisms underlying Kupffer cell death in metabolic-associated steatotic liver disease (MASLD). The authors propose that KCs undergo massive cell death in MASLD and that glycolysis drives this process. However, there appears to be a discrepancy between the reported high rates of KC death and the apparent maintenance of KC homeostasis and replacement capacity.

Strengths:

This is an in vivo study.

Weaknesses:

There are discrepancies between the authors' observations and previous reports, as well as inconsistencies among their own findings.

Before presenting the percentage of CLEC4F⁺TUNEL⁺ cells, the authors should have first shown the number of CLEC4F⁺ cells per unit area in Figure 1. At 16 weeks of age, the proportion of TUNEL⁺ KCs is extremely high (~60%), yet the flow cytometry data indicate that nearly all F4/80⁺ KCs are TIMD4⁺, suggesting an embryonic origin. If such extensive KC death occurred, the proportion of embryonically derived TIMD4⁺ KCs would be expected to decrease substantially. Surprisingly, the proportion of TIMD4⁺ KCs is comparable between chow-fed and 16-week HFHC-fed animals. Thus, the immunostaining and flow cytometry data are inconsistent, making it difficult to explain how massive KC death does not lead to their replacement by monocyte-derived cells.

We thank the reviewer for the insightful comment and the opportunity to clarify this important point. To ensure consistency between our methodologies, we replaced Clec4f staining with TIM4 staining results as requested by the reviewer. We first showed the number of TIM4⁺ cells per unit area in Figure 1B. The results showed a significant and progressive loss of TIM4⁺ cells per unit area in the liver parenchyma, decreasing from approximately 60 cells/FOV at baseline (0w) to nearly 50 at 4w and further to about 30 at 16w post-HFHC diet. This finding is fully consistent with our flow cytometry data. The percentage of the embryonically derived KC population (CD11blow F4/80hi TIM4hi) among CD45⁺ cells dropped from 30.2% (0w) to 24.3% (4w) and 17.6% (16w) (Revised Figure 1C). The absolute number per gram of liver decreased from roughly 12 x 10⁵ (1w) to 9 x 10⁵ (4w) and 5 x 10⁵ (16w) (Revised Figure 1D).

These data suggest that despite the reported high rate of cell death among CLEC4F⁺TIMD4⁺ KCs, the population appears to self-maintain, with no evidence of monocyte-derived KC generation in this model, which contradicts several recent studies in the field.

We appreciate the reviewer’s insightful comment. We agree that our data show no substantial generation of monocyte-derived Kupffer cells (MoKCs) within the 16-week HFHC model. However, we do not believe the remaining embryonic KCs(EmKCs) are maintained through self-renewal, as the proportion of Ki67⁺TIM4⁺ cells remains low at all time points (Revised Figure S2D). Instead, our observations align with a phased replacement model: recruited monocytes first differentiate into monocyte-derived macrophages (MoMFs), which we see accumulate (Revised Figure S2B, S2C), and only later adopt a KC phenotype. Consistent with this, our 16-week model shows significant EmKC loss and MoMF expansion, but not yet the emergence of TIM4-MoKCs. This timing is supported by prior studies, where TIM4-KCs were observed at 24 weeks, but not at 16 weeks, on similar diets (Ref. 1,2). Therefore, we interpret our findings as capturing an earlier phase of MASLD progression, characterized by EmKC death and MoMF accumulation, prior to their full differentiation into MoKCs.

Moreover, there is no evidence that TIM4⁺CLEC4F⁺ KCs increase their proliferation rate to compensate for such extensive cell death. If approximately 60% of KCs are dying and no monocyte-derived KCs are recruited, one would expect a much greater decrease in total KC numbers than what is reported.

Thank you for raising this point, which allows for an important clarification. The interpretation that approximately 60% of KCs are dying is correct, but this refers to the proportion of the remaining KC population at 16 weeks that is TUNEL⁺, not to 60% of the original KC pool. Since our data show that over half of the EmKCs are lost by 16 weeks (Revised Figure 1B), the 60% of dying cells at this late time point corresponds roughly to only 25-30% of the total original KC population at baseline. This distinction reconciles the high rate of apoptosis observed late in disease with the overall progressive depletion of the EmKC pool.

It is also unexpected that the maximal rate of KC death occurs at early time points (8 weeks), when the mice have not yet gained substantial weight (Figure 1B). Previous studies have shown that longer feeding periods are typically required to observe the loss of embryo-derived KCs.

We appreciate the reviewer’s insightful observation. We think KC death is a continuous event during MASLD. To induce MASH, previous studies typically assess the loss of EmKCs after longer feeding periods, which might leave us an impression that longer feeding periods are required to observe substantive loss of embryonically derived KCs. In our HFHC model, the proportion of dying KCs was already elevated by 8 weeks, and this high rate was sustained through the 16-week endpoint. In a separate MCD dietary model characterized by rapid MASLD progression, a high rate of KC death was detectable as early as 6 weeks (Revised Figure 1F). Collectively, these data suggest that the onset of significant KC death is dependent on the pace of MASLD pathogenesis, more likely an early-initiated event that is through MASLD progression.

Furthermore, it is surprising that the HFD induces as much KC death as the HFHC and MCD diets. Earlier studies suggested that HFD alone is far less effective than MASH-inducing diets at promoting the replacement of embryonic KCs by monocyte-derived macrophages.

We appreciate the reviewer’s insightful comment. In our study, we observed significant KCs death under both HFD and HFHC feeding for 20, 16 weeks, respectively. Moreover, both HFHC and HFD induced similar stages of MASLD (characterized by significant lipid accumulation without fibrosis development) by these time points (Authir response image 1). Therefore, these data support that the onset of substantial KCs death may be an early MASLD event, before the progression to MASH. Additionally, this finding aligns with existing literature showing that 16 weeks of HFD feeding alone is sufficient to cause a marked reduction in the TIM4⁺KCs population (Ref. 1).

Author response image 1.

Detection of liver fibrosis in MASLD mouse models. Male wild-type C57BL/6J mice were fed a high-fat, high-cholesterol (HFHC) diet for 16 weeks or a high-fat diet (HFD) for 20 weeks to induce MASLD. Mice fed a normal chow diet (NCD) served as controls. (A) Sirius Red staining of liver sections was performed to assess collagen deposition and fibrosis during MASLD progression. Scale bar, 20 μm. (B) Western blot analysis of liver tissue lysates showing α-smooth muscle actin (α-SMA) expression as a marker of hepatic stellate cell activation and liver fibrosis.

In Figure 2D, TIMD4 staining appears extremely faint, making the results difficult to interpret. In contrast, the TUNEL signal is strikingly intense and encompasses a large proportion of liver cells (approximately 60% of KCs, 15% of hepatocytes, 20% of hepatic stellate cells, 30% of non-KC macrophages, and a proportion of endothelial cells is also likely affected). This pattern closely resembles that typically observed in mouse models of acute liver failure. Given this apparent extent of cell death, it is unexpected that ALT and AST levels remain low in MASH mice, which is highly unusual.

Thank you for this important feedback. To address concerns about the clarity of our imaging, we have provided high-resolution split-channel raw images for Figure 2D (Revised Figure 2D), which distinctly show the localization of TIM4, TUNEL, and GS. These confirm the progressive reduction of TIM4⁺KCs and the increase in TUNEL⁺ TIM4⁺cells over time. We agree that the high proportion of TUNEL⁺cells seems at odds with the modest ALT/AST elevation. This discrepancy might be explained by the distinct nature of cell death in MASLD. Unlike the acute necrosis with membrane rupture seen in acute liver failure—which causes massive, rapid enzyme release— obesity-related liver injury is a chronic process dominated by apoptosis (Ref. 4,5). Apoptosis preserves membrane integrity until late stages (Ref. 6), with dying cells packaged into apoptotic bodies for efficient phagocytic clearance by neighboring macrophages (Ref. 7,8). This controlled disposal system minimizes the leakage of intracellular enzymes. Therefore, the coexistence of widespread apoptosis (high TUNEL signal) with limited enzyme release (low ALT/AST) is a recognized feature of chronic MASLD pathogenesis.

No statistical analysis is provided for Figure 5D, and it is unclear which metabolites show statistically significant changes in Figure 5C.

We thank the reviewer for raising this statistical problem. We have now included statistical analysis in Revised Figure 5D.

In addition, there is no evaluation of liver pathology in Clec4f-Cre × Chil1flox/flox mice. It remains possible that the observed effects on KC death result from aggravated liver injury in these animals. There is also no evidence that Chil1 deficiency affects glucose metabolism in KCs in vivo.

We thank the reviewer for these important points. We previously characterized the liver pathology of Clec4f^ΔChil1 mice in detail (preprint: eLife 2025, DOI: 10.7554/eLife.107023.1, Fig. 2). On a normal chow diet, these mice showed no differences in body weight, hepatic lipid deposition, metabolic parameters, or glucose tolerance compared to controls. However, on an HFHC diet, Clec4f^ΔChil1 mice developed significantly worse metabolic and histological phenotypes. Crucially, our in vitro data demonstrate that recombinant Chi3l1 directly reduces KC death (preprint, Fig. 6E-F), indicating that the aggravated MASLD in knockout mice is a consequence of increased KC loss, not its cause.

Regarding glucose metabolism, we have previously shown that Chi3l1 deficiency leads to increased glucose uptake by KCs in vivo using the fluorescent glucose analog 2-NBDG. This effect was reversed by supplementing knockout mice with recombinant Chi3l1 (preprint Fig. 6G-H). This provides direct evidence that Chi3l1 modulates glucose uptake in KCs in vivo.

Finally, the authors should include a more direct experimental approach to modulate glycolysis in KCs and assess its causal role in KC death in MASH.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) in the HFHC-induced MASLD model (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for four weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity during active disease development. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data together with our complementary in vitro gain-of-function experiments, support a contributory role for excessive glycolytic activity in promoting KC apoptosis in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

Reviewer #2 (Public review):

Summary:

In this manuscript, He et al. set out to investigate the mechanisms behind Kupffer Cell death in MASLD. As has been previously shown, they demonstrate a loss of resident KCs in MASLD in different mouse models. They then go on to show that this correlates with alterations in genes/metabolites associated with glucose metabolism in KCs. To investigate the role of glucose metabolism further, they subject isolated KCs in vitro to different metabolic treatments and assess cleaved caspase 3 staining, demonstrating that KCs show increased Cl. Casp 3 staining upon stimulation of glycolysis. Finally, they use a genetic mouse model (Chil1KO) where they have previously reported that loss of this gene leads to increased glycolysis and validate this finding in BMDMs (KO). They then remove this gene specifically from KCs (Clec4fCre) and show that this leads to increased macrophage death compared with controls.

Strengths:

As we do not yet understand why KCs die in MASLD, this manuscript provides some explanation for this finding. The metabolomics is novel and provides insight into KC biology. It could also lead to further investigation; here, it will be important that the full dataset is made available.

Weaknesses:

Different diets are known to induce different amounts of KC loss, yet here, all models examined appear to result in 60% KC death. One small field of view of liver tissue is shown as representative to make these claims, but this is not sufficient, as anything can be claimed based on one field of view. Rather, a full tissue slice should be included to allow readers to really assess the level of death.

Thank you for raising this point regarding data presentation. We analyzed full tissue slices and found that including a view of the entire slice at a standard magnification makes individual KC difficult to resolve (Author response image 2). To clearly represent the extent and distribution of KCs death across the liver tissue slice, we now include lower-magnification images that provide a wider field of view, allowing readers to assess the pattern across a larger tissue area (Revised Figures 1, 2, 6F).

Author response image 2.

Assessment of KCs death on full liver tissue slice. (A) Immunofluorescence staining was performed to detect Kupffer cell (KC) death in liver sections from mice fed an MCD diet for 6 weeks. Cell death was assessed by TUNEL staining (green), and KCs were identified by TIM4 staining (red). Nuclei were counterstained with DAPI (blue). Representative whole-tissue view is shown. Scale bars, 1mm.

Additionally, there is no consistency between the markers used to define KCs and moMFs, with CLEC4F being used in microscopy, TIM4 in flow, while the authors themselves acknowledge that moKCs are CLEC4F+TIM4-. As moKCs are induced in MASLD, this limits interpretation. Additionally, Iba1 is referred to as a moMF marker but is also expressed by KCs, which again prevents an accurate interpretation of the data. Indeed, the authors show 60% of KCs are dying but only 30% of IBA1+ moMFs, as KCs are also IBA1+, this would mean that KCs die much more than moMFs, which would then limit the relevance of the BMDM studies performed if the phenotype is KC specific. Therefore, this needs to be clarified.

We thank the reviewer for the constructive comments. For consistency, we have standardized our KC marker to TIM4 for all immunostaining data, aligning it with our flow cytometry analysis (Revised Figures 1, 2D, 6F). We have also clarified that IBA1 is expressed by hepatic macrophages (both KCs and MoMFs)(Revised Figure 2C, Revised manuscript, page 5, lines 182-183). Moreover, we also included the clarification that 60% of TIM4⁺ KCs are TUNEL⁺ versus 30% of total IBA1⁺ cells further supports that KCs undergo death more readily than MoMFs (Revised manuscript, page 5, lines 186-189). We also acknowleged the limitation of BMDM studies in the Revised manuscript, page 8, line 332-340.

The claim that periportal KCs die preferentially is not supported, given that the majority of KCs are peri-portal. Rather, these results would need to be normalised to KC numbers in PP vs PC regions to make meaningful conclusions.

We thank the reviewer for this important point. We included the normalized data. At 8 weeks, the normalized death rate was significantly higher in periportal versus pericentral regions (p = 0.041), supporting increased periportal KC susceptibility during early MASLD. By 16 weeks, proportional death rates became comparable between zones (Revised Figure 2D, Revised manuscript, page 6, lines 194-201).

Additionally, KCs are known to be notoriously difficult to keep alive in vitro, and for these studies, the authors only examine cl. Casp 3 staining. To fully understand that data, a full analysis of the viability of the cells and whether they retain the KC phenotype in all conditions is required.

We appreciate the reviewer’s suggestions. To confirm the identity and health of isolated KCs in our in vitro studies, we showed that ~95% of primary isolated KCs are TIM4⁺ (Revised Figure S3A). Furthermore, Calcein-AM staining confirmed that the remaining KCs under our experimental conditions are viable and healthy (Revised Figure S4A).

Finally, in the Cre-driven KO model, there does not seem to be any death of KCs in the controls (rather numbers trend towards an increase with time on diet, Figure 6E), contrary to what had been claimed in the rest of the paper, again making it difficult to interpret the overall results.

We thank the reviewer for this comment. During our analysis, we indeed observed no reduction in KCs in the Clec4f cre control mice. This prompted us to consider that Cre insertion itself might influence KCs mainteinence. To investigate this, we performed TIM4/Ki67 co-staining, which revealed significantly higher numbers of proliferating KCs in Clec4f cre mice compared with C57BL/6J mice under NCD. Following HFHC feeding, KCs proliferation in Clec4f cre mice increased even further. These results indicate that Cre insertion enhanced KCs self-renewal in Clec4f cre mice，which contributes to maintenance of the KCs pool during MASLD (Revised Figures S8A and S8B). (Revised manuscript, page 9, line 363-370).

Additionally, there is no validation that the increased death observed in vivo in KCs is due to further promotion of glycolysis.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for five weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity in KCs. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data, together with our complementary in vitro gain-of-function experiments support a contributory role for excessive glycolytic activity in promoting KCs death in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

Reviewer #3 (Public review):

This manuscript provides novel insights into altered glucose metabolism and KC status during early MASLD. The authors propose that hyperactivated glycolysis drives a spatially patterned KC depletion that is more pronounced than the loss of hepatocytes or hepatic stellate cells. This concept significantly enhances our understanding of early MASLD progression and KC metabolic phenotype.

Through a combination of TUNEL staining and MS-based metabolomic analyses of KCs from HFHC-fed mice, the authors show increased KC apoptosis alongside dysregulation of glycolysis and the pentose phosphate pathway. Using in vitro culture systems and KC-specific ablation of Chil1, a regulator of glycolytic flux, they further show that elevated glycolysis can promote KC apoptosis.

However, it remains unclear whether the observed metabolic dysregulation directly causes KC death or whether secondary factors, such as low-grade inflammation or macrophage activation, also contribute significantly. Nonetheless, the results, particularly those derived from the Chil1-ablated model, point to a new potential target for the early prevention of KC death during MASLD progression.

The manuscript is clearly written and thoughtfully addresses key limitations in the field, especially the focus on glycolytic intermediates rather than fatty acid oxidation. The authors acknowledge the missing mechanistic link between increased glycolysis and KC death. Still, several interpretations require moderation to avoid overstatement, and certain experimental details, particularly those concerning flow cytometry and population gating, need further clarification.

Strengths:

(1) The study presents the novel observation of profound metabolic dysregulation in KCs during early MASLD and identifies these cells as undergoing apoptosis. The finding that Chil1 ablation aggravates this phenotype opens new avenues for exploring therapeutic strategies to mitigate or reverse MASLD progression.

(2) The authors provide a comprehensive metabolic profile of KCs following HFHC diet exposure, including quantification of individual metabolites. They further delineate alterations in glycolysis and the pentose phosphate pathway in Chil1-deficient cells, substantiating enhanced glycolytic flux through 13C-glucose tracing experiments.

(3) The data underscore the critical importance of maintaining balanced glucose metabolism in both in vitro and in vivo contexts to prevent KC apoptosis, emphasizing the high metabolic specialization of these cells.

(4) The observed increase in KC death in Chil1-deficient KCs demonstrates their dependence on tightly regulated glycolysis, particularly under pathological conditions such as early MASLD.

Weaknesses:

(1) The novelty is questionable. The presented work has considerable overlap with a study by the same lab, which is currently under review (citation 17), and it should be considered whether the data should not be presented in one paper.

We appreciate the reviewer for the opportunity to clarify the relationship between the two studies. In our previous work (citation 17), we focused on the transcriptional metabolic differences between Kupffer cells (KCs) and monocyte-derived macrophages (MoMFs) and identified Chi3l1 as a selective protective factor that limits glucose uptake and shields KCs from metabolic stress–induced cell death, with minimal effects on MoMFs. That study directly motivated the current work. The observation that KCs are uniquely protected from metabolic stress led us to hypothesize that excessive glycolytic activation itself may be a primary driver of KCs death, which forms the central question of the present study. Accordingly, the current manuscript shifts the focus from Chi3l1-mediated protection to the mechanistic role of hyperglycolysis in driving KCs mortality, using distinct experimental approaches and addressing a different biological question. Because the two studies address conceptually distinct aims—one defining a protective regulator of KCs survival and the other dissecting glycolysis-driven KCs death mechanisms—we believe they are best presented as separate manuscripts. Combining them into a single study would dilute the mechanistic depth and clarity of each story.

(2) The authors report that 60% of KCs are TUNEL-positive after 16 weeks of HFHC diet and confirm this by cleaved caspase-3 staining. Given that such marker positivity typically indicates imminent cell death within hours, it is unexpected that more extensive KC depletion or monocyte infiltration is not observed. Since Timd4 expression on monocyte-derived macrophages takes roughly one month to establish, the authors should consider whether these TUNEL-positive KCs persist in a pre-apoptotic state longer than anticipated. Alternatively, fate-mapping experiments could clarify the dynamics of KC death and replacement.

We thank the reviewer for this astute observation. As shown in revised Figure 2D, the proportion of TIM4⁺TUNEL⁺KCs peaks at 8 weeks after HFHC feeding and remains elevated at 16 weeks. However, examination of the corresponding single-channel TIM4 staining during this period reveals that the overall density of TIM4⁺ KCs does not undergo abrupt or synchronous depletion. This temporal dissociation between sustained TUNEL positivity and relatively gradual KCs loss suggests that TUNEL-positive KCs do not undergo immediate clearance. Based on these observations, we agree with the reviewer that a substantial fraction of TUNEL-positive KCs likely persists in a prolonged pre-apoptotic or stressed state rather than undergoing rapid cell death. This interpretation is consistent with the absence of extensive KCs depletion or compensatory monocyte infiltration at these time points. Importantly, previous studies (Ref. 1,2) indicate that KCs are eventually lost as MASLD progresses, supporting the notion that KC death is a gradual process that unfolds over an extended time frame rather than acutely.

(3) The mechanistic link between elevated glycolytic flux and KC death remains unclear.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for five weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity of KCs. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data, together with our complementary in vitro gain-of-function experiments, support a contributory role for excessive glycolytic activity in promoting KC apoptosis in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

(4) The study does not address the polarization or ontogeny of KCs during early MASLD. Given that pro-inflammatory macrophages preferentially utilize glycolysis, such data could provide valuable insight into the reason for increased KC death beyond the presented hyperreliance on glycolysis.

We thank the reviewer for this insightful comment. Regarding KCS ontogeny, flow cytometry analysis (Revised Figure 1C) shows that KCs remain uniformly TIM4^hi during early MASLD, indicating that monocyte-derived KCs (TIM4^low) have not yet emerged at these stages. To address KCs polarization, we assessed the expression of M1-type (pro-inflammatory) markers (Nos2, Cxcl9, CIITA, Cd86, Ccl3, and Ccl5) and M2-type (anti-inflammatory) markers (Chil3, Retnla, Arg1, and Mrc1) in KCs isolated from WT mice fed a HFHC diet for 0, 8, and 16 weeks. As shown in revised Figure S5A, M1 markers progressively increase over time, whereas M2 markers remain unchanged or slightly decrease. This polarization shift is consistent with the increased glycolytic activity observed in KCs during early MASLD. Together, these data indicate that embryonically derived KCs undergo a pro-inflammatory polarization accompanied by enhanced glycolytic metabolism during early MASLD, providing mechanistic context for their increased susceptibility to metabolic stress–induced cell death beyond hyperreliance on glycolysis alone (Revised manuscript, page 7-8, line 307-321).

(5) The gating strategy for monocyte-derived macrophages (moMFs) appears suboptimal and may include monocytes. A more rigorous characterization of myeloid populations by including additional markers would strengthen the study's conclusions.

We thank the reviewer for raising this important point. To improve the rigor of our analysis, we adopted gating strategies established in previous studies (PMID: 41131393; PMID: 32562600). Specifically, Kupffer cells were defined as CD45⁺CD11b⁺F4/80^hi TIM4^hi cells, while monocyte-derived macrophages (MoMFs) were defined as CD45⁺Ly6G^-CD11b⁺F4/80^low TIM4^low/− cells, thereby excluding contaminating neutrophils and minimizing inclusion of circulating monocytes. Using this refined gating strategy, we observed a progressive reduction of KCs accompanied by a corresponding increase in MoMFs in WT mice during HFHC feeding (Revised Figures 1C and S2B–C), (Revised manuscript, page 4, line 154-163).

(6) While BMDMs from Chil1 knockout mice are used to demonstrate enhanced glycolytic flux, it remains unclear whether Chil1 deficiency affects macrophage differentiation itself.

We thank the reviewer for this important question. To determine whether Chi3l1 deficiency affects macrophage differentiation, we analyzed the expression of M1-type (pro-inflammatory) markers (Nos2, Cxcl9, CIITA, Cd86, Ccl3, and Ccl5) and M2-type (anti-inflammatory) markers (Chil3, Retnla, Arg1, and Mrc1) in Kupffer cells isolated from WT and Chil1^-/- mice fed a HFHC diet for 0, 8, and 16 weeks. At baseline (0 weeks), Chi3l1 deficiency was associated with elevated expression of multiple M1 markers, whereas M2 marker expression was comparable between WT and Chil1^-/- KCs. During MASLD progression, the pro-inflammatory signature in Chil1^-/- KCs was further enhanced, while anti-inflammatory marker expression became dysregulated (revised Figure S5C). Together, these data indicate that Chi3l1 deficiency does not impair macrophage differentiation per se but biases KCs toward a partially pro-inflammatory, M1-like phenotype, providing additional context for the enhanced glycolytic flux observed in Chi3l1-deficient macrophages (Revised manuscript, page 7-8, line 307-321).

(7) The authors use the PDK activator PS48 and the ATP synthase inhibitor oligomycin to argue that increased glycolytic flux at the expense of OXPHOS promotes KC death. However, given the high energy demands of KCs and the fact that OXPHOS yields 15-16 times more ATP per glucose molecule than glycolysis, the increased apoptosis observed in Figure 4C-F could primarily reflect energy deprivation rather than a glycolysis-specific mechanism.

We thank the reviewer for highlighting this important point. We agree that KCs are highly metabolically active and that perturbations of OXPHOS can influence overall cellular energy balance. As noted in our response to comment #3, we further performed glycolysis inhibition assay by 2-DG in vivo, the protection of KCs observed following 2-DG in vivo (Revised Figure 4E-G) further provides evidence that increased glycolytic flux is not merely correlated with, but functionally contributes to KCs loss in

MASLD.

(8) In Figure 1C, KC numbers are significantly reduced after 4 and 16 weeks of HFHC diet in WT male mice, yet no comparable reduction is seen in Clec4Cre control mice, which should theoretically exhibit similar behavior under identical conditions.

We thank the reviewer for this comment. During our analysis, we indeed observed no reduction in KCs in the Clec4f cre control mice. This prompted us to consider that Cre insertion itself might influence KCs mainteinence. To investigate this, we performed TIM4/Ki67 co-staining, which revealed significantly higher numbers of proliferating KCs in Clec4f cre mice compared with C57BL/6J mice under NCD. Following HFHC feeding, KCs proliferation in Clec4f cre mice increased even further. These results indicate that Cre insertion enhanced KCs self-renewal in Clec4f cre mice，which contributes to maintenance of the KCs pool during MASLD (Revised Figures S8A and S8B). (Revised manuscript, page 9, line 363-370).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

To address the concerns raised in the public review, the authors should:

(1) Reassess their conclusions using the same panels in flow and microscopy, e.g., the combination of CLEC4F, TIM4, and IBA1. This will allow resKCs (CLEC4F+TIM4+IBA1+), moKCs (CLEC4F+TIM4-IBA1+), and moMFs (CLEC4F-TIM4-IBA1+) to be accurately defined and hence their viability and numbers correctly assessed.

We thank the reviewer for this insightful suggestion. In our flow cytometry analysis, we did not detect a CD45⁺CD11b^lowF4/80^hiTIM4^low population, indicating that monocyte-derived KCs (moKCs) have not emerged in our model at this stage. To more accurately quantify resident KCs (resKCs) in the current study, we replaced CLEC4F with TIM4 staining and enumerated TIM4⁺as well as TIM4⁺TUNEL⁺ cells. These data were highly consistent with CLEC4F⁺TUNEL⁺cell counts, confirming that moKCs are not involved in KCs death during early MASLD (Revised Figure 1A,B,E,F).

(2) Investigate why the number of KCs in controls and MASLD are so distinct between Figures 1 and 6.

We appreciate the reviewer’s suggestions. Like we explained above, Cre insertion promotes KCs self-renewal (Revised manuscript, Figure S8). This enhanced proliferative capacity likely accounts for the relative preservation of KCs numbers in Clec4f-Cre mice during HFHC feeding, explaining the apparent discrepancy with WT mice (Revised manuscript, Figure 6D-E).

(3) Normalise the tunel+ cells based on the number of KCs in PP vs PC regions.

After normalizing KCs death to KCs numbers in periportal (PP) versus pericentral (PC) regions, we found the proportion was significantly higher in PV regions compared to CV regions at 8 weeks of HFHC feeding. We have therefore revised our texts. (Revised manuscript, page 5, lines 194-201).

(4) Demonstrate the viability of KCs in vitro across conditions.

To confirm the identity and health of isolated KCs in our in vitro studies, we show that ~95% of primary isolated KCs are TIM4⁺ (Revised Figure S3A). Furthermore, Calcein-AM staining confirmed that the remaining KCs under our experimental conditions are viable and healthy (Revised Figure S4A).

(5) Confirm previous studies demonstrating different degrees of KC loss depending on the model of MASLD.

We thank the reviewer for highlighting this point. Consistent with previous studies, KCs loss has been reported to varying degrees depending on the MASLD model used, reflecting the heterogeneity of hepatic macrophages, marker choice, mouse husbandry, and diet regimen. For example, in a 6-week MCD feeding model, ~10% of CLEC4F⁺ KCs were TUNEL⁺ (Figure 4A, Ref. 9). Another 6-week MCD study reported a drop from 66% to 26% TIM4⁺ KCs (Figure 2A, Ref. 12). In an HFD model, TIM4⁺ KCs decreased by ~20% after 16 weeks (Figure 1G, Ref. 1). In a Western diet model, TIM4⁺KCs decreased by >50% at 36 weeks (Figures 1J and 2C, Ref. 2). Together, these studies underscore the model-dependent nature of KCs loss and highlight the importance of experimental context and marker selection when assessing KCs dynamics in MASLD. We have included these studies in our discussion section (Revised manuscript, page 9-10, line 393-402)

(6) Demonstrate in vivo that loss of CHIL1 drives further glycolysis in KCs.

In Figure 6G-H of our previous study, we showed that Chi3l1 deficiency leads to more glucose uptake by KCs in vivo whereas suppelementing KO mice with recombinant Chi3l1 will significantly reduced glucose uptake by KCs through treating mice with a fluorescent glucose analog 2-NBDG. We included the related figure here as Author response image 3.

Author response image 3.

Chi3l1 limits glucose uptake by Kupffer cells in vivo. (A) Measurement of 2-NBDG (a fluorescent glucose analog) uptake by KCs in vivo. WT and Chil1^-/- mice, either untreated or supplemented with rChi3l1, were injected intraperitoneally with 12 mg/kg 2-NBDG. After 45mins, KCs were isolated and glucose uptake assessed by spectrophotometry. (B) Representative immunofluorescence images of liver sections stained for TIM4 (red) and 2-NBDG uptake (green) to visualize glucose uptake by KCs in situ. Scale bar = 10 µm (zoom). Quantification is shown as the percentage of TIM4⁺ cells that are also 2-NBDG⁺. Representative images were shown in B. One-way ANOVA was performed in A, B. P value is as indicated.

(7) There is no mention of the publication of the metabolomics dataset; this should be released with the manuscript.

We included the raw metabolomics dataset as Table S1 and S2 now.

Reviewer #3 (Recommendations for the authors):

(1) Methods: Reconsider which methods are described in the main text versus the Supplementary Information to improve readability and consistency.

Thank you for your valuable suggestion. We have reevaluated and adjusted the placement of the methods section between the main text and the supplementary materials.

(2) Line 34: Check for grammar issues.

L34 has been revised as follows : Additionally, using Chi3l1-deficient mice, we further demonstrated that increased glucose utilization accelerates KCs death in vivo.

(3) Lines 101, 110: Explicitly reference the corresponding Supplementary Methods sections.

We have included the references for these two methods sections (Revised supplementary materials and methods, Line 30, 65, respectively).

(4) Figure 2: Iba1 marks all macrophages, not only monocyte-derived macrophages; both figure and text (line 205) require correction.

We have corrected Iba1 represent hepatic macrophages including both KCs and MoMFs (Revised Figure 2C, manuscript page 5, line 182).

(5) Line 218-219: Avoid overinterpretation, as only KCs, hepatocytes, and hepatic stellate cells were assessed - not all hepatic populations.

We appreciate the reviewer’s valuable suggestion and rephrased our description accordingly (Revised manuscript, page 5, line 186-189).

(6) Line 262: Use abbreviations consistently throughout the manuscript.

We have gone through the whole manuscript and double checked the abbreviations.

(7) Line 264: Include the palmitic acid (PA) concentration used.

We included 800 µM PA in the revised manuscript (Revised manuscript, page 6, line 250).”

(8) Lines 316-317: Check for grammar errors.

Grammar errors are checked (Revised manuscript, page 8, line 340-341).

(9) Line 337-338: See comment above on gating strategy.

We updated gating strategy accordingly (Revised manuscript, page 9, line 361-362).

(10) Line 343-344: Note that Chi3l1 is not exclusively expressed by KCs.

We rephrased our words accordingly (Revised manuscript, page 9, line 374-378).

(11) Lines 355-358: The statement that "sustained glycolytic hyperactivation culminates not in sustained activation, but in apoptotic cell death" is unsupported by data or literature, as macrophage polarization was not analyzed in this study.

We removed the statement from the revised manuscript.

(12) Lines 375-379: Rephrase to clarify that while KCs are metabolically active and glucose-demanding, excessive glycolytic flux accelerates apoptosis.

We have rephrased to clarify (Revised Manuscript, page 10, lines 405-407).

(13) Lines 375-385 & 387-397: Consolidate overlapping statements for conciseness and coherence.

We have consolidate the overlapping statements (Revised manuscript, page 10, lines 405-425).

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eLife Assessment

The present manuscript by Cordeiro et al., shows convincing evidence that α-mangostin, a xanthone obtained from the fruit of the Garcinia mangostana tree, behaves as a strong activator of the large-conductance (BK) potassium channels. The authors suggest that α-mangostin activation of the BK channel is state-independent, and molecular docking and mutagenesis suggest that α-mangostin binds to a site in the internal cavity. Additionally, the authors show that α-mangostin can relax arteries, further suggesting the plausibility of the proposed effects of this compound. These are valuable findings that should be of interest to channel biophysicists and physiologists alike.

Reviewer #1 (Public review):

In this manuscript, the authors aimed to identify the molecular target and mechanism by which α-Mangostin, a xanthone from Garcinia mangostana, produces vasorelaxation that could explain the antihypertensive effects. Building on on prior reports of vascular relaxation and ion channel modulation, the authors convincingly show that large-conductance potassium BK channels are the primary site of action. Using electrophysiological, pharmacological, and computational evidence, the authors achieved their aims and showed that BK channels are the critical molecular determinant of mangostin's vasodiltory effects, even though the vascular studies are quite preliminary in nature.

Strengths:

(1) The broad pharmacological profiling of mangostin across potassium channel families, revealing BK channels - and the vascular BK-alpha/beta1 complex - as the potently activated target in a concentration-dependent manner.

(2) Detailed gating analyses showing large negative shifts in voltage-dependence of activation and altered activation and deactivation kinetics.

(3) High-quality single-channel recordings for open probability and dwell times.

(4) Convincing activation in reconstituted BKα/β1-Caᵥ nanodomains mimicking physiological condition and functional proof-of-concept validation in mouse aortic rings.

Weaknesses are minor:

(1) Some mutagenesis data (e.g., partial loss at L312A) could benefit from complementary structural validation.

The author's rebuttal provides alphafold3 models for mutants. While there are interesting preliminary observations, the authors decided not to include these in the main manuscript, awaiting further structual validation. I concur.

(2) While Cav-BK nanodomains were reconstituted, direct measurement of calcium signals after mangostin application onto native smooth muscle could be valuable.

In their response, the authors acknowledge the importance of measuring Ca2+ sparks in smooth muscle cells to further validate their findings. However, this is not provided in the manuscript. Part of my earlier comment alludes to the possibility of α-Mangostin directly affecting Cav1.2 or ryanodine receptor activity, and therefore BK activity would go up. With the current provided evidence, these possibilities cannot be excluded and need to be acknowledged.

(3) The work has impact for ion channel physiology and pharmacology, providing a mechanistic link between a natural product and vasodilation. Datasets include electrophysiology traces, mutagenesis scans, docking analyses, and aortic tension recordings. The latter however are preliminary in nature.

The authors acknowledge that additional vascular physiology experiments would strengthen the argument they make. They are however unable to provide such evidence in the present manuscript. Therefore, I strongly suggest that the authors tune down the physiological implications of α-Mangostin that they include in the manuscript. I'd also suggest that "vasorelaxation" is removed from the manuscript title, given the preliminary nature of the findings.

Reviewer #2 (Public review):

Summary:

In the present manuscript, Cordeiro et al. show that α-mangostin, a xanthone obtained from the fruit of the Garcinia mangostana tree, behaves as an agonist of the BK channels. The authors arrive at this conclusion by examining the effects of mangostin on macroscopic and single-channel currents elicited by BK channels formed by the α subunit and α + β1 subunits, as well as αβ1 channels coexpressed with voltage-dependent Ca2+ (CaV1,2) channels. The single-channel experiments show that α-mangostin produces a robust increase in the probability of opening without affecting the single-channel conductance. The authors contend that α-mangostin activation of the BK channel is state-independent, and molecular docking and mutagenesis suggest that α-mangostin binds to a site in the internal cavity. Importantly, α-mangostin (10 μM) alleviates noradrenaline-induced contracture. Mangostin is ineffective if the contracted muscles are pretreated with the BK toxin iberiotoxin.

In this revised version of the manuscript by Cordeiro et al., the authors have adequately answered my previous concerns. However, as I stated in my comments, without determining the probability of opening across a wide range of voltages, any conclusion about the drug's mechanism of action can be questioned. For example, the statement in Discussion line 481: "The higher shift observed in 1 μM Cai 2+ may reflect the steep Cai2+-dependence of the closed-open equilibrium (Cui, Cox and Aldrich, 1997) and the allosteric coupling of voltage and Cai2+ signals (Horrigan and Aldrich, 2002; Magleby, 2003; Clay, 2017), which are effective in this concentration range, which may lead to a higher apparent activation when voltage activation is facilitated by Cai 2+ (Sun and Horrigan, 2022)." has no support in the data and is not predicted by the allosteric model. In order to have a larger shift induced by the drug in the presence of Ca2+, you need either to alter the Ca2+ binding or the allosteric coupling factor C.<br /> Please note that in the manuscript, there are several problems with the English in this sentence.

Minor

In Figure 1E, BKa should read BKalpha.

Reviewer #3 (Public review):

Summary:

This research shows that a-mangostin, a proposed nutraceutical, with cardiovascular protecting properties, could act through the activation of large conductance potassium permeable channels (BK). The authors provide convincing electrophysiological evidence that the compound binds to BK channels and induces a potent activation, increasing the magnitude of potassium currents. Since these channels are important modulators of the membrane potential of smooth muscle in vascular tissue, this activation leads to muscle relaxation, possibly explaining cardiovascular protecting effects.

Strengths:

The authors have satisfactorily answered my previous comments and present evidence based on several lines of experiments that a-mangostin is a potent activator of BK channels. The quality of the experiments and the analysis is high and represents an appropriate level of analysis. This research is timely and provides a basis to understand the physiological effects of natural compounds with proposed cardio protective effects.

Weaknesses:

The identification of the binding site continues to be the least developed point of the manuscript. The authors show that the binding site is probably located in the hydrophobic cavity of the pore and show that point mutations reduce the magnitude of the negative voltage shift of activation produces by a-mangostin. This binding site should be demonstrated in the future using structural techniques such as cryo-EM.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors aimed to identify the molecular target and mechanism by which α-Mangostin, a xanthone from Garcinia mangostana, produces vasorelaxation that could explain the antihypertensive effects. Building on prior reports of vascular relaxation and ion channel modulation, the authors convincingly show that large-conductance potassium BK channels are the primary site of action. Using electrophysiological, pharmacological, and computational evidence, the authors achieved their aims and showed that BK channels are the critical molecular determinant of mangostin's vasodilatory effects, even though the vascular studies are quite preliminary in nature.

Strengths:

(1) The broad pharmacological profiling of mangostin across potassium channel families, revealing BK channels - and the vascular BK-alpha/beta1 complex - as the potently activated target in a concentration-dependent manner.

(2) Detailed gating analyses showing large negative shifts in voltage-dependence of activation and altered activation and deactivation kinetics.

(3) High-quality single-channel recordings for open probability and dwell times.

(4) Convincing activation in reconstituted BKα/β1-Ca_v nanodomains mimicking physiological conditions and functional proof-of-concept validation in mouse aortic rings.

We thank the reviewer for acknowledging the strength of the different aspects investigated in our study.

Weaknesses are minor:

(1) Some mutagenesis data (e.g., partial loss at L312A) could benefit from complementary structural validation.

In the attempt to improve structural insight for the presented mutagenesis data, we have used Alphafold3 (AF3; Abramson et al., 2024) to generate models of the I308A, L312M and A316P substitutions and repeated the docking for each (Fig. R1). According to these predictive models,

The I308A substitution considerably straightens the S6 helix starting at this residue. Hence, all residues are displaced relative to the WT: C_a of L312, F315, and A316 are displaced by 2.8 Å, 4.2 Å, and 4.6 Å, respectively, widening the bottom of the binding pocket. However, the prediction confidence is rated lower as in the other AF3 models for all helices (70 > plDDT > 50). In the docking, poses in the binding pocket comparable to these observed in the WT (i.e. involving I308A, L312 and A316) and with the same molecule orientation have higher binding energies (-7.13 to -6.66 kcal mol^-1). Additionally, poses without contact to I308A arise that have a more vertical position, indicating that the structural change affects the binding region.

The changes induced by L312M are localized to residues 313-323, where S6 bends towards S5. Binding energies are lower especially in the best 2 poses that are also most comparable to the WT docking (-9.88 kcal mol^-1), but clustering overall is poor and poses are more heterogeneous. Interactions with L312M are completely abolished, while interactions with I308 (in 11/20 poses), F315 (in all poses), and A316 (in 5/20 poses) persist. Because of the rather small structural alteration induced by the substitution and the variable poses one could speculate that the reduced V_½ shift is due to the observed loss in binding to L312M; however, retained interactions to the other residues would still allow α-Mangostin to activate.

A316P induces a displacement of the S6 helix compared to the WT while the other pore helices are not affected. S6 shows an enhanced outward bending around A316, which results in displacements of residues where a-Mangostin would bind, i.e., the C_a of F315 and L312M are displaced by 2.4 Å and 2.8 Å (I308 is not affected). Residues below are moved in a more rotational way, resulting in a C_a displacement of 3.1 Å for Y318 and even 5.7 Å for V319, before displacements decrease again towards the intracellular helix end. While interactions with A316P are present in 10/20 analyzed poses, the helix displacement seems to hinder I308 and L312 interactions, as the best docked a-Mangostin pose (-8.41 kcal mol^-1) is predicted to only contact F315 and Y318, and overall, any I308 or L312 contacts only occurred in 3/20 and 7/20 poses (wildtype: 17/20 and 20/20 poses). This may hint at a mechanism where A316P probably has a substantial allosteric share in reducing the V_½ shift induced by a-Mangostin and underlines the exceptional effect of this mutation (i.e., complete loss of a V_½ shift).

Author response image 1.

Alphafold3 models of BK I308A, L312M, and A316P with α-Mangostin docked to the mutant structures. The upper row shows an overview of the mutant pore helices (AF3 models) used for molecular docking. The lower row shows the binding region with the wildtype structure overlaid in gray. Only 3 helices are shown for clarity.

Although these results provide interesting tentative explanations for the effect of the mutations and conclusions from AF3 models become increasingly robust, we think that definitive statements of their mechanistic contributions would require experimental studies of mutant channels, i.e., cryo-EM or crystallography, that are beyond our means. Therefore, we have decided not to include this data in the manuscript; however, it is accessible for the interested reader within the public review. Hopefully, as cryo-EM structures have been obtained for the wildtype channel, there will be studies on mutations of this gating-relevant S6 segment in the future.

(2) While Cav-BK nanodomains were reconstituted, direct measurement of calcium signals after mangostin application onto native smooth muscle could be valuable.

We are not sure if a global elevation of cellular calcium concentration would be informative. We rather expect that the relevant local Ca²⁺ elevation would occur as sparks in the BK-Ca_v nanodomains, close to the membrane. We would anticipate a change in spark duration, as the Ca²⁺ inward current would be stopped faster by the enhanced repolarization via a-Mangostin activated BKα/β1 channels. This would require fast Ca²⁺ imaging acquisition speed to capture spark activity. We concur that this would be an informative experiment to investigate a more native situation. However, we would have to accomplish such methodologically challenging measurements in a separate project, which could fruitfully be combined with a more extensive characterization of aortic contraction as also suggested in the following remark (3).

(3) The work has an impact on ion channel physiology and pharmacology, providing a mechanistic link between a natural product and vasodilation. Datasets include electrophysiology traces, mutagenesis scans, docking analyses, and aortic tension recordings. The latter, however, are preliminary in nature.

We completely agree with the reviewer that there is ample room for further studies that could characterize different tissues important in blood pressure regulation (such as resistance arteries), elucidate even more physiological detail (such as modulatory effects of the endothelium), or look deeper into the pharmacology using chemically altered Mangostin derivatives. While we very much like this to happen in future projects, in this study we focused on the functional aspects of a-Mangostin in BK channel gating. We present our tension recordings as a proof-of-concept to underline the activity of a-Mangostin in native tissues, and we clearly show the importance of the BK channel by using iberiotoxin as a specific inhibitor which impressively abolished relaxation.

References:

Abramson, J. et al. (2024) “Accurate structure prediction of biomolecular interactions with AlphaFold 3,” Nature, 630(8016), pp. 493–500. Available at: https://doi.org/10.1038/s41586-024-07487-w.

Reviewer #2 (Public review):

Summary:

In the present manuscript, Cordeiro et al. show that α-mangostin, a xanthone obtained from the fruit of the Garcinia mangostana tree, behaves as an agonist of the BK channels. The authors arrive at this conclusion through the effect of mangostin on macroscopic and single-channel currents elicited by BK channels formed by the α subunit and α + β1 sununits, as well as αβ1 channels coexpressed with voltage-dependent Ca2+ (CaV1,2) channels. The single-channel experiments show that α-mangostin produces a robust increase in the probability of opening without affecting the single-channel conductance. The authors contend that α-mangostin activation of the BK channel is state-independent and molecular docking and mutagenesis suggest that α-mangostin binds to a site in the internal cavity. Importantly, α-mangostin (10 μM) alleviates the contracture promoted by noradrenaline. Mangostin is ineffective if the contracted muscles are pretreated with the BK toxin iberiotoxin.

Strengths:

The set of results combining electrophysiological measurements, mutagenesis, and molecular docking reveals α-mangostin as a potent activator of BK channels and the putative location of the α-mangostin binding site. Moreover, experiments conducted on aortic preparations from mice suggest that α-mangostin can aid in developing drugs to treat a myriad of diverse diseases involving the BK channel.

We thank the reviewer for pointing out the significance of our study.

Weaknesses:

Major:

(1) Although the results indicate that α-mangostin is modifying the closed-open equilibrium, the conclusion that this can be due to a stabilization of the voltage sensor in its active configuration may prove to be wrong. It is more probable that, as has been demonstrated for other activators, the α-mangostin is increasing the equilibrium constant that defines the closed-open reaction (L in the Horrigan, Aldrich allosteric gating model for BK). The paper will gain much if the authors determine the probability of opening in a wide range of voltages, to determine how the drug is affecting (or not), the channel voltage dependence, the coupling between the voltage sensor and the pore, and the closed-open equilibrium (L).

We would like to take the opportunity to clarify this potential misunderstanding. In our manuscript, we have discussed three mechanistic explanations for the Mangostin activation: (1) an electrostatic effect at the selectivity filter, (2) structural and electrostatic changes of S6 that facilitate the opening of a putative lower gate, and (3) hydrophobic gating, i.e., counteracting dewetting of the pore. All possibilities would impact S6 and lower the free energy for pore opening, and we concur that therefore Mangostin most likely affects the closed-open equilibrium (L) of the BKα channel.

The sentence at the original lines 470-471, “(…) caused by an enhanced shift of the closed-open equilibrium toward the open state, such as the stabilization of the voltage sensor in an active conformation” refers to the observation that the presence of the β1 subunit enhances this closed-open shift. The stabilization of the voltage sensor domain was mentioned as one example of how it achieves this. We recognize that this example was an unfortunate choice, as β1 rather facilitates Ca²⁺-dependent allosteric pore opening unrelated to the discussed mechanisms of Mangostin. We have therefore removed this statement.

As to the suggestion to dissect the effect of Mangostin on C, D, and L, we agree with the reviewer that this would surely add to a full biophysical characterization. However, in our project, we strove towards including more experiments showing the physiological implications of Mangostin activation to emphasize the implication for vasodilation. We hope the reviewer understands that, with limited resources, this came at the expense of a full investigation of the different gating components, which could pose a separate project by itself.

(2) Apparently, the molecular docking was performed using the truncated structure of the human BK channel. However, it is unclear which one, since the PDB ID given in the Methods (6vg3), according to what I could find, corresponds to the unliganded, inactive PTK7 kinase domain. Be as it may, the apo and Ca2+ bound structures show that there is a rotation and a displacement of the S6 transmembrane domain. Therefore, the positions of the residues I308, L312, and A316 in the closed and open configurations of the BK channel are not the same. Hence, it is expected that the strength of binding will be different whether the channel is closed or open. This point needs to be discussed.

We apologize for the typing error and thank the reviewer for indicating this erroneous PDB ID. (“6vg3”). It should have read PDB ID 6v3g as in the legend to Fig. 4B. The reviewer appropriately points out that there are differences in the S6 segment addressed in our study between the two available cryo-EM structures obtained in the presence (PDB ID 6v38) and absence of Ca²⁺ (PDB ID 6v3g) (Tao and MacKinnon, 2019).

We had actually performed the docking with both structures, but chosen to show the Ca²⁺-free structure to better visualize the I308 position. a-Mangostin is found in the same S6 region in both, not obstructing the K⁺ conduction pathway. The binding energies of the favored poses are very similar; the binding energy in the best-ranking conformational cluster in the Ca²⁺-bound structure even was slightly lower (-8.64 kcal mol^-1) than in the docking with the Ca²⁺-free channel (-8.58 kcal mol^-1; Fig. 4B), which may not be a relevant difference.

We compared the residue interactions in both dockings (Author response table 1). S317 and Y318, which did not reduce the shift in V_½ upon substitution, were not predicted to contact a-Mangostin in either structure. In both structures, L312 and F315 were predicted to interact in virtually all poses analyzed. In the docking to the Ca²⁺-free state, also I308 was predicted to interact in 17/20 poses, while contacts to A316 occurred in 5/20 poses. In the Ca²⁺-bound state, predicted interactions shifted from I308 (which is expected as it is buried in the protein) to A316, and the isoprenyl moiety close to I308 rotated downwards. This could indicate that a-Mangostin adopts a more horizontal position following the upward reorientation of S6 in the Ca²⁺-bound state when the channel moves from one to the other conformation (Fig. S4).

Author response table 1.

Number of interactions of S6 residues in 20 analyzed α-Mangostin poses in the molecular dockings to the Ca2+-free and Ca2

These docking results are consistent with our functional measurements. Recent structures of the BK/γ1 complex showed that the VSD and Ca²⁺-bowl are stabilized in an active-like conformation that corresponds to the conformation seen in the Ca²⁺-bound state (Kallure et al., 2023; Yamanouchi et al., 2023; Redhardt, Raunser and Raisch, 2024), indicating that very likely the Ca²⁺-bound and Ca²⁺-free structures indeed represent open and closed conformations of the channel. We observed that α-Mangostin can bind to both of these states to activate the channel (Fig. 3C, D), showing the presence of a binding site in both conformations. Further, α-Mangostin induced a left-shift in V_½ also in higher Ca²⁺ concentration (Fig. 2D), indicating that it still binds to and activates the channel after the conformational change in S6. As we could not determine affinity for the mutants due to limited solubility, we have no information on the nature of the contribution of the substitutions, i.e., reduced binding or allosteric effect. As I308 is buried in the Ca²⁺-bound state, its contribution is likely mostly allosteric. We have also proposed dewetting as possible activation mechanism, which we expect to be less sensitive to the exact pose of a molecule (as shown for NS11021, Nordquist et al., 2024). Therefore, α-Mangostin could, e.g., change solvent accessibility of the I308 sidechain, energetically favoring the buried (open) state.

We have now included both dockings and Author response table 1 in Fig. S4, and we have added passages to the results section (starting at line 373) and discussion section (starting at lines 544, 588).

Minor:

(1) From Figure 3A, it is apparent that the increase in Po is at the expense of the long periods (seconds) that the channel remains closed. One might suggest that α-mangostin increases the burst periods. It would be beneficial if the authors measured both closed and open dwell times to test whether α-mangostin primarily affects the burst periods.

We thank the reviewer for this valuable suggestion, which we have implemented. In our single channel measurements shown in our original Fig. 3 we have not observed burst behavior of the BKɑ channels. This can be explained by the fact that we measured in resting condition (100 nM free Ca_i</sup>2+</sup>) and with rather mild depolarisation (+40 mV) where Po was very low. We have therefore analyzed measurements in 5 µM free a_i</sup>2+</sup> where we recorded sufficient burst activity also in the basal state.

The burst analysis showed that ɑ-Mangostin indeed prolongs bursts and shortens the interburst closures. Within bursts, both closed times and open times were increased, and we recorded a higher number of opening events per burst. We conclude that ɑ-Mangostin acts in both the closed and the open state, where it slows open-closed transitions resulting in less flicker, and stabilizes the open state via longer open times and a higher probability for closed-open transitions.

We now show this data in Fig. 3D-F and Table S8, and have accordingly added passages to the results section (starting at line 285), the discussion (line 510), and the methods section (starting at line 746).

(2) In several places, the authors make similarities in the mode of action of other BK activators and α-mangostin; however, the work of Gessner et al. PNAS 2012 indicates that NS1619 and Cym04 interact with the S6/RCK linker, and Webb et al. demonstrated that GoSlo-SR-5-6 agonist activity is abolished when residues in the S4/S5 linker and in the S6C region are mutated. These findings indicate that binding of the agonist is not near the selectivity filter, as the authors' results suggest that α-mangostin binds.

We will gladly clarify our ideas concerning the binding sites of other activators and ɑ-Mangostin. We first hypothesized that ɑ-Mangostin may share characteristics and mode of action with the class of negatively charged activators (NCA) that we have described before (Schewe et al., 2019). NCA were found to occupy a common fenestration site that is located close to the selectivity filter in TREK K2P channels, and in this manuscript we have shown by THexA competition and mutagenesis experiments that ɑ-Mangostin also binds in this fenestration region in TREK-1 channels (Fig. S3).

The existence of this common NCA binding site was also proposed for BK channels, as a docking placed the NCA NS11021 in an equivalent binding region, and, among others, NS11021 and GoSlo-SR-5-6 competed with THexA for binding in the pore (Schewe et al., 2019). These results were indeed not fully in agreement with the proposed binding site of GoSlo-SR-5-6 in Webb et al. (2015), although the most effective (double) mutants were located at S317 and I323, at the intracellular end of the cleft between neighboring S6 segments. In this manuscript, we have shown that α-Mangostin is present in the pore of BK channels by molecular docking, a THexA competition assay, and two mutations that reduced the shift in V_½ induced not only by ɑ-Mangostin but also by GoSlo-SR-5-6 (Fig. 4). While the docking was rather a starting point, both functional tests argue against a binding site in the S4/5 linker/S6C region; however, allosteric mechanisms could still reduce activation also in mutants in the S4/5 linker/S6C region far from the pore binding region proposed by us in the 2019 study and the present manuscript.

To summarize, we did not mean to imply that all BK activators should bind to this site, especially if they are not part of the NCA class (as NS1619, Cym4, as well as BC5, whose different binding site enabled us to use it as a control in our THexA competition assay). However, the cleft close to gating relevant S6 residues may well pose a region especially susceptible to modulator binding (as BL-1249, GoSlo-SR-5-6, and ɑ-Mangostin). We have moved, respectively separated, the initial GoSlo references from the reference to the pore binding site in the paragraph (lines329, 358) to improve clarity.

(3) The sentence starting in line 452 states that there is a pronounced allosteric coupling between the voltage sensors and Ca2+ binding. If the authors are referring to the coupling factor E in the Horrigan-Aldrich gating model, the references cited, in particular, Sun and Horrigan, concluded that the coupling between those sensors is weak.

We are grateful for the opportunity to improve this passage. We intended to express that observed effects (in this case the shift in V_½) are pronounced around 1 µM Ca²⁺. As the reviewer states, the coupling factor between the voltage and calcium sensors (E; 2.4) is weak compared to the coupling of Ca²⁺ (C; 8) and voltage (D; 25) to the pore in the Horrigan-Aldrich model. However, the shape of the Ca²⁺-dependence of V_½ cannot be completely described when E is neglected, with the highest difference around 1-2 µM Ca²⁺ (Horrigan and Aldrich, 2002). Deletion of the gating ring underlines the allosteric sensor coupling (Clay, 2017). This together with the steep Ca²⁺-dependence in this concentration range (meaning high Po changes upon occupancy increase; Cui, Cox and Aldrich, 1997) explains the higher apparent activation, visible as the higher shift in V_½ observed at the 1 µM Ca²⁺. Speaking with the model of Sun and Horrigan (2022), the suppressing “molecular logic gate” is already relieved by the presence of intermediate Ca²⁺, and the direct “gating lever” pathway via voltage acts synergistically and achieves the observed higher V_½ shift upon depolarization. We have adapted the sentence and separated the citations for better understanding (lines 503-507).

References:

Clay, J.R. (2017) “Novel description of the large conductance Ca2+-modulated K+ channel current, BK, during an action potential from suprachiasmatic nucleus neurons,” Physiological Reports, 5(20), p. e13473. Available at: https://doi.org/10.14814/phy2.13473.

Cui, J., Cox, D.H. and Aldrich, R.W. (1997) “Intrinsic Voltage Dependence and Ca2+ Regulation of mslo Large Conductance Ca-activated K+ Channels,” Journal of General Physiology, 109(5), pp. 647–673. Available at: https://doi.org/10.1085/jgp.109.5.647.

Horrigan, F.T. and Aldrich, R.W. (2002) “Coupling between voltage sensor activation, Ca2+ binding and channel opening in large conductance (BK) potassium channels,” The Journal of General Physiology, 120(3), pp. 267–305. Available at: https://doi.org/10.1085/jgp.20028605.

Kallure, G.S. et al. (2023) “High-resolution structures illuminate key principles underlying voltage and LRRC26 regulation of Slo1 channels.” bioRxiv, p. 2023.12.20.572542. Available at: https://doi.org/10.1101/2023.12.20.572542.

Nordquist, E.B., Jia, Z., Chen, J., 2024. “Small Molecule NS11021 Promotes BK Channel Activation by Increasing Inner Pore Hydration.” J. Chem. Inf. Model. 64, 7616–7625. https://doi.org/10.1021/acs.jcim.4c01012

Redhardt, M., Raunser, S. and Raisch, T. (2024) “Cryo-EM structure of the Slo1 potassium channel with the auxiliary γ1 subunit suggests a mechanism for depolarization-independent activation,” FEBS Letters, 598(8), pp. 875–888. Available at: https://doi.org/10.1002/1873-3468.14863.

Schewe, M. et al. (2019) “A pharmacological master key mechanism that unlocks the selectivity filter gate in K + channels.,” Science, 363(6429), pp. 875–880. Available at: https://doi.org/10.1126/science.aav0569.

Sun, L. and Horrigan, F.T. (2022) “A gating lever and molecular logic gate that couple voltage and calcium sensor activation to opening in BK potassium channels,” Science Advances, 8(50), p. eabq5772. Available at: https://doi.org/10.1126/sciadv.abq5772.

Tao, X. and MacKinnon, R. (2019) “Molecular structures of the human Slo1 K+ channel in complex with β4,” eLife 8, p. e51409. Available at: https://doi.org/10.7554/eLife.51409.

Webb, T.I. et al. (2015) “Molecular mechanisms underlying the effect of the novel BK channel opener GoSlo: Involvement of the S4/S5 linker and the S6 segment,” Proceedings of the National Academy of Sciences, 112(7), pp. 2064–2069. Available at: https://doi.org/10.1073/pnas.1400555112.

Yamanouchi, D. et al. (2023) “Dual allosteric modulation of voltage and calcium sensitivities of the Slo1-LRRC channel complex,” Molecular Cell, 83(24), pp. 4555-4569.e4. Available at: https://doi.org/10.1016/j.molcel.2023.11.005.

Reviewer #3 (Public review):

Summary:

This research shows that a-mangostin, a proposed nutraceutical, with cardiovascular protective properties, could act through the activation of large conductance potassium permeable channels (BK). The authors provide convincing electrophysiological evidence that the compound binds to BK channels and induces a potent activation, increasing the magnitude of potassium currents. Since these channels are important modulators of the membrane potential of smooth muscle in vascular tissue, this activation leads to muscle relaxation, possibly explaining cardiovascular protective effects.

Strengths:

The authors present evidence based on several lines of experiments that a-mangostin is a potent activator of BK channels. The quality of the experiments and the analysis is high and represents an appropriate level of analysis. This research is timely and provides a basis to understand the physiological effects of natural compounds with proposed cardio-protective effects.

We sincerely thank the reviewer for appraising the achievements of our study.

Weaknesses:

The identification of the binding site is not the strongest point of the manuscript. The authors show that the binding site is probably located in the hydrophobic cavity of the pore and show that point mutations reduce the magnitude of the negative voltage shift of activation produced by a-mangostin. However, these experiments do not demonstrate binding to these sites, and could be explained by allosteric effects on gating induced by the mutations themselves.

We are aware that our functional data are unfortunately not sufficient to clearly distinguish between effects due to affinity loss or due to allosteric mechanisms. Our attempts to generate complete dose–response curves for the mutants to determine accurate apparent IC₅₀ values were unfortunately limited by the solubility of the compound. Consequently, we have avoided making claims about affinity loss in the mutant analysis, and have instead only reported the reduction in potency, expressed as the shift in V_½. To reduce confounding effects from the mutations themselves, we selected substitutions that preserved the most wildtype-like GV-relationships, based on the extensive mutagenesis work of (Chen, Yan and Aldrich, 2014). We address this matter also in our answer to Recommendation (6) below, and we have replaced the word “binding” in the title of the manuscript. Nevertheless, we consider the proposed binding region to be well supported by the THexA competition experiments in combination with molecular docking, even though the specific mechanistic contributions of individual residues cannot yet be resolved.

Reviewer #3 (Recommendations for the authors):

(1) Natural xanthones as α-Mangostin induce vasorelaxation via binding to key gating residues in the S6 domain of BK channels.

(2) If α-Mangostin occupies a similar binding site to quaternary ammoniums, what is the explanation for not observing a reduction in the single-channel current (fast blocking effect)? The α-Mangostin site proposed here is in a region of the channel that should occlude ion permeation. The authors should discuss possible explanations for this apparently contradictory observation.

As the reviewer states, we indeed have not observed a reduced single channel amplitude in any measurement. The THexA competition assay showed that ɑ-Mangostin is present in the pore cavity and interferes with THexA access to its binding site. However, we do not think that their binding sites are similar, as QA ions bind directly below the filter entrance to block permeation, while our studies suggest that ɑ-Mangostin binds in the upper portion of the cleft between S6 helices. In this position, it would clearly overlap with the QA binding site and hinder access, but not block permeation. We would therefore not expect to see an amplitude reduction by intermittent α-Mangostin block. Consistently, all binding poses in our dockings were close to the cavity wall, without interfering with the central ion conduction pathway. To better illustrate this, we have added updated intracellular views of the dockings in the Ca²⁺-free and Ca²⁺-bound state (which we have also now included as suggested by another reviewer) to the supplementary information (Fig. S4A).

(3) In Figure 2D, it is difficult to appreciate the differences between the symbols representing the G-V relationships of BKa channels at different intracellular Ca concentrations, before and after activation with 10 μM a-Mangostin. A clearer distinction between the curves would help to interpret the data more easily.

We thank the reviewer for the suggestion to improve figure accessibility. We have changed the line appearance for better discrimination of the overlying portions.

(4) Both THexA and TPA block BK channels through voltage and state-dependent mechanisms. Therefore, their apparent affinity could change if a-Mangostin simply increases open probability or alters dwell times rather than physically blocking access to the binding site.

The reviewer addresses valid limitations that can affect the meaningfulness of competition experiments under certain conditions. However, we think that this does not apply to our results:

Previous studies have shown that the voltage dependence of quaternary ammonium blockers up to C₁₀ is rather weak in BK channels, and only a slight increase in block is present in the voltage range +30 mV to +100 mV (Li and Aldrich, 2004; Thompson and Begenisich, 2012). Hence, THexA voltage dependence has already reached a plateau in the competition assay (at +40 mV), and its voltage dependence would have little effect on our results.

Controversy exists about the nature of the state dependence of different quaternary ammonium blockers, but TBA is often recognized as an open channel blocker of BK channels, which probably also applies to THexA (Wilkens and Aldrich, 2006; Tang, Zeng and Lingle, 2009; Thompson and Begenisich, 2012; Posson, McCoy and Nimigean, 2013). Assuming such an open-channel block, apparent IC₅₀ values would be inversely proportional to Po. The THexA IC₅₀ was about 80 nM in the basal state, when Po is very low (0.024 at +40 mV as derived from the GV-relationship); an increase of open dwell times, respectively Po, in the presence of α-Mangostin to, e.g., 0.3 would therefore lead to a ≈10-fold decrease in apparent IC₅₀. However, the apparent THexA IC₅₀ strongly increased rather than decreased (more than 20-fold to around 1.6 µM). This cannot arise from Po change and must reflect the altered access of THexA to its binding site caused by α-Mangostin. Assuming a pure closed channel block where apparent IC₅₀ would correlate with the closed times, an increase of about 1.4-fold is expected. However, we recorded a much stronger 20-fold increase. Therefore, we are convinced that we have conclusively shown that α-Mangostin is present in the BK pore irrespective of the state dependence of THexA block.

(5) The pH dependence of the V1/2 shift supports the idea that α-Mangostin becomes more negatively charged at higher pH (enhancing its effect.) However, although the data are consistent with this interpretation, additional controls such as using a non-ionizable analog or assessing solubility changes with pH would be needed to confirm that the shift is caused specifically by ionization of α-Mangostin and not by indirect pH effects on channel gating.

We agree with the reviewer that the pH experiment by itself is not sufficient to clearly tie the existence of a charge to a possible activation mechanism. We still think that this is an interesting observation and should be made known, as we have investigated the mechanism of negatively charged activators in different K⁺ channel families before (Schewe et al., 2019). Unfortunately, we do not have access to uncharged derivatives mimicking the 3D conformation. From the commercially available substances, the bare xanthone backbone is completely insoluble in water. We have therefore tested the derivative 3-hydroxyxanthone as example with a minimal number of hydroxyl substituents (Author response image 2, Author response table 2 ). The 3-hydroxyxanthone indeed shows reduced activation compared to α-Mangostin. The shift in V_½ induced by 10 µM 3-hydroxyxanthone was only 14.99 ± 5.67 mV (≈50 mV for α-Mangostin). This supports that the presence of several (potentially) charged substituents is important for the activation mechanism. However, we have no knowledge about the efficacy of the compound or the local pK_a of the different hydroxyl groups. As the reviewer stated, systematic chemical modifications would be necessary to elucidate the importance of the charged substituent number and positions, which is not within our capabilities.

Author response image 2.

Activation of BKα by 3-hydroxyxanthone. (A) GV-relationship before and after application of 10 µM 3-hydroxyxanthone. (B) V_½ before and after application of 10 µM 3-hydroxyxanthone compared to α-Mangostin and the resulting difference in V_½ (ΔV_½). Measurements were conducted as described in the main manuscript with 100 nM free Ca_i²⁺.

Author response table 2.

Comparison of the V_½ ± SEM and ΔV_½ ± SEM before and after activation by 10 µM α-Mangostin or 10 µM 3-hydroxyxanthone in BKα channels. Unpaired t-test, two-tailed P values (α=0.05)

(6) The reduced V1/2 shifts observed in the I308A, L312M, and A316PP mutants may result from intrinsic gating alterations rather than a true loss of a-Mangostin binding. The GoSlo-SR-5-6 control is informative, but the persistence of activation in A316P does not fully resolve this. A more convincing test would be employing double or triple mutants.

As stated above, we acknowledge that our functional data do not allow us to definitively separate effects arising from a true loss of binding affinity from those due to potential allosteric effects. We tried to minimize intrinsic gating alteration brought by substitutions by not conducting a pure alanine or cysteine scanning mutagenesis. Instead, substitutions were chosen to be closest to the wildtype GV-relationship in (Chen, Yan and Aldrich, 2014) where possible. While L312M was virtually identical to the wildtype, A316P showed a change in slope in high Ca²⁺ concentrations, which could indicate a changed voltage sensitivity. Additionally, A316P completely abolished α-mangostin activation. We therefore also used A316G to ensure that the channel is functional and retains voltage sensitivity, even if its V_½ was shifted stronger. As we have conducted paired measurements and assessed the V_½ before and after activation, we are confident that we can attribute a reduced shift to the reduced action of α-mangostin.

Following the reviewer’s suggestion, we have generated and measured the double mutants I308A/L312M, I308A/A316G, and L312M/A316G (the triple mutant I308A/L312M/A316G did not produce measurable currents). The mutants I308A/L312M and I308A/A316G showed a moderate energy-additive effect and reduced the shift in V_½ by further ≈7 mV compared to the single mutation with the stronger shift. The combination L312M/A316G, however, did not further reduce the shift seen in the single mutations and did not even produce the shift induced by A316G alone.

Author response image 3.

Double Mutants I308A/L312M, I308A/A316G and L312M/A316G compared to the single mutations in the main manuscript. The V½ before and after activation with 10 µM α-Mangostin, the resulting shift in V½, and the GV-relationships are shown (n=6-7), measurements were made as in Fig. 4.

Author response table 3.

Summary of the V_½ before and after Mangostin activation and the resulting shifts in V_½ for the double mutants compared to the single mutants shown in the main manuscript.

Following a suggestion by another reviewer, we have generated Alphafold3 (AF3) models for I308A, L312M and A316P and repeated the Mangostin docking. We learned that the mutations are all predicted to substantially impact the structure of the S6 helix, therefore altering the binding region, and A316P especially impacted the nature of residue interactions. This could be an explanation why the double mutants do not show a clear and consistent additive effect.

Unfortunately, this outcome is not conclusive and the double mutants do not reveal further information compared to the single mutants. We have therefore decided not to include these measurements in the manuscript.

As we do not know if our answers will be sent to all reviewers, we repeat the relevant part about the AF3 models here:

(…) According to these predictive models,

The I308A substitution considerably straightens the S6 helix starting at this residue. Hence, all residues are displaced relative to the WT: C_a of L312, F315, and A316 are displaced by 2.8 Å, 4.2 Å, and 4.6 Å, respectively, widening the bottom of the binding pocket. However, the prediction confidence is rated lower as in the other AF3 models for all helices (70 > plDDT > 50). In the docking, poses in the binding pocket comparable to these observed in the WT (i.e. involving I308A, L312 and A316) and with the same molecule orientation have higher binding energies (-7.13 to -6.66 kcal mol^-1). Additionally, poses without contact to I308A arise that have a more vertical position, indicating that the structural change affects the binding region.

The changes induced by L312M are localized to residues 313-323, where S6 bends towards S5. Binding energies are lower especially in the best 2 poses that are also most comparable to the WT docking (-9.88 kcal mol^-1), but clustering overall is poor and poses are more heterogeneous. Interactions with L312M are completely abolished, while interactions with I308 (in 11/20 poses), F315 (in all poses), and A316 (in 5/20 poses) persist. Because of the rather small structural alteration induced by the substitution and the variable poses one could speculate that the reduced V_½ shift is due to the observed loss in binding to L312M; however, retained interactions to the other residues would still allow α-Mangostin to activate.

A316P induces a displacement of the S6 helix compared to the WT while the other pore helices are not affected. S6 shows an enhanced outward bending around A316, which results in displacements of residues where a-Mangostin would bind, i.e., the C_a of F315 and L312M are displaced by 2.4 Å and 2.8 Å (I308 is not affected). Residues below are moved in a more rotational way, resulting in a C_a displacement of 3.1 Å for Y318 and even 5.7 Å for V319, before displacements decrease again towards the intracellular helix end. While interactions with A316P are present in 10/20 analyzed poses, the helix displacement seems to hinder I308 and L312 interactions, as the best docked a-Mangostin pose (-8.41 kcal mol^-1) is predicted to only contact F315 and Y318, and overall, any I308 or L312 contacts only occurred in 3/20 and 7/20 poses (wildtype: 17/20 and 20/20 poses). This may hint at a mechanism where A316P probably has a substantial allosteric share in reducing the V_½ shift induced by a-Mangostin and underlines the exceptional effect of this mutation (i.e., complete loss of a V_½ shift). (…)

(7) The subtraction approach used to isolate BK currents (difference before and after a-Mangostin) assumes that the compound affects only BK channels. However, a-Mangostin could also modulate Cav currents directly, as reported for other polyphenolic compounds. No vehicle (DMSO) control is shown.

We agree with the reviewer that α-Mangostin could also modulate Ca_v currents; however, this would not interfere with the conclusions drawn from this nanodomain experiment. We intended to show the overall current modulation by ɑ-Mangostin in the voltage range relevant for Ca_v-BK coupling, as this would be the determinant for the membrane potential mediating the vasoactive effect. In native tissue, BK and Ca_v channels (among others) would likewise contribute to the net membrane conductance, with BK channels being a major contributor when activated. In fact, a concomitant inhibition of Ca_v channels could act synergistically in favor of vasodilation. This could therefore be a subject for the further investigation of potential ɑ-Mangostin targets. However, the fact that iberiotoxin prevented relaxation in aortic preparations conclusively showed that BK channels are the major player in native tissue.

We have reformulated some sentences to prevent misunderstandings that we refer to isolated BK currents instead of α-Mangostin activated currents.

DMSO controls were conducted and did not impact BK or Ca_v1.2 currents or the aortic tissue contraction. We have added representative measurements as Fig. S6 and stated the DMSO concentration in the Methods section (line 655).

(8) Most kinetic fits were obtained at strong depolarizations (around +100 mV), which limits how well these results can be extrapolated to physiological voltages. Although the BK-Cav experiments show facilitation between -50 and +50 mV, providing plots for activation and deactivation in that range would strengthen the physiological relevance.

We thank the reviewer for this valuable suggestion. We now additionally show that the impact of ɑ-Mangostin on activation is high at lower depolarisation, indeed underlining its physiological relevance. To address the activation time course in a more physiological voltage range, we have used our measurements of BKɑ channels in 10 µM Ca_i</sup>2+</sup> (where the V_½ shift induced by ɑ-Mangostin is equal to 100 nM ca_i²⁺+; Fig. 2D). The outward currents already present in the lower voltage range under these conditions allowed us to fit a monoexponential function to the traces of 0 mV to 100 mV prepulses. The τ of activation decreased from 29.6 ± 3.1 ms at 0 mV to 2.4 ± 2 ms at +100 mV. After ɑ-Mangostin activation, the time course was accelerated, with a τ of activation of 9.5 ± 4.7 ms at 0 mV to 2 ± 0.6 ms at +100 mV. This faster activation was particularly effective in the lower voltage range far from high Po, e.g., ɑ-Mangostin caused a decrease of more than half of the τ of activation at +20 mV (from 12.2 ± 0.6 ms to 4.98 ± 1.6 ms).

Our data consists of families of different prepulse voltages and a fixed repolarisation step (to -50 mV for 100 nM free Ca_i²⁺, and to -100 mV for 10 µM free Ca_i²⁺). Thus, we are not able to add plots for the voltage-dependence of deactivation in the same way as for activation. However, we can present the deactivation time constants of lower prepulse voltage steps that produce outward currents in symmetrical ion conditions with 10 µM free Ca_i</sup>2+</sup>. For -20 mV and +20 mV prepulse voltages, which better reflect physiological depolarisation, the deactivation time constant shows a 3-to 5-fold increase after ɑ-Mangostin activation.

We now show the plot for the voltage dependence of activation in Fig. S2A and a bar graph for activation/ deactivation time constants at +20 mV as Fig. S2B; data are summarized in Table S5. We hope this adds to illustrating the effect of ɑ-Mangostin under physiological conditions.

(9) Minor: In several parts of the paper, induced shifts to negative voltages are referred to "leftward shifts". It would be useful to be consistent and employ a more specific reference to negative or positive directions.

We thank the reviewer for the careful reading and have harmonized the terminology.

References

Chen, X., Yan, J. and Aldrich, R.W. (2014) “BK channel opening involves side-chain reorientation of multiple deep-pore residues,” Proceedings of the National Academy of Sciences, 111(1), pp. E79–E88. Available at: https://doi.org/10.1073/pnas.1321697111.

Li, W. and Aldrich, R.W. (2004) “Unique Inner Pore Properties of BK Channels Revealed by Quaternary Ammonium Block,” Journal of General Physiology, 124(1), pp. 43–57. Available at: https://doi.org/10.1085/jgp.200409067.

Posson, D.J., McCoy, J.G. and Nimigean, C.M. (2013) “The voltage-dependent gate in MthK potassium channels is located at the selectivity filter,” Nature Structural & Molecular Biology, 20(2), pp. 159–166. Available at: https://doi.org/10.1038/nsmb.2473.

Schewe, M. et al. (2019) “A pharmacological master key mechanism that unlocks the selectivity filter gate in K + channels.,” Science, 363(6429), pp. 875–880. Available at: https://doi.org/10.1126/science.aav0569.

Tang, Q.-Y., Zeng, X.-H. and Lingle, C.J. (2009) “Closed-channel block of BK potassium channels by bbTBA requires partial activation,” The Journal of General Physiology, 134(5), pp. 409–436. Available at: https://doi.org/10.1085/jgp.200910251.

Thompson, J. and Begenisich, T. (2012) “Selectivity filter gating in large-conductance Ca2+-activated K+ channels,” Journal of General Physiology, 139(3), pp. 235–244. Available at: https://doi.org/10.1085/jgp.201110748.

Wilkens, C.M. and Aldrich, R.W. (2006) “State-independent block of BK channels by an intracellular quaternary ammonium.,” The Journal of General Physiology, 128(3), pp. 347–364. Available at: https://doi.org/10.1085/jgp.200609579.

eLife Assessment

This study introduces a valuable toolkit for zebrafish transgenesis, significantly enhancing the flexibility and efficiency of transgene generation for immunological applications. The authors provide convincing evidence through well-designed experiments, demonstrating the toolkit's utility in generating diverse and functional transgenic lines.

Reviewer #1 (Public review):

Summary:

The authors introduce ImPaqT, a modular toolkit for zebrafish transgenesis, utilizing the Golden Gate cloning approach with the rare-cutting enzyme PaqCI. The toolkit is designed to streamline the construction of transgenes with broad applications, particularly for immunological studies. By providing a versatile platform, the study aims to address limitations in generating plasmids for zebrafish transgenesis.

Strengths:

The ImPaqT toolkit offers a modular method for constructing transgenes tailored to specific research needs. By employing Golden Gate cloning, the system simplifies the assembly process, allowing seamless integration of multiple genetic elements while maintaining scalability for complex designs. The toolkit's utility is evident from its inclusion of a diverse range of promoters, genetic tools, and fluorescent markers, which cater to both immunological and general zebrafish research needs. Even small DNA fragements, such as the viral 2a sequence, can be cloned into a multi-component plasmid in one step. The components can be assembled from PCR fragments or synthesized DNA fragments, forgoing the need for "entry" vectors. Further, the authors show that the exisiting PaqCI sites can be domesticated to improve the versatility of the system. The validation provided in the manuscript is Convincing, demonstrating the successful generation of several functional transgenic lines. These examples highlight the toolkit's efficacy, particularly for immune-focused applications.

Comments on revisions:

The authors have addressed all the concerns raised in the first review. Congratulations to the authors for their effort.

Reviewer #2 (Public review):

Summary:

Hurst et al. developed a new Tol2-based transgenesis system, ImPaqT, an Immunological toolkit for PaqCl-based Golden Gate Assembly of Tol2 Transgenes, to facilitate the production of transgenic zebrafish lines. This Golden Gate assembly-based approach relies on only a short 4-base-pair overhang sequence in the final construct, and the insertion construct and backbone vector can be assembled in a single-tube reaction using PaqCl and a ligase. This approach can also be expandable by introducing new overhang sequences while maintaining compatibility with existing ImPaqT constructs, allowing users to add fragments as needed.

The generation of several transgenic zebrafish lines for immunological studies demonstrates the feasibility of the ImPaqT in vivo. Lineage tracing of macrophages via LPS injection demonstrates the approach's functionality and validates its use in vivo.

Comments on revisions:

The authors have addressed all my concerns.

Author Response:

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

We thank the reviewers and editors for their careful reading of our manuscript and thoughtful comments on it. We appreciate the overall positive opinion on our manuscript and helpful comments and suggestions from the reviewers. Overall, the main points identified by reviewers were 1) further broadening of the system to a range of inputs as well as the construct types that can be generated with the system and 2) Further consideration of any off-target joining or off-target effects on genes/proteins and the limits to the expandability of the kit. To address these concerns, we have added new data in Figure 6, illustrating the generation of a new construct using PCR and dsDNA fragments, new constructs for mpeg1.1 and for CRISPR gRNA expression and have revised the text to further address concerns and limitations of the toolkit. We thank the reviewers and editors for these suggestions and feel that they have substantially improved the manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors introduce ImPaqT, a modular toolkit for zebrafish transgenesis, utilizing the Golden Gate cloning approach with the rare-cutting enzyme PaqCI. The toolkit is designed to streamline the construction of transgenes with broad applications, particularly for immunological studies. By providing a versatile platform, the study aims to address limitations in generating plasmids for zebrafish transgenesis.

Strengths:

The ImPaqT toolkit offers a modular method for constructing transgenes tailored to specific research needs. By employing Golden Gate cloning, the system simplifies the assembly process, allowing seamless integration of multiple genetic elements while maintaining scalability for complex designs. The toolkit's utility is evident from its inclusion of a diverse range of promoters, genetic tools, and fluorescent markers, which cater to both immunological and general zebrafish research needs. Furthermore, the modular design ensures expandability, enabling researchers to customize constructs for diverse experimental designs. The validation provided in the manuscript is solid, demonstrating the successful generation of several functional transgenic lines. These examples highlight the toolkit's efficacy, particularly for immune-focused applications.

We appreciate the overall positive evaluation of our toolkit and the time and effort in evaluating it.

Weaknesses:

While the toolkit's technical capabilities are well-demonstrated, there are several areas where additional validation and examples could enhance its impact. One limitation is the lack of data showing whether the toolkit can be directly used for rapid cloning and testing of enhancers or promoters, particularly cloning them directly from PCR using PaqCI overhangs without needing an entry vector. Similarly, the feasibility of cloning genes directly from PCR products into the system is not demonstrated, which would significantly increase the utility for researchers working with genomic elements.

This is an excellent point. Given the increased use of gene synthesis and dsDNA fragments, we also thought it was good to demonstrate incorporation of these as well. We have added a new figure, Figure 6, which demonstrates generation of two new transgene constructs constructed by direct cloning of three PCR products along with a synthetic dsDNA fragment into a Tol2 flanked backbone plasmid as an alternative, rapid approach to generation of transgenes. The resulting plasmids, encoding the mpeg1.1. promoter, a separate p2a, and a tdTomato fluorescent protein along with either wildtype or dominant negative rac2 were properly assembled and in transient transgenic zebrafish injected with these constructs, dominant negative rac2 prevented macrophage recruitment to tail wounds, indicating that this approach worked for the generation of functional transgenes. These results are discussed in new text (lines 304-391) describing this new experiment and the finding that both PCR products and synthesized dsDNA could be efficiently incorporated in constructions generated with our approach as well as in the discussion (lines 494-499).

The authors discuss potential applications such as using the toolkit for tissue-specific knockout applications by assembling CRISPR/Cas9 gRNA constructs. However, they do not demonstrate the cloning of short fragments, such as gRNA sequences downstream of a U6 promoter, which would be an important proof-of-concept to validate these applications. Furthermore, while the manuscript focuses on macrophage-specific promoters, the widely used mpeg1.1 promoter is not included or tested, which limits the toolkit's appeal for researchers studying macrophages and microglia.

Yes, in the new figure described above, we have now shown that this method works with shorter PCR fragments such as the p2a fragment cloned within the tdTomato-p2a-rac2 constructs described above. This fragment is ~70 bp and while this is somewhat longer than a simple gRNA targeting sequence (though smaller than a complete sgRNA), we believe that this indicates that smaller size fragments can still be incorporated within these constructs. We also agree with the general idea of increasing functionality to incorporate CRISPR/Cas9 and now include a 3E encoding the zebrafish U6 promoter. As CRISPR expression constructs frequently incorporate complex construction, for instance, expression of tagged Cas9 along with the U6 driven gRNA as in Zhou et al., 2018 or along with rescue constructs as in Wang et al., 2021, we have given these constructs the non-standard 5’ end O3c, to enable multiplexing in these complex constructs.

We agree that it is important to include mpeg1.1, given the broad use of this promoter within the field, we’ve now included an 5E mpeg1.1 construct within the toolkit.

Another potential limitation is the handling of sequences containing PaqCI recognition sites. Although the authors discuss domestication to remove these sites, a demonstration of cloning strategies for such cases or alternative methods to address these challenges would provide practical guidance for users.

Absolutely, we have now included a new figure (Supplementary Figure 6) that illustrates one domestication approach using PCR and homology-based cloning as an easy approach to domestication. In addition, we have also mentioned alternative approaches for domestication in the discussion (lines 439-444).

Reviewer #2 (Public review):

Summary:

Hurst et al. developed a new Tol2-based transgenesis system ImPaqT, an Immunological toolkit for PaqCl-based Golden Gate Assembly of Tol2 Transgenes, to facilitate the production of transgenic zebrafish lines. This Golden Gate assembly-based approach relies on only a short 4-base pair overhang sequence in their final construct, and the insertion construct and backbone vector can be assembled in a single-tube reaction using PaqCl and ligase. This approach can also be expandable by introducing new overhang sequences while maintaining compatibility with existing ImPaqT constructs, allowing users to add fragments as needed.

Strengths:

The generation of several lines of transgenic zebrafish for the immunologic study demonstrates the feasibility of the ImPaqT in vivo. The lineage tracing of macrophages by LPS injection shows this approach's functionality, validating its usage in vivo.

We appreciate the positive sentiments for our toolkit and the effort put into reviewing our manuscript.

Weaknesses:

(1) There is no quantitative data analysis showing the percentage of off-target based on these 4bp overhang sequences.

While we agree that this is an important variable for the method, we feel that previous studies that have broadly tested off-target effects of all potential 4 bp overhang sequences have already given an effective overview of interactions between each of these overhangs (Potapov et al., 2018; Pryor et al., 2020). The results from these studies were incorporated into the NEB ligase fidelity viewer that we used to predict the overhangs that would have minimal off-target with each other: the tool also reports the expected off-target ligation of individual 4 bp overhangs. In all cases, we selected overhangs that would have minimal off-target efficiency, with each of the overhangs showing 1% or less off-target ligation with any of the other overhangs chosen. We have added new text, lines 119-124, that further clarifies that our selection for these ends.

(2) There is no statement for the upper limitation of the expandability.

Yes, we’ve been curious as well. While our cloning of 6 distinct fragments in Figure 5 and a new 5 fragment cloning added in revision seen in Figure 6, suggests that 5-6 fragments can be readily assembled, in the course of revisions we also attempted to generate a larger product of 11 fragments that ultimately failed. While the 11 fragment construct was unsuccessful, it is unclear whether this is due to the constructs chosen, the potential size of the plasmid or due to a failure of the technique/enzymes themselves. Given that published descriptions of PaqCI Golden Gate cloning approaches have found that PaqCI can assemble at least 32 fragments and can produce large sequences (e.g. in Sikkema et al., 2023, where they assemble the ~40 kbp T7 genome from 12, 24 and 32 distinct fragments using a PaqCI Golden Gate reaction), we suspect that our issues with the 11 fragment assembly are likely due to complications with the specific group of constructs that were combined, however, we have not been able to exhaustively test a range of constructs and assemblies of varying complexity levels. To recognize this, we have added additional text (lines 490-493) to the discussion describing that we have only combined 6 constructs, but that we think that this likely encompasses many of the applications that may be needed for this system, while recognizing that expansion beyond this number may be possible.

(3) There is no data about any potential side effect on their endogenous function of promoter/protein of interest with the ImPaqT method.

Absolutely, we have added new text (lines 457-470) to our discussion describing the potential side effects on protein function. For instance, the need to be aware of whether N- or C-termini of proteins can be modified and recognition of the potential for affecting/creating ectopic transcription factor binding sites as potential pitfalls to keep in mind.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The data presented in the manuscript is robust and well-supported. However, to fully demonstrate the broad applicability of the toolkit and strengthen its impact, a few additional experiments could be beneficial. Specific suggestions for these experiments and areas of improvement are outlined in the 'Weaknesses' section of the Public Review. Additionally, Figures 2-4 illustrate the same concept - cloning three fragments from entry vectors-which comes across as repetitive. Incorporating a more diverse range of use cases would better highlight the versatility of the toolkit.

As we described in our replies to your public points above, we have now added new Figure 6 and new Supplementary Figure 6 addressing the cloning of PCR fragments, short fragments as well as a mechanism of domestication. We have also included the mpeg1.1 promoter within the toolkit. In addition, your point on the repetition of assay is fair and in our new Figure 6, we instead used wild type and dominant-negative Rac2 expression and failure of macrophage recruitment to the tail wound.

Reviewer #2 (Recommendations for the authors):

Hurst et al. developed a new Tol2-based transgenesis system ImPaqT, it is interesting and potentially efficient, but I have a few concerns:

(1) The author claimed that the ImPaqT system is more efficient than other existing systems. The authors should provide such data to support their claim.

Our argument wouldn’t be that the ImPaqT system is strictly speaking more efficient, but rather that the combination of minimal added sequence, the ability to expand or contract the fragments used, and, in our new Figure 6, the ability to directly utilize PCR products and dsDNA fragments, while retaining the ability to combinatorially build constructs from a suite of existing sequences is the main point of the method. We now explicitly state that Golden Gate cloning isn’t more efficient than existing techniques in the text (lines 534-537), but rather the particular strength of the method is the flexibility and minimal added sequence.

(2) The ImPaqT is theoretically less prone to have off-target effects than existing systems, the authors should provide such data to validate their claim.

Good point, we have now searched the zebrafish genome for PaqCI sites as well as for BsaI and BsmBI which are the 6-base cutters most commonly used for Golden Gate cloning. We found that PaqCI cuts every ~17 kb in the zebrafish genome while BsaI and BsmBI cut every ~9 kb or ~13 kb respectively, further supporting that PaqCI sites are rarer in the genome and should generally require domestication less often. We have now added new text describing this in lines 129-132.

(3) The authors should mention any potential side effects of this system on the endogenous function of the promoter/protein of interest, at least in their discussion part.

Yes, this should absolutely be expanded, as we said in your public comments above, we have now added new text describing potential pitfalls that this method may have on promoter or gene expression.

(4) The authors are suggested to provide a balanced discussion about the expandable usage of this system beyond the immune system.

We agree, this is also a good point that we should have emphasized more. We’ve added new text (lines 537-541) recognizing that in principle, many of the components we’ve derived should be useful in non-immune systems, but we also recognize that adapting this to new tissues will require the development of new promoters within the Golden Gate system which can be combined with these already developed tools.

References

Potapov, V., Ong, J.L., Kucera, R.B., Langhorst, B.W., Bilotti, K., Pryor, J.M., Cantor, E.J., Canton, B., Knight, T.F., Evans, T.C., Jr., et al. (2018). Comprehensive Profiling of Four Base Overhang Ligation Fidelity by T4 DNA Ligase and Application to DNA Assembly. ACS Synth Biol 7, 2665-2674.

Pryor, J.M., Potapov, V., Kucera, R.B., Bilotti, K., Cantor, E.J., and Lohman, G.J.S. (2020). Enabling one-pot Golden Gate assemblies of unprecedented complexity using data-optimized assembly design. PLoS One 15, e0238592.

Sikkema, A.P., Tabatabaei, S.K., Lee, Y.J., Lund, S., and Lohman, G.J.S. (2023). High-Complexity One-Pot Golden Gate Assembly. Curr Protoc 3, e882.

Wang, Y., Hsu, A.Y., Walton, E.M., Park, S.J., Syahirah, R., Wang, T., Zhou, W., Ding, C., Lemke, A.P., Zhang, G., et al. (2021). A robust and flexible CRISPR/Cas9-based system for neutrophilspecific gene inactivation in zebrafish. J Cell Sci 134.

Zhou, W., Cao, L., Jeffries, J., Zhu, X., Staiger, C.J., and Deng, Q. (2018). Neutrophil-specific knockout demonstrates a role for mitochondria in regulating neutrophil motility in zebrafish. Dis Model Mech 11.

eLife Assessment

This study maps the genotype-phenotype landscapes of three E. coli transcription factors and the topographical features of these landscapes. It shows that ruggedness and epistasis do not hinder the evolution of strong transcription factor binding sites. These convincing findings contribute important insights into fitness landscape theories and highlight the role of chance, contingency, and evolutionary biases in gene regulation. The authors then study the topographical features of these landscapes, especially the number and distribution of local maxima, as well as the statistical properties of evolutionary paths on these landscapes.

Reviewer #1 (Public review):

Summary:

For each of three key transcription factor (TF) proteins in E. coli, the authors generate a large library of TF binding site (TFBS) sequences on plasmids, such that each TFBS is coupled to the expression of a fluorescence reporter. By sorting the fluorescence of individual cells and sequencing their plasmids to identify each cell's TFBS sequence (sort-seq), they are able to map the landscape of these TFBSs to the gene expression level they regulate. The authors then study the topographical features of these landscapes, especially the number and distribution of local maxima, as well as the statistical properties of evolutionary paths on these landscapes. They find the landscapes to be highly rugged, with about as many local peaks as a random landscape would have, and with those peaks distributed approximately randomly in sequence space. This is quite different from previous work on landscapes for eukaryotic TFBSs, which tend to be rather smooth. The authors find that there are a number of peaks that produce regulation stronger than that of the wild-type sequence for each TF, and that it is not too unlikely to reach one of those "high peaks" from a random starting sequence. Nevertheless, the basins of attraction for different peaks have significant overlap, which means that chance plays a major role in determining which peak a population will evolve to.

Strengths:

(1) The apparent differences in landscape topography between prokaryotic TFBSs and other molecular landscapes is a fascinating discovery to add to the field of genotype-phenotype maps. I am really excited to learn the molecular mechanisms of this in the future.

(2) The experiments and analysis of this paper are very well-executed and, by and large, very thorough. I appreciated the systematic nature of the project, both the large-scale experiments done on three TFs with replicates, and the systematic analysis of the resulting landscapes. This not only makes the paper easy to follow, but also inspires confidence in their results since there is so much data and so many different ways of analyzing it. It's a great recipe for other studies of genotype-phenotype landscapes to follow.

(3) Considering how technical the project was, I am really impressed at how easy to read I found the paper, and the authors deserve a lot of credit for making it so. They do a great job of building up the experiments and analyses step-by-step, and explaining enough of the basics of the experimental design and essence of each analysis in the main text without getting too complicated with details that can be left to the Methods or SI.

Weaknesses:

(1) Regarding the effect of measurement uncertainties, one way in which they attempt to test their effect is to simulate dynamics on noisy and noise-free versions of the landscape and measure visitation frequencies. While they show that visitation frequencies are highly correlated between these cases, I'd prefer a more direct test of epistasis or navigability (e..g, number of local peaks), since that's how they are characterizing the landscapes, and the connection between that and visitation frequency of individual states is unclear.

(2) I am still a little concerned about the fraction of sequences missing from the data due to filtering, although I appreciate the difficulties in testing the importance of this (requiring additional assumptions) and the authors' good-faith efforts to do their best with the data they have.

Reviewer #2 (Public review):

The authors aim to investigate the ability of evolution to create strong transcription factor binding sites (TFBSs) de novo in E. coli. They focus on three global transcriptional regulators: CRP, Fis, and IHF, using a massively parallel reporter assay to evaluate the regulatory effects of over 30,000 TFBS variants. By analyzing the resulting genotype-phenotype landscapes, they explore the ruggedness, accessibility, and evolutionary dynamics of regulatory landscapes, providing insights into the evolutionary feasibility of strong gene regulation. Their experiments show that de novo adaptive evolution of new gene regulation is feasible. It is also subject to a blend of chance, historical contingency, and evolutionary biases that favor some peaks and evolutionary paths.

(1) Strengths of the methods and results:

The authors successfully employed a well-designed sort-seq assay combined with high-throughput sequencing to map regulatory landscapes. The experimental design ensures reliable measurement of regulation strengths. Their system accounts for gene expression noise and normalizes measurements using appropriate controls.

Comprehensive Landscape Mapping:<br /> The study examines ~30,000 TFBS variants per transcription factor, providing statistically robust and thorough maps of the regulatory landscapes for CRP, Fis, and IHF. The landscapes are rigorously analyzed for ruggedness (e.g., number of peaks) and epistasis, revealing parallels with theoretical uncorrelated random landscapes.

Evolutionary Dynamics Simulations:<br /> Through simulations of adaptive walks under varying population dynamics, the authors demonstrate that high peaks in regulatory landscapes are accessible despite ruggedness. They identify key evolutionary phenomena, such as contingency (multiple paths to peaks) and biases toward specific evolutionary outcomes.

Biological Relevance and Novelty:<br /> The author's work is novel in focusing on global regulators, which differ from previously studied local regulators (e.g., TetR). They provide compelling evidence that rugged landscapes are navigable, facilitating de novo evolution of regulatory interactions. The comparison of landscapes for CRP, Fis, and IHF underscores shared topographical features, suggesting general principles of global transcriptional regulation in bacteria.

(2) Weaknesses of the methods and results:

Undersampling of Genotype Space:<br /> Approximately 40% of the theoretical TFBS genotype space remains uncharacterized after quality filtering. The authors now discuss this limitation more explicitly and provide analyses suggesting that undersampling does not strongly bias their conclusions at the landscape level. Nevertheless, predictive modeling approaches could further extend these landscapes in future work.

Simplified Regulatory Architecture:<br /> The study considers a minimal system consisting of a single TFBS upstream of a reporter gene. While this simplification allows clean interpretation and high-throughput measurement, natural promoters often involve combinatorial regulation and chromosomal context effects that may alter landscape topography.

Lack of Experimental Evolution Validation:<br /> The evolutionary conclusions are based on simulations rather than direct experimental evolution. The authors provide a reasonable justification for this choice and frame their conclusions at the statistical level rather than for specific trajectories, but experimental validation would be a valuable future extension.

Impact on the Field:<br /> This study advances our understanding of adaptive landscapes in gene regulation and offers a critical step toward deciphering how global regulators evolve de novo binding sites. The findings provide foundational insights for synthetic biology, evolutionary genetics, and systems biology by highlighting the evolutionary accessibility of strong regulation in bacteria.

Utility of Methods and Data:<br /> The sort-seq approach, combined with landscape analysis, provides a robust framework that can be extended to other transcription factors and systems. If made publicly available, the study's data and code would be valuable for researchers modeling transcriptional regulation or studying evolutionary dynamics.

Additional Context:<br /> The study builds on a growing body of work exploring regulatory evolution. For instance, recent studies on local regulators like TetR and AraC have revealed high ruggedness and epistasis in TFBS landscapes. This study distinguishes itself by focusing on global regulators, which are more complex biologically and more influential in bacterial gene networks. The observed evolutionary contingency aligns with findings in other biological systems, such as protein evolution and RNA folding landscapes, underscoring the generality of these evolutionary principles.

Conclusion:<br /> The authors successfully mapped the genotype-phenotype landscapes for three global regulators and simulated evolutionary dynamics to assess the feasibility of strong TFBS evolution. They convincingly demonstrate that ruggedness and epistasis, while prominent, do not preclude the evolution of strong regulation. Their results support the notion that gene regulation evolves through a blend of chance, contingency, and evolutionary biases.

This paper makes a significant contribution to the understanding of regulatory evolution in bacteria. While minor limitations exist, the authors' methods are robust, and their findings are well-supported. The work will likely be of broad interest to researchers in molecular evolution, synthetic biology, and gene regulation.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

(1) The main weakness of this paper, in my view, is that it felt disconnected from the larger body of work on fitness and genotype-phenotype landscapes, including previous data on TFBSs in E. coli, genotype-phenotype maps of TFBSs in other systems, protein sequence landscapes (e.g., from mutational scans or combinatorially-complete libraries), and fitness landscapes of genomic mutations (e.g., combinatorially-complete landscapes of antibiotic resistance alleles). I have no doubt the authors are experts in this literature, and they probably cite most of it already given the enormous number of references. But they don't systematically introduce and summarize what was already known from all that work, and how their present study builds on it, in the Abstract and Introduction, which left me wondering for most of the paper why this project was necessary. Eventually, the authors do address most of these points, but not until the end, in the Discussion. Readers who have no familiarity with this literature might read this paper thinking that it's the first paper ever to study topography and evolutionary paths on genotype-phenotype landscapes, which is not true.

There were two points that made this especially confusing for me. First, in order to choose which nucleotides in the binding sites to vary, the authors invoke existing data on the diversity of these sequences (position-weight matrices from RegulonDB). But since those PWMs can imply a genotype-phenotype map themselves, an obvious question I think the authors needed to have answered right away in the Introduction is why it is insufficient for their question. They only make a brief remark much later in the Results that the PWM data is just observed sequence diversity and doesn't directly reflect the regulation strength of every possible TFBS sequence. But that is too subtle in my opinion, and such a critical motivation for their study that it should be a major point in the Introduction.

The second point where the lack of motivation in the Introduction created confusion for me was that they report enormous levels of sign epistasis in their data, to the point where these landscapes look like random uncorrelated landscapes. That was really surprising to me since it contrasts with other empirical landscape data I'm familiar with. It was only in the Discussion that I found some significant explanation of this - namely that this could be a difference between prokaryotic TFBSs, as this paper studies, and the eukaryotic TFBSs that have been the focus of many (almost all?) previous work. If that is in fact the case - that almost all previous studies have focused on eukaryotic TFBSs or other kinds of landscapes, and this is the first to do a systematic test of prokaryotic TFBS, then that should be a clear point made in the Abstract and Introduction. (I find a comparable statement only in the very last paragraph of the Discussion.) If that's the case, then I would also find that point to be a much stronger, more specific conclusion of this paper to emphasize than the more general result of observing epistasis and contingency (as is currently emphasized in the Abstract), which has been discussed in tons of other papers. This raises all sorts of exciting questions for future studies - why do the landscapes of prokaryotic TFBSs differ so dramatically from almost all the other landscapes we've observed in biology? What does that mean for the evolutionary dynamics of these different systems?

We thank the reviewer for this thoughtful and detailed critique. We agree that the original version of the manuscript did not sufficiently motivate the study early on, nor did it clearly position our work within the broader literature on genotype–phenotype (GP) and fitness landscapes. We also agree that two specific issues, the role of PWMs and the unexpectedly high levels of sign epistasis, were insufficiently explained early on, which could lead to confusion for readers not already familiar with this field.

Positioning within the broader landscape literature

In response, we have substantially revised the Abstract and Introduction to explicitly situate our work within existing empirical studies of GP and fitness landscapes, including TFBS landscapes in bacteria, eukaryotic TFBS genotype–phenotype maps, in vitro TF–DNA binding studies, deep mutational scans of proteins, and combinatorially complete fitness landscapes such as antibiotic resistance alleles (Abstract; Introduction, lines 64–85). We now make clear that our study builds directly on this extensive body of work, rather than introducing the landscape framework itself. For example, we write in the introduction:

“Over the last decade, genotype–phenotype (GP) maps and fitness landscapes have become central tools for understanding how molecular systems evolve under mutation and selection[22–25]. Such maps and landscapes have been experimentally studied for DNA[6,8,18,19,26,27], protein[28–32] and RNA[33–35] molecules, revealing key topographical properties that shape evolutionary outcomes, including epistasis[24,36]—the non-additive effects of multiple mutations on phenotype—landscape ruggedness, reflected in the number and distribution of fitness peaks, and constraints on adaptive evolution.”

At the same time, we clarify what remains rare in the literature: large-scale, in vivo genotype–phenotype landscapes for bacterial transcription factor binding sites that are sufficiently dense to support explicit evolutionary analyses. While numerous high-throughput studies have characterized bacterial regulatory elements, these datasets typically do not provide quantitative regulatory phenotypes across large genotype spaces, nor do they analyze evolutionary accessibility. To our knowledge, only one such in vivo TFBS landscape had previously been characterized at comparable resolution for a bacterial local regulator (TetR). Our work extends this approach to three global regulators, enabling systematic comparisons across prokaryotic systems (Abstract, Introduction, lines 64–85). For example, we write in the introduction:

“For transcription factor binding sites, most pertinent large-scale studies are based on in vitro binding assays, such as protein-binding microarrays (PBMs), and they focus predominantly on eukaryotic transcription factors[6]. While these studies have been instrumental in characterizing transcription factor binding preferences, they typically do not measure regulatory output in a native cellular context. In contrast, comprehensive in vivo data for bacterial TFBSs remain extremely rare. To our knowledge, only two high-resolutionin vivo landscapes have been previously mapped for bacterial regulators, those of the local regulators TetR[18] and LacI[27]. As a result, it remains unclear whether principles inferred from protein landscapes, eukaryotic TFBSs, or in vitro binding assays generalize to transcriptional regulation in bacteria, particularly for global regulators[11] that integrate multiple physiological signals.”

Why PWMs are insufficient for our question.

We agree with the reviewer that our original explanation of the role of PWMs was too cursory and should have been addressed explicitly in the Introduction. We have now revised the Introduction to clearly explain why PWMs derived from RegulonDB cannot substitute for empirical GP landscapes in our study (Introduction, lines 102–113).

In this passage we now explain that, first, PWMs are inferred from a limited number of naturally occurring binding sites—typically on the order of hundreds of sequences—whose diversity reflects evolutionary history and genomic context rather than systematic exploration of sequence space. As a result, PWMs sample only a small and biased subset of the possible TFBS variants, whereas our libraries probe tens of thousands of sequences in a controlled manner, providing substantially broader and more uniform coverage of genotype space (Introduction, lines 102–113).

Second, PWM scores are not direct measurements of regulatory strength. Instead, they represent probabilistic or heuristic scores that are primarily used for identifying candidate binding sites in genomes. Numerous studies have shown that PWM scores often correlate weakly with in vivo binding affinity or regulatory output, where DNA shape, cooperative interactions, and chromosomal context play important roles. As such, PWMs do not provide quantitative genotype–phenotype relationships for regulation strength (Introduction, lines 102–113).

Third, PWMs assume independent and additive contributions of individual nucleotide positions. This assumption excludes epistatic interactions by construction. Because epistasis is central to landscape ruggedness, peak structure, and evolutionary accessibility, PWM-based models are fundamentally unsuited to address the evolutionary questions we study here (Introduction, lines 102–113). We now explicitly state this limitation early in the manuscript, rather than only alluding to it later in the Results.

Sign epistasis and contrast with prior TFBS landscapes.

We also agree with the reviewer that the extensive sign epistasis we observe—approaching levels expected for uncorrelated random landscapes—is surprising in light of much of the existing empirical landscape literature. Importantly, as the reviewer notes, most previous TFBS landscape studies have focused on in vitro binding systems or on eukaryotic transcription factors, which tend to exhibit smoother and more additive landscapes.

To address this concern, we have revised the Abstract and Introduction to explicitly frame this contrast as a central result of the study (Abstract; Introduction, lines 151-153, Discussion, lines 652–668). For example, we write in the discussion:

“We showed that the regulatory landscapes of all three TFs are highly rugged and have multiple peaks. The ruggedness of all three landscapes is also supported by the prevalence of epistasis between pairs of TFBS mutations (Supplementary Table S5). A particularly important form of epistasis is sign epistasis[24,93,94], because it can lead to multiple adaptive peaks [24,93,94] (see Supplementary Methods 7.5). Our landscapes contain up to 65% of mutation pairs with sign epistasis, a value that is especially high compared to the almost exclusively additive interactions of mutations in eukaryotic TFs[6,125].”

We now emphasize that prokaryotic TFBS landscapes, particularly for global regulators, appear to be substantially more rugged and epistatic than most previously characterized TFBS landscapes, and that this difference likely reflects fundamental biological distinctions between regulatory systems.

Revised emphasis and conclusions.

Following the reviewer’s suggestion, we have adjusted the emphasis of the manuscript accordingly. Rather than highlighting epistasis and contingency as generic evolutionary phenomena, we now present the extreme ruggedness of prokaryotic TFBS landscapes as a system-specific finding with important implications for the evolution of gene regulation. We explicitly note that this raises new questions for future work—such as why prokaryotic regulatory landscapes differ so markedly from eukaryotic ones, and how these differences shape evolutionary dynamics—which we now highlight in the Introduction and Discussion (Abstract; Introduction, lines 151-153, Discussion, lines 652–668). For example, we write in the discussion:

“… A possible reason for this greater incidence of epistasis lies in the nature of prokaryotic TFBSs. Specifically, prokaryotic TFBSs are at approximately 20bps twice as long as eukaryotic TFBSs[80,128] and exhibit symmetries that reflect the dimeric state of their cognate TFs[129–131]. These factors may increase the likelihood of intramolecular epistasis. Our observations raise important questions for future work, such as why the landscapes of prokaryotic TFBSs differ so dramatically from those of eukaryotic ones. And what do these differences imply for the evolutionary dynamics of gene regulation?”

We believe that these revisions substantially improve the clarity, motivation, and positioning of the manuscript, and directly address the reviewer’s concerns by making both the necessity and the novelty of the study clear from the outset.

(2) I am a bit concerned about the lack of uncertainties incorporated into the results. The authors acknowledge several key limitations of their approach, including the discreteness of the sort-seq bins in determining possible values of regulation strength, the existence of a large number of unsampled sequences in their genotype space, as well as measurement noise in the fluorescence readouts and sequencing. While the authors acknowledge the existence of these factors, I do not see much attempt to actually incorporate the effect of these uncertainties into their conclusions, which I suspect may be important. For example, given the bin size for the fluorescence in sort-seq, how confident are they that every sequence that appears to be a peak is actually a peak? Is it possible that many of the peak sequences have regulation strengths above all their neighbors but within the uncertainty of the fluorescence, making it possible that it's not really a peak? Perhaps such issues would average out and not change the statistical nature of their results, which are not about claiming that specific sequences are peaks, just how many peaks there are. Nevertheless, I think the lack of this robustness analysis makes the results less convincing than they otherwise would be.

We thank the reviewer for raising this important concern. We fully agree that uncertainties arising from experimental resolution, measurement noise in fluorescence and sequencing, and incomplete sampling of genotype space should be incorporated explicitly into the analysis. While these limitations were acknowledged qualitatively in the original manuscript, we recognize that a direct, quantitative assessment of their impact on our conclusions is essential to strengthen the robustness of the study.

We first clarify that regulation strength is not discretized in our analysis. For each TFBS, regulation strength is calculated as a continuous weighted average of fluorescence across all sorting bins, based on the sequencing read-count distribution of each sequence across bins. We clarified this information in the main text (Results, lines 201-203). Nevertheless, finite binning resolution and experimental noise introduce uncertainty in these estimates, which could in principle affect the identification of local peaks.

Importantly, our study does not aim to assert that specific TFBS sequences are definitively peaks. Rather, our focus is on landscape-level statistical and topological properties—such as ruggedness, the abundance and distribution of peaks, and the evolutionary accessibility of strong regulation. We therefore centered our new analyses on testing whether these conclusions are robust to experimentally plausible sources of uncertainty, rather than on the identity of individual peaks.

To address the reviewer’s concern, we performed two complementary analyses. The first evaluates whether the observed ruggedness of the landscapes could arise as an artifact of incomplete sampling. It addressed the effects of missing genotypes and the possibility of spurious peak identification due to unsampled neighbors. Sparse sampling can introduce opposing biases: true peaks may be missed, while other genotypes may be falsely classified as peaks because fitter neighbors are absent. As shown for uncorrelated random (House-of-Cards) landscapes (Kauffman & Levin, 1987), these effects can partially cancel.

In this analysis, we constructed a null model by randomly permuting regulation strengths across the mapped genotype network while preserving its topology. The number of peaks in these randomized landscapes is only modestly higher than in the empirical data, indicating that the measured landscapes are close to the maximal ruggedness compatible with the sampled network (Results, lines 308–320).

In addition, we quantified potential sampling bias by analyzing genotype connectivity. Here we defined the relative connectivity of a genotype as the fraction of possible single-mutant neighbors for which we had measured regulation strength. We observed only a very weak correlation between connectivity and regulation strength (R=-0.1, -0.1, 0.01 for the CRP, Fis, and IHF landscapes, Figures S13-S15). Similarly, the relative connectivity of peak genotypes is only weakly correlated with their regulation strength (R=-0.05, -0.04, 0.06 for the CRP, Fis, and IHF landscapes). (Results, lines 321–330), indicating that strongly regulating genotypes are not preferentially oversampled or undersampled (Results, lines 321–330).

The second, and most important, analysis directly addresses the reviewer’s concern that experimental uncertainty could affect peak classification and, consequently, landscape navigability. We explicitly incorporated experimentally measured, genotype-specific noise estimates from biological replicates when comparing fitness values between neighboring genotypes. Using these uncertainty-aware comparisons, we then recomputed adaptive-walk dynamics and genotype visitation frequencies on the resulting noisy landscapes.

We observe strong correlations between visitation frequencies in the noise-free and noisy landscapes across all three transcription factors (new Supplementary Figure S35), indicating that evolutionary accessibility patterns are robust to realistic levels of experimental uncertainty. These analyses are described in the revised Results (lines 622–636) and in a new Supplementary Methods section (“Incorporation of experimental uncertainty into adaptive walks”).

Reviewer #2 (Public review):

The authors aim to investigate the ability of evolution to create strong transcription factor binding sites (TFBSs) de novo in E. coli. They focus on three global transcriptional regulators: CRP, Fis, and IHF, using a massively parallel reporter assay to evaluate the regulatory effects of over 30,000 TFBS variants. By analyzing the resulting genotype-phenotype landscapes, they explore the ruggedness, accessibility, and evolutionary dynamics of regulatory landscapes, providing insights into the evolutionary feasibility of strong gene regulation. Their experiments show that de novo adaptive evolution of new gene regulation is feasible. It is also subject to a blend of chance, historical contingency, and evolutionary biases that favor some peaks and evolutionary paths.

(1) Strengths of the methods and results:

The authors successfully employed a well-designed sort-seq assay combined with high-throughput sequencing to map regulatory landscapes. The experimental design ensures reliable measurement of regulation strengths. Their system accounts for gene expression noise and normalizes measurements using appropriate controls.

Comprehensive Landscape Mapping:

The study examines ~30,000 TFBS variants per transcription factor, providing statistically robust and thorough maps of the regulatory landscapes for CRP, Fis, and IHF. The landscapes are rigorously analyzed for ruggedness (e.g., number of peaks) and epistasis, revealing parallels with theoretical uncorrelated random landscapes.

Evolutionary Dynamics Simulations:

Through simulations of adaptive walks under varying population dynamics, the authors demonstrate that high peaks in regulatory landscapes are accessible despite ruggedness. They identify key evolutionary phenomena, such as contingency (multiple paths to peaks) and biases toward specific evolutionary outcomes.

Biological Relevance and Novelty:

The author's work is novel in focusing on global regulators, which differ from previously studied local regulators (e.g., TetR). They provide compelling evidence that rugged landscapes are navigable, facilitating de novo evolution of regulatory interactions. The comparison of landscapes for CRP, Fis, and IHF underscores shared topographical features, suggesting general principles of global transcriptional regulation in bacteria.

(2) Weaknesses of the methods and results:

Undersampling of Genotype Space:

While the quality filtering of the data ensures robustness, ~40% of the TFBS space remains uncharacterized. The authors acknowledge this limitation but could improve the analysis by employing subsampling or predictive modeling.

We thank the reviewer for raising this point. We agree that undersampling of genotype space is an important limitation of our dataset and that, in principle, subsampling or predictive modeling approaches could be used to address missing genotypes. We have now clarified in the manuscript why these approaches are not straightforward in the context of our analyses and why we did not pursue them here.

Although approximately 40% of TFBS genotypes were removed during the filtering step due to lack of reliable measurements, this filtering step was necessary to ensure robust estimation of regulation strength from sort-seq data. Importantly, random subsampling of the genotypes in our data set would not alleviate this limitation, because many of our key analyses—such as peak identification, quantification of epistasis, and assessment of evolutionary accessibility—require combinatorially complete local neighborhoods in genotype space. Subsampling would remove mutational neighbors from many neighborhoods, and thus further limit our ability to characterize landscape topology.

Predictive modeling approaches could, in principle, be used to infer missing genotypes and reconstruct more complete landscapes. However, developing, experimentally validating, and benchmarking such models would not only substantially expand the scope of an already long paper, it would  also require additional assumptions about genotype–phenotype relationships that entail their own limitations. Our primary goal in this work was to provide the first large-scale empirical in vivo regulatory landscapes for global bacterial transcription factors, comprising tens of thousands of experimentally measured variants. We view these empirical landscapes as a necessary foundation upon which predictive modeling and landscape completion can be built in future, complementary studies.

We have now revised the Discussion (lines 760-770) to explicitly articulate these points and to clarify that, while undersampling remains a limitation, it does not invalidate the landscape-level conclusions we draw from the combinatorially complete neighborhoods present in our data. There we also outline predictive modeling as an important directions for future work.

For a more detailed answer regarding subsampling and peak classification, please also see our response to comment (2) of Reviewer #1.

Simplified Regulatory Architecture:

The study considers a minimal system of a single TFBS upstream of a reporter gene. While this may have been necessary for clarity, this simplification may not reflect the combinatorial complexity of transcriptional regulation in vivo.

Point well taken. We have added paragraph to state explicitly that the system we use to study gene regulation is much simpler than most in vivo regulatory circuits (Discussion, lines 797-802)

Lack of Experimental Validation of Simulations:

The adaptive walks are based on simulated dynamics rather than experimental evolution. Incorporating in vivo experimental evolution studies would strengthen the conclusions. Although this is a large request for the paper, that would not prevent publication.

We thank the reviewer for this important point. We fully agree that in vivo experimental evolution would provide a valuable and complementary way to validate the evolutionary dynamics inferred from our simulations. However, we ask for the reviewer's understanding that adding experimental evolution to an (already long) paper would go far beyond the scope of our study.

Also, the goal of our study was not to reproduce evolutionary trajectories experimentally, but to characterize the structure of large empirical regulatory landscapes, and to use these landscapes as a data-driven basis for exploring evolutionary accessibility under well-defined population-genetic assumptions. The adaptive walks we employ are parameterized directly from experimentally measured genotype–phenotype maps, and incorporate established fixation probabilities. Such walks have been widely used to study evolutionary dynamics on empirical landscapes when experimental evolution is not tractable, because it would involve tens of thousands of genotypes that represent small mutational targets and would thus take a long time to evolve.

An additional issue related to the feasibility of experimental evolution is that performing in vivo experimental evolution for the regulatory landscapes analyzed here would require tracking large populations across a combinatorially vast TFBS space, while simultaneously measuring regulatory phenotypes for thousands of evolving lineages, which is currently not experimentally feasible. This is another reason why simulation-based approaches have been the standard method for linking large-scale empirical landscapes to evolutionary dynamics in both theoretical and experimental studies.

Furthermore, our conclusions are intentionally framed at the level of statistical and landscape-wide properties (e.g., accessibility of high peaks, contingency, and evolutionary bias), rather than at the level of specific mutational trajectories. As such, they do not rely on the precise reproduction of any single evolutionary path, but on aggregate patterns that are robust to reasonable variation in population-genetic parameters.

In sum, we do not view experimental evolution as essential for the conclusions we draw, but as an important and exciting direction for future work that may be enabled by the landscapes we have experimentally mapped.

Impact on the Field:

This study advances our understanding of adaptive landscapes in gene regulation and offers a critical step toward deciphering how global regulators evolve de novo binding sites. The findings provide foundational insights for synthetic biology, evolutionary genetics, and systems biology by highlighting the evolutionary accessibility of strong regulation in bacteria.

Utility of Methods and Dat

The sort-seq approach, combined with landscape analysis, provides a robust framework that can be extended to other transcription factors and systems. If made publicly available, the study's data and code would be valuable for researchers modeling transcriptional regulation or studying evolutionary dynamics.

Additional Context:

The study builds on a growing body of work exploring regulatory evolution. For instance, recent studies on local regulators like TetR and AraC have revealed high ruggedness and epistasis in TFBS landscapes. This study distinguishes itself by focusing on global regulators, which are more biologically complex and influential in bacterial gene networks. The observed evolutionary contingency aligns with findings in other biological systems, such as protein evolution and RNA folding landscapes, underscoring the generality of these evolutionary principles.

Conclusion:

The authors successfully mapped the genotype-phenotype landscapes for three global regulators and simulated evolutionary dynamics to assess the feasibility of strong TFBS evolution. They convincingly demonstrate that ruggedness and epistasis, while prominent, do not preclude the evolution of strong regulation. Their results support the notion that gene regulation evolves through a blend of chance, contingency, and evolutionary biases.

This paper makes a significant contribution to the understanding of regulatory evolution in bacteria. While minor limitations exist, the authors' methods are robust, and their findings are well-supported. The work will likely be of broad interest to researchers in molecular evolution, synthetic biology, and gene regulation.

We thank the reviewer for their thorough evaluation and for their supportive opinion of this paper.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Line 28 (Abstract): "Landscape ruggedness does not prevent the evolution of strong regulation, because more than 10% of evolving populations can attain one of the highest peaks." I did not find this interpretation very convincing; only 10% of populations being able to achieve strong regulation sounds to me like ruggedness DOES impede adaptation in the vast majority of cases.

We thank the reviewer for this thoughtful comment and agree that our original phrasing in the Abstract overstated this conclusion. We did not intend to imply that landscape ruggedness has only a minor effect on adaptation. On the contrary, our results clearly show that ruggedness strongly constrains evolutionary outcomes and prevents the majority of evolving populations from reaching the globally highest regulatory peaks. We have therefore toned down the wording in both the Abstract and the Discussion (lines 670-679) to reflect this more accurately. For example, in the abstract we now state

“Nonetheless, evolutionary simulations show that ~10% of evolving populations can reach a peak of strong regulation, a proportion that is significantly greater than in comparable random landscapes.”

In the discussion we state:

“… Specifically, our evolutionary simulations show that 10% of populations with a size typical of E. coli reach one of the highest peaks. This percentage is significantly higher than in randomized landscapes (Supplementary Methods 9; Supplementary Figure S30)"

Our intended interpretation was more limited: namely, that ruggedness does not fully preclude the evolution of strong regulation. In highly rugged landscapes with extensive sign epistasis—whose topological properties approach those of uncorrelated random landscapes—the a priori expectation is that access to the strongest peaks could be vanishingly rare or effectively impossible under Darwinian evolution. In this context, observing that a non-negligible fraction of populations (on the order of 10%) can reach one of the highest peaks suggests that strong regulation remains evolutionarily attainable, even though it is far from guaranteed.

Motivated by the reviewer’s suggestion, we also added a null-model analysis that makes this point more explicitly and quantitatively. Specifically, we constructed randomized landscapes by permuting regulation-strength values across genotypes while preserving the experimentally sampled genotype network topology and all parameters of the evolutionary simulations (Supplementary Methods 9, “Randomized landscape null model for peak accessibility”). We then repeated the adaptive-walk simulations on these shuffled landscapes. This null model provides an expectation for peak accessibility in landscapes with identical sampling, neighborhood structure, and evolutionary dynamics, but without genotype–phenotype correlations.

Using this null model, we find that the fraction of populations that reach high peaks in the empirical landscapes is substantially higher than expected by chance alone (new Supplementary Figure S30; Results, lines 504–516). Specifically, across the three transcription factors, empirical landscapes exhibit on average a ~3-fold higher accessibility of high regulatory peaks than shuffled landscapes. This comparison does not weaken the conclusion that ruggedness strongly impedes adaptation; rather, it shows that the structure of the measured genotype–phenotype landscapes enables greater accessibility of strong regulation than would be expected in equally rugged but unstructured landscapes.

In response to the reviewer’s concern, we have revised the abstract and main text to avoid the phrase “does not prevent” and to more accurately convey this balance between constraint and accessibility. We now emphasize that ruggedness strongly constrains adaptation, while still allowing access to strong regulatory peaks at rates that exceed null expectations. (Discussion, lines 512-516). For example, in the discussion we state:

“… In sum, rugged regulatory landscapes strongly constrain evolutionary trajectories, yet do not render the evolution of strong regulation vanishingly rare. Instead, strong regulatory phenotypes remain evolutionarily attainable at levels that exceed null expectations, even though they are reached by only a minority of evolving populations.”

We believe that the revised wording, together with the added null-model analysis more faithfully represents our results and strengthens the quantitative interpretation of accessibility in these landscapes.

(2) Line 123: I found the explanation of the plasmid system and the accompanying SI figures (Figures S1 and S2) confusing in terms of how many plasmids there were. In particular, the Figure S1 graphics show the plasmid specifically with CRP but the text in the graphic and in the caption refers to the plasmid pCAW-Sort-Seq-V2 (which, according to Table S1, isn't that just the base plasmid without any TF?). Figure S2 also shows the plasmid with CRP and does specify pCAW-Sort-Seq-V2-CRP-CRP0 in the graphic, but then the caption refers again only to the base plasmid pCAW-Sort-Seq-V2. I recommend the authors clarify these items for readers who might want to reproduce or build upon their system. In particular, I recommend the main text explain more explicitly that they generate three versions of this plasmid (one for each TF), and then on the backgrounds of each of those three plasmids, a whole library with all the binding site variants.

We thank the reviewer for pointing out this lack of clarity. We agree that the original description of the plasmid system and the accompanying Supplementary Figures S1 and S2 could be confusing with respect to how many plasmids were used and how they differ.

To clarify the experimental design, we start from a common backbone plasmid, pCAW-Sort-Seq-V2, which contains all shared regulatory and reporter elements but does not encode any transcription factor. From this backbone, we generated three distinct TF-specific plasmids, each carrying one of the transcription factors studied here—CRP, Fis, or IHF—resulting in pCAW-Sort-Seq-V2-CRP, pCAW-Sort-Seq-V2-Fis, and pCAW-Sort-Seq-V2-IHF. On the background of each TF-specific plasmid, we then constructed a complete library of plasmids containing all variants of the corresponding TF binding site cloned upstream of the reporter gene.

We have revised the main text to explicitly describe this plasmid hierarchy and library construction strategy and to clarify that three TF-specific plasmids were generated prior to TFBS library construction (Results, Landscape mapping section; lines 159–193). In addition, we have redesigned Supplementary Figures S1 and S2 to facilitate understanding of the plasmid system. Specifically, these figures now clearly distinguish between the base plasmid backbone and the TF-specific plasmid derivatives. Also, the plasmid names shown in the graphics and captions are now consistent with those listed in Supplementary Table S1. Upon final publication, we will also deposit the sequences of all plasmids in Addgene to further facilitate reproducibility.

(3) Line 135: Can the authors clarify whether these TFs are essential in these media conditions and, if not, why? I was expecting them to be so given the core functions of these TFs as described in the Introduction, but then Figure S3 appears to show that all knockouts are viable.

We thank the reviewer for raising this important point and apologize for the lack of clarity in the original version of the manuscript. The transcription factors CRP, Fis, and IHF are not essential for viability under the growth conditions used in this study, but they are important for optimal growth and cellular fitness, consistent with their roles as global regulators.

Under our experimental conditions, single-gene knockout strains (Δcrp, Δfis, and Δihf) are viable but exhibit slower growth dynamics compared to the wild-type strain, reflecting impaired regulation of core cellular processes (Supplementary Figure S3). This behavior is consistent with previous work showing that many global transcriptional regulators in E. coli are conditionally essential or strongly fitness-affecting, rather than absolutely essential under standard laboratory conditions.

Importantly, while single knockouts remain viable, double mutants involving these global regulators are not viable, indicating substantial functional redundancy and network-level essentiality among global transcription factors. This explains why each TF can be studied individually in isolation, while combinations of deletions cannot be maintained.

We have now clarified this point in the Results section by explicitly stating that the knockout strains show reduced growth rates but reach comparable cell densities during late exponential or early stationary phase, the growth phase at which all measurements were performed (Results, Landscape mapping section; lines 185–193). This clarification reconciles the apparent discrepancy between the biological importance of these transcription factors discussed in the Introduction and the viability of the single-knockout strains shown in Supplementary Figure S3.

(4) Lines 141 and 227: The authors appear to refer to two different citations for different versions of RegulonDB (refs. 47 and 66). Did they actually use both versions for different purposes (if so, why?), or is this a typo?

We thank the reviewer for noticing this inconsistency. We did not use two different versions of RegulonDB. The two separate references were an error. We have now corrected this by using a single, consistent RegulonDB citation in both locations.

(5) Line 166 (Figure 1 caption): I think 2^8 here should be 4^8.

Thank you. We have corrected “2⁸” to “4⁸” in the Figure 1 caption.

(6) Figure 2Are the distributions in Figure 2a (regulation strengths across all TFBSs in the libraries) equivalent to the distributions in Figures S4-S6 (direct fluorescence readout from cell sorting), just transformed from fluorescence to regulation strength? If so I think that would be helpful to clarify, perhaps in the captions to Figures S4-S6 so that it's clear these contain the same information.

No. Figures S4–S6 and Figure 2a do not show the same distributions. Figures S4–S6 display the raw fluorescence distributions obtained from cell sorting, whereas Figure 2a shows regulation strengths (S), which are derived quantities computed from these fluorescence data. Specifically, regulation strength is calculated as a weighted average over fluorescence bins using the sequencing read distribution for each TFBS (see Methods, “Regulation strengths”).

To clarify this relationship, we have revised the main text (lines 201-203 and Figure 1b-c), to explicitly state how regulation strengths (S) were calculated.

(7) Figure 2b: Can the authors label each logo/frequency matrix with its corresponding TF name in the graphic itself? I think this is only implied in the caption.

We have updated Figure 2b to label each sequence logo / frequency matrix directly in the graphic with its corresponding transcription factor name (CRP, Fis, or IHF), in addition to mentioning these names in the caption. This change clarifies the figure and makes the TF identity immediately apparent to the reader.

(8) Lines 290 and 298 (Figure 2 caption): The labels for panels b and c appear to be swapped in the caption.

We thank the reviewer for pointing this out. The labels for panels b and c in the Figure 2 caption were indeed swapped. This has now been corrected.

(9) Line 379: There is a missing period at the end of this line.

We have added the missing period at the end of this line.

(10) Line 400 (Figure 3 caption): There is a missing subtitle for panel c in the caption for this figure (all other panels seem to have bolded subtitles in their captions).

We have added the missing subtitle for panel c in the Figure 3 caption to match the formatting of the other panels.

(11) Line 583: There is a missing period after "Methods 7.5)".

We have added the missing period after “Methods 7.5)”.

(12) Line 641: "All three landscapes highly rugged" should probably be "All three landscapes are highly rugged".

We have corrected the sentence to read “All three landscapes are highly rugged.”

eLife Assessment

Findings from this study are considered fundamental because they identify amino acid uptake, cholesterol synthesis, and protein prenylation as key metabolic regulators of B cell activation, proliferation, and survival, advancing understanding of T-independent immune responses. The study links metabolic reprogramming directly to B cell function, highlighting how cellular metabolism supports immune fitness. The evidence is compelling, combining unbiased proteomic profiling with genetic and pharmacological validation to demonstrate causal roles for these pathways.

Reviewer #1 (Public review):

The work presented by Cheung et al. used a quantitative proteomics method to capture molecular changes in B cells exposed to LPS and IL-4, a combination of stimuli activating naive B cells. Amino acid transporters, cholesterol biosynthetic enzymes, ribosomal components, and other proteins involved in cell proliferation were found to increase in stimulated B cells. Experiments involving genetic loss-of-function (SLC7A5), pharmacological inhibition (HMGCR, SQLE, prenylation), and functional rescue by metabolites (mevalonate, GGPP) validated the proteomics data and revealed that amino acid uptake, cholesterol/mevalonate biosynthesis, and cholesterol uptake played a crucial role in B cell proliferation, survival, biogenesis, and immunoglobulin class switching. Experiments involving cholesterol-free medium showed that both biosynthesis and LDLR-mediated uptake catered to the cholesterol demand of LPS/IL-4-stimulated B cells. A role for protein prenylation in LDLR-mediated cholesterol uptake was postulated and backed by divergent effects of GGPP rescue in the presence and absence of cholesterol in culture medium.

Strengths:

The discovery was made by proteome-wide profiling and unbiased computational analysis. The discovered proteins were functionally validated using appropriate tools and approaches. The metabolic processes identified and prioritized from this comprehensive survey and systematic validation highly likely represent mechanisms of high importance and influence. Analysis of immune cell metabolism at the protein level is relatively compared to transcriptomic and metabolomic analysis.

The conclusions from functional validation experiments were supported by clear data and based on rational interpretations. This was enabled by well-established readouts/analytical methods used to determine cell proliferation, viability, size, cholesterol content, and transporter/enzyme function. The data generated from these experiments strongly support the conclusions.

This work reveals a complex, yet intriguing, relationship between cholesterol metabolism and protein prenylation as they serve to promote B cell activation. The effects of pharmacological inhibition and metabolite replenishment on the cholesterol content and activation of B cells were determined and logically interpreted.

Weaknesses:

The findings of this study were obtained almost exclusively from ex vivo B cell stimulation experiments. Their contribution to B cell state and B cell-mediated immune responses in vivo was not explored. Without in vivo data, the study still provides valuable mechanistic information and insights, but it remains unknown, and there is no discussion about, how the identified mechanisms may play out in B cell immunity.

The role of HMGCR, SQLE, and prenylation in B cell activation was assessed using pharmacological inhibitors. Evidence from other loss-of-function approaches, which could strengthen the conclusions, does not exist. This is a moderate weakness and somewhat offset by other data, including those obtained from the tests involving multiple distinct pharmacological inhibitors and the metabolite replenishment experiments.

Reviewer #2 (Public review):

This study uses mass spectrometry to quantify how LPS + IL-4 modify the mouse B cell proteome as naïve cells undergo blastogenesis and enter the cell cycle. This analysis revealed changes in key proteins involved in amino acid transport and cholesterol biosynthesis. Genetic and pharmacological experiments indicated important roles for these metabolic processes in B cell proliferation.

This work provides new information about the regulation of TI B cell responses by changes in cell metabolism and also a comprehensive mass spectrometry dataset which will be an important general resource for future studies. The experiments are thorough and carefully carried out. The majority of conclusions are backed up by data that is shown to be highly significant statistically. The comprehensive mass spectrometry dataset will be an important general resource for future studies.

After revision, the study now includes new data showing that the up regulation of amino acid uptake and cholesterol metabolism is not restricted to LPS + IL-4 (TLR4 + IL4R) stimulation but is also observed after stimulation of TLR7, TLR9, CD40 and the BCR. This increases the impact of this work and shows that this metabolic rewiring is a common feature of B cell activation. The inclusion of inhibitor data showing important roles for MTOR and ERK/p38a MAP kinases in the metabolic changes identified and provides preliminary insights into the mechanisms involved.

Author Response:

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

Reviewer #1 (Public review):

We agree with the reviewer that a limitation of our study is its focus on cell-based assays rather than in vivo experiments. We did consider evaluating the effects of statins on B cell responses in vivo; however, this approach is complicated by findings that statins can influence antigen presentation by dendritic cells, thereby impacting antibody responses (Xia et al, 2018). We have revised the discussion section to acknowledge this points.

The reviewer also noted that our study assessed the roles of HMGCR, SQLE, and prenylation in B cell activation using pharmacological inhibitors and genetic knockdown/out approaches. Loss-of-function techniques such as RNAi, siRNA, and CRISPR can be challenging to apply to primary B cells, but we are exploring their feasibility for future revisions. While we acknowledge the limitations of using pharmacological inhibitors, we have taken several steps to mitigate these, including targeting multiple steps in the cholesterol biosynthetic pathway using structurally distinct inhibitors and conducting rescue experiments by supplementing downstream metabolites. To strengthen the results on prenylation further, we have added data using two further distinct prenylation inhibitors (revised Figure 6). To further investigate potential off-target effects of statins, we performed proteomic analysis of B cells treated with and without fluvastatin. The data suggest that fluvastatin primarily affects cholesterol metabolism and does not cause widespread off-target effects (new Supplementary Figure 9).

Reviewer #1 (Recommendations for the authors):

What signalling mechanisms link LPS sensing to proteomic and metabolic changes? Do these changes depend on specific signalling modules downstream of TLR4 (e.g., MyD88, TRIF, NF-kappaB, MAPKs)? Other receptors found to produce similar effects (TLR7, TLR9, CD40) may share these modules. This information could strengthen the conclusion by showing the chain of molecular events through which immune stimuli reprogram B cell metabolism.

Signalling through most TLRs, including TLR4, TLR7 and TLR9, requires the adaptor protein MyD88. To determine if MyD88 is required for LPS-induced signalling, we carried out immunoblotting to compare signalling in B cells between WT mice and MyD88-deficient mice. We found that phosphorylation of key downstream proteins, including p38 and ERK1/2 (MAPK signalling), Akt, p70S6K and S6 (mTOR signalling) was diminished in MyD88-deficient mice (Figure S11). These results have been added to the manuscript as Supplementary Figure 11.

We assessed the requirement of these signalling pathways for LPS-induced proliferation by treating B cells with rapamycin to block mTORC1, PD184352 for MEK1/MEK2 (the upstream activators of ERK1/2), VX745 for p38 or a combination of PD184352 and VX745. These results have been added to the manuscript as the new Figure 9. Rapamycin demonstrated the strongest inhibitory effect on proliferation, and combinatorial blocking of MAPK signalling mildly reduced proliferation (Figure 9A-B). In terms of cholesterol metabolism, treatment with all of these inhibitors reduced cholesterol levels; however, treatment with PD184352 and VX745 reduced cholesterol to the same level as naïve B cells (Figure 9F).

Other activating stimuli appear to have similar effects, we showed originally that TLR7 and TLR9 activation had a similar effect on proliferation and cholesterol to TLR4, as did activation of CD40 and the BCR (Figure 10). We have now expanded this and shown that these other receptors can also promote protein synthesis (new Supplementary Figure 4).

There seem to be errors in the manuscript text.

(1) Page 6, line 232: ssRNAseq?

We that the reviewer for spotting these issues. This has been amended to scRNAseq.

(2) Page 13, line 490: SC7A5?

This has been amended to SLC7A5

(3) The abbreviation CF (cholesterol-free?) is not defined when it first appears.

This has been amended to cholesterol-free (CF) on page 9, line 411.

Reviewer #2 (Public review):

The reviewer suggested that the study would be strengthened by determining whether the observed changes are specific to LPS + IL-4 stimulation or represent a more general B cell response to mitogenic signals. We believe that these effects are not specific to LPS and also occur with other mitogenic stimuli. We have expanded on the data in the original draft showing that other TLR agonists as well as CD40 and BCR stimulation increase both B cell proliferation and cholesterol levels and also looked at the effects of these stimuli on protein synthesis.

Reviewer #2 (Recommendations for the authors):

(1) One of the most highly enriched processes is 'response to interferon alpha'. This stands out as most of the other processes identified involve more general cellular processes (i.e., cell proliferation, cell metabolism, etc...). Minimally, interferon alpha should be discussed. It would also be interesting to test whether type I interferons regulate any of the metabolic changes identified.

Response to interferon alpha has the highest fold enrichment of 6.78. To look at this further compiled a list of proteins upregulated by IFN-α stimulation in murine B cells, derived from (Mostafavi et al, 2016) and compared these with our proteome. We found that most of the IFNα regulated genes were not significantly upregulated following LPS + IL-4 stimulation compared to naïve B cells (Figure S3A). We also measured phosphorylation of the transcription factor STAT1, which is induced by IFNα and IFNβ signalling, and found that LPS stimulation did not induce p-STAT1 (Figure S3B-C). These results have been added to the manuscript as Supplementary Figure 3. Despite this, as discussed further in the manuscript we cannot rule out a weak interferon response in the proteomics.

(2) The proteome of BCR-stimulated B cells has been analyzed by mass spectrometry. This dataset should be compared with the LPS + IL-4 dataset of the current study. This may reveal whether these two stimulations have similar or different effects on B-cell function. In particular, it is interesting to know whether BCR stimulation induces SLC7A5 expression and whether proteins involved in cholesterol metabolism are altered by BCR stimulation.

A similar study using anti-IgM and anti-CD40 to activate murine B cells has found an upregulation of amino acid transporters, including SLC7A5, in their proteomic data, suggesting that this is not a stimulus-specific effect. This has been added to the text subsection “Protein synthesis in LPS + IL-4 stimulated B cells is dependent on the uptake of amino acids.” In line with this we have also shown that stimulation of the BCR upregulates protein synthesis (new Supplementary Figure 4). We have added data on HMGCR, SQLE and LDLR form the BCR proteomics experiments to the new Supplementary Figure 13. As the BCR proteome published as a preprint (James et al 2024) is about to be resubmitted as a distinct paper that does not deal with cholesterol metabolism, we have not expanded on this dataset further.

(3) A role for mTORC1 has been shown for proteome remodelling following BCR stimulation of naïve B cells, regulating the expression of amino acid transporters. Is mTORC1 involved in any of the changes detected following LPS + IL-4 stimulation? (i.e., cell proliferation, ribosome biogenesis, amino acid transport, cholesterol biogenesis).

To determine the importance of mTORC1 for B cell function, we treated B cells with rapamycin. We found that rapamycin treatment slightly reduced protein synthesis (Figure S12A) and amino acid uptake (Figure S12B). These results have been added to the manuscript as Supplementary Figure 12. Rapamycin reduced cholesterol to almost the levels in naïve B cells (new Figure 9F) and had a significantly inhibitory effect on proliferation (new Figure 9A-B).

(4) Analysis of Slc7a5 knockout B cells showed that SLC7A5 is required for LPS-induced proliferation (Figure 4G). Is SLC7A5 required for B cell growth following LPS + IL-4 stimulation? Is SLC7A5 required for BCR-induced B cell proliferation/growth?

There appears to be a misunderstanding, as Figure 4G compares proliferation between WT and SLC7A5 KO B cells following LPS + IL-4 stimulation and not LPS stimulation alone.

Unfortunately, we no longer have access to Slc7a5fl/fl/Vav-iCre+/- mice and will not be able to measure CTV staining for proliferation following BCR stimulation. However, a similar study using anti-IgM and anti-CD40 to activate murine B cells found that B cells from Slc7a5fl/fl/Vav-iCre+/- mice were significantly smaller, had reduced expression of the chaperone protein CD98 and impaired expression of the transferrin receptor CD71, which is required for iron uptake, compared to WT B cells (James et al, 2024).

(5) The expression of several key proteins (regulating proliferation/amino acid transport/cholesterol metabolism) is shown to be significantly upregulated by LPS + IL-4 stimulation of naïve B cells. It would be interesting to determine whether these increases result from induced transcription of the relevant genes. This could initially be assessed by qRT-PCR analysis of LPS + IL-4 stimulated primary B cells, or alternatively, mining of online RNAseq datasets.

We mined RNA-Seq data from C57BL/6 mice (Tesi et al, 2019) which compared naïve B cells and B cells after 2,4, or 8 hours of LPS stimulation. We found that the transcription of genes that coded for the amino acid transporter SLC7A5/SLC3A2 (Figure S6A-B) and key genes involved in cholesterol metabolism followed the same pattern of upregulation as our proteomic data (Figure S6C-F). These results have been added to the manuscript as a new Supplementary Figure 6.

(6) Cholesterol levels are shown to be increased following resiquimod, CpG, anti-IgM, and CD40L stimulation (Figure 9). What effect do these agonists have on levels of HMGCR, SQLE, and LDLR in B cells? Is B-cell growth by these agonists impaired by Fluvastatin.

We found that stimulation of murine B cells with either IL-4, anti-IgM or anti-CD40 could increase levels of HMGCR, SQLE and LDLR, with the largest increase seen with a combination of these stimuli (Figure S13A-D) (James et al, 2024). These results have been added to the manuscript as Supplementary Figure 13.

Figures 10C-E show that B cell growth, survival and proliferation are impaired by Fluvastatin after Resiquimod, CpG, anti-IgM, and CD40L stimulation, although we do not have proteomic data from these stimuli to confirm the levels of HMGCR, SQLE and LDLR.

We carried out proteomics after 24 hours of LPS + IL-4 stimulation in normal/CF media, with or without Fluvastatin. We found that Fluvastatin treatment in normal media increased the expression of HMGCR, SQLE and LDLR. Fluvastatin treatment in CF media had the highest increase in the expression of these key proteins (Figure S9G-J). These results have been added to the manuscript as Supplementary Figure 9.

(7) Do Fluvastatin or FGTI-2734 affect early activation of signaling pathways by LPS + IL-4 stimulation of B cells? (eg. MAPKs, STATs, PI3K/AKT).

This is an interesting question, we will pursue this in our future work.

References:

James O, Sinclair LV, Lefter N, Salerno F, Brenes A & Howden AJM (2024) A proteomic map of B cell activation and its shaping by mTORC1, MYC and iron. bioRxiv 2024.12.19.629506 doi:10.1101/2024.12.19.629506

Xia Y, Xie Y, Yu Z, Xiao H, Jiang G, Zhou X, Yang Y, Li X, Zhao M, Li L, et al (2018) The Mevalonate Pathway Is a Druggable Target for Vaccine Adjuvant Discovery. Cell 175: 1059-1073.e21

eLife Assessment

This study represents a useful finding on the social modulation of the complex repertoire of vocalizations made across a variety of strains of lab mice. The evidence supporting the claims is, at present, incomplete, as numerous concerns regarding the appropriate categorization of vocalizations, the averaging of data points with disparate levels of occurrence, the interpretation of the function of noisy calls, and a general lack of adequate analyses of experimental data were raised. With these issues addressed, the work will be of importance to scientists studying rodent vocal communication.

Reviewer #1 (Public review):

Summary:

Adult laboratory mice produce ultrasonic vocalizations during free social interactions, as well as lower-frequency, voiced calls (squeaks) during aversive contexts. The question of whether mice possess a more complex repertoire of vocalizations has been of great interest to scientists studying rodent vocal behavior. In the current study, the authors analyze the rates and acoustic features of vocalizations produced by pairs of mice that are allowed to interact across a barrier, which prevents direct physical interaction. In this context, they find that same-sex (but not opposite-sex) pairs of mice produce vocalizations that are lower in frequency than the typical 70 kHz ultrasonic vocalizations produced during free interactions and that are also distinct from squeaks. These lower frequency vocalizations were observed in both male-male and female-female pairs, as well as in same-sex pairs from multiple mouse strains. The authors also report that call rates and acoustic features are not affected in male-male pairs that have been treated with the anxiolytic drug buspirone, suggesting that anxiety is not a major driver of vocalization in this behavioral context.

Strengths:

(1) The observation that same-sex pairs of mice produce lower frequency (<70 kHz) vocalizations in this behavioral context is novel.

(2) The consideration of multiple types of pairs (female-female, male-male, and female-male), as well as the inclusion of multiple strains of mice and barriers with different hole diameters, are all strengths of the study.

(3) The authors include detailed analyses of vocalization acoustic features, as well as detailed tracking of mouse positions relative to the barrier.

Weaknesses:

The categorization applied to vocalizations based on their mean frequencies is poorly supported and ignores the distinction in laryngeal production mechanism between voiced and ultrasonic vocalizations. Specifically, the authors are likely lumping together voiced and ultrasonic vocalizations into their "low frequency" (< 30 kHz) category, while they reserve the term "ultrasonic" exclusively for the subset of ultrasonic vocalizations with the highest mean frequencies (> 50 kHz). This categorization scheme also does not align well with past work on lower frequency rodent vocalizations, which complicates the comparison of the present findings to that past work.

In some analyses, the authors report that different groups of mice produce different relative proportions of vocalization types (as defined by mean frequency) but then compare acoustic features of vocalizations between groups after pooling all vocalizations together. The analyses of acoustic features conducted in this way may be confounded by the different proportions of vocalization types across groups.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors examine vocal communication during same-sex dyadic interactions in mice, comparing periods of physical separation (with limited sensory access) to direct social contact. They report that separation dramatically alters the vocal repertoire, shifting it away from canonical ultrasonic vocalizations (USVs) toward low-frequency vocalizations (LFVs) and broadband "noisy" calls. While LFVs and noisy calls have been described previously, largely in aversive contexts, this study provides a detailed, systematic characterization of these vocalizations during social interactions, thereby extending prior work.

The authors explore several experimental manipulations and analyses, including divider hole size, strain and sex differences, anxiolytic drug treatment, and correlations with spatial proximity, to infer potential functions of these call types. Although the dataset is rich, the results are largely descriptive, and many conclusions remain tentative. Several experimental variables are not fully controlled, and in some cases, the interpretation exceeds what the data can clearly support. Nonetheless, with improved experimental framing, additional analyses of existing data, and a clearer discussion of limitations, this work has the potential to make a valuable contribution by broadening the field's focus beyond USVs to understand a wider vocal repertoire relevant to social context.

Strengths:

Much work on mouse vocal communication focuses almost exclusively on USVs. This manuscript convincingly demonstrates that non-USV vocalizations (LFVs and noisy calls) are prominent and systematically modulated by social context, highlighting an underappreciated dimension of mouse communication. Furthermore, the authors employ several experimental manipulations, including sensory access, strain, sex, and pharmacological treatment, to assess changes in vocalization repertoire. This provides a valuable resource for the field and reveals robust context dependence of vocalization. The discussion is thoughtful and integrative, particularly in its consideration of potential communicative roles of LFVs and noisy calls and their relationship to sensory constraints and signal propagation, although these ideas will require further experimental validation.

Weaknesses:

There are several concerns regarding experimental design and data interpretation that could be addressed to strengthen the manuscript.

(1) The terminology used for vocalization types is confusing and needs better clarification. The authors refer to Grimsley et al. (2016) multiple times, yet they use the same names for their vocalizations while applying different definitions. This makes it very difficult to compare the two papers. Since this study and Grimsley et al. use different mouse strains (FVB vs CBA), a direct comparison of absolute frequencies may also not be appropriate. Please explicitly clarify the definitions of the call types (e.g., frequency range, voiced vs. USV) and explain how they relate to those in the previous study earlier in the manuscript.

(2) In the initial experiment, mice always experience separation first (15 minutes), followed by unification (5 minutes), using novel same-sex dyads. Multiple factors besides physical contact could influence vocalization across this sequence, including habituation to the arena, reduced anxiety over time, or increasing familiarity with the partner despite physical separation. It is unclear whether the authors have tested the reverse order (unification first, followed by separation). If not, this limitation should be explicitly acknowledged. In addition, examining whether vocalizations or behaviors change over the course of the 15-minute separation period, for example, by comparing early vs late phases, could help disentangle effects of habituation from those of physical separation per se.

(3) The conclusion that separation-induced LFVs are unlikely to be anxiety-driven may overinterpret the buspirone experiment (Figure 8). Vehicle injections themselves produced large changes in call rate and call-type distribution, raising concerns about stress or arousal induced by the injection procedure. Comparisons between buspirone-treated animals and untreated animals are therefore problematic, as these groups differ in their experimental histories, including the number of exposures. The manuscript would benefit from independent measures confirming the anxiolytic efficacy of buspirone compared to vehicle injection in this paradigm, such as behavioral readouts of anxiety. In addition, the experimental design requires a clearer description. It is not always clear whether the same dyads were tested twice, or how social familiarity, contextual familiarity, and habituation to injections were handled. Male data comparing first and second exposures should also be included as supplementary figures to allow direct comparison with the excluded female dataset.

(4) The idea that noisy calls function to attract conspecific attention is intriguing. However, in Figure 5, all call types, including LFVs and USVs, are most likely to occur when mice are already in close proximity during separation, which seems inconsistent with a long-distance signaling role. Analyses of the temporal relationship between vocalizations and behavior would strengthen this claim. For example, it would be informative to test whether bouts of noisy calls precede approach behavior or a reduction in inter-animal distance. Examining whether calls occur before, during, or after orientation toward the partner could further clarify whether these vocalizations actively modulate social behavior.

(5) The effects of divider hole size on vocal repertoire are striking but difficult to interpret. Unexpectedly, small holes and no holes yield similar call distributions, whereas large holes produce a markedly different profile dominated by LFVs, which also differs from free interactions. If large holes allow greater tactile or close-range interaction, the reduction in USVs and MFV is counterintuitive. Incorporating behavioral metrics such as distance, orientation, or specific interaction types alongside call classification would greatly aid interpretation and help link vocal output to interaction quality rather than divider type alone.

(6) Throughout the study, vocalizations are pooled across both animals in the dyad. Because the arena is neutral rather than a home cage, either animal could be initiating vocalization. Assigning calls to individuals, where possible, using spatial or acoustic cues, would substantially strengthen functional interpretations. Even limited analyses, e.g., identifying which animal vocalizes first or whether calls precede approach by the partner, could provide important insight into the communicative role of different call types.

Author Response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Adult laboratory mice produce ultrasonic vocalizations during free social interactions, as well as lower-frequency, voiced calls (squeaks) during aversive contexts. The question of whether mice possess a more complex repertoire of vocalizations has been of great interest to scientists studying rodent vocal behavior. In the current study, the authors analyze the rates and acoustic features of vocalizations produced by pairs of mice that are allowed to interact across a barrier, which prevents direct physical interaction. In this context, they find that same-sex (but not opposite-sex) pairs of mice produce vocalizations that are lower in frequency than the typical 70 kHz ultrasonic vocalizations produced during free interactions and that are also distinct from squeaks. These lower frequency vocalizations were observed in both male-male and female-female pairs, as well as in same-sex pairs from multiple mouse strains. The authors also report that call rates and acoustic features are not affected in male-male pairs that have been treated with the anxiolytic drug buspirone, suggesting that anxiety is not a major driver of vocalization in this behavioral context.

Strengths:

(1) The observation that same-sex pairs of mice produce lower frequency (<70 kHz) vocalizations in this behavioral context is novel.

(2) The consideration of multiple types of pairs (female-female, male-male, and female-male), as well as the inclusion of multiple strains of mice and barriers with different hole diameters, are all strengths of the study.

(3) The authors include detailed analyses of vocalization acoustic features, as well as detailed tracking of mouse positions relative to the barrier.

Weaknesses:

The categorization applied to vocalizations based on their mean frequencies is poorly supported and ignores the distinction in laryngeal production mechanism between voiced and ultrasonic vocalizations. Specifically, the authors are likely lumping together voiced and ultrasonic vocalizations into their "low frequency" (< 30 kHz) category, while they reserve the term "ultrasonic" exclusively for the subset of ultrasonic vocalizations with the highest mean frequencies (> 50 kHz). This categorization scheme also does not align well with past work on lower frequency rodent vocalizations, which complicates the comparison of the present findings to that past work.

We thank the reviewer for their assessment. Firstly, we did not use mean frequencies, but peak frequencies of each single call.

The distinction between ‘voiced’ and ‘whistled’ vocalizations based on their spectral-temporal features is hardly possible. While evidence in form of audio recordings made from both deer mouse and grasshopper mouse in helium-enriched air suggests vocalizations with lower fundamental frequency being ‘voiced’ (Pasch et al., 2017; Riede et al., 2022), a computational model considering the laryngeal anatomy of Mus musculus estimates fundamental frequencies of vocalizations at subglottal phonation threshold pressures usual for USVs to be in the range of 1 – 5 kHz and approaching 10 kHz for higher subglottal pressures usually found in the production of ‘voiced’ vocalizations (Pasch et al., 2017). Furthermore, a recent study in the singing mouse (Scotinomys teguina) found minimal fundamental frequencies of single song notes, produced by a whistle mechanism, to be about 4 kHz (Zheng et al., 2025). Thus, the presence of low fundamental (peak) frequencies in mouse vocalizations alone appears to be insufficient for deducing the production mechanism of these vocalizations.

We did not observe differences in acoustic features clearly separating our ‘LFV’ calls into two groups suggestive of different production mechanisms. Thus, we cannot rule out that our ‘LFV’ class contains vocalizations produced by different mechanisms. However, we did not observe any squeaks in our experiments and can therefore rule out that this prominent type of ‘voiced’ call is lumped together with other calls in the ‘LFV’ calls.

While the questions regarding production mechanism, the neurocircuitry involved, and the context-dependent choice of which mechanism to use is intriguing/enticing, the distinction between ‘voiced’ and ‘whistled’ vocalizations lies beyond the scope of our manuscript. Instead, the neurocircuitry involved in mouse vocalization production, particularly USVs and squeaks has been revealed by other laboratories. Optogenetical activation of RAm Nts neurons elicited emission of both audible vocalizations (fundamental frequencies of 10 kHz and below) and USVs in awake mice in a stimulus-dependent manner (Veerakumar et al., 2023). Furthermore, optogenetical activation of RAm-vocalization neurons led to immediate measurable adduction of vocal folds and emission of canonical USVs (Park et al., 2024). While different populations of PAG neurons are responsible for the production both squeaks and USVs (Ziobro et al., 2024), the two input streams seem to converge on RAm vocalization neurons, as silencing the output of these neurons abolished both squeak and USV emission completely (Park et al., 2024). Thus, while near complete closing of the vocal folds is necessary for the production of canonical USVs (Mahrt et al., 2016; Park et al., 2024), it is not clear which degree of vocal fold opening would result in what fundamental frequencies.

We will add a paragraph on this issue to the discussion in the next version of the manuscript.

In some analyses, the authors report that different groups of mice produce different relative proportions of vocalization types (as defined by mean frequency) but then compare acoustic features of vocalizations between groups after pooling all vocalizations together. The analyses of acoustic features conducted in this way may be confounded by the different proportions of vocalization types across groups.

We displayed the relative distribution of the different call classes demonstrating that 80% of the call repertoire during the separation consisted of noisy calls and ‘LFV’. Thus, the per individual averaged acoustic features e.g. peak frequency would be predominantly shaped by the features of these two call classes. However, we agree with the reviewer’s criticism and will provide a more detailed display and analysis of the acoustic features of each call class.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors examine vocal communication during same-sex dyadic interactions in mice, comparing periods of physical separation (with limited sensory access) to direct social contact. They report that separation dramatically alters the vocal repertoire, shifting it away from canonical ultrasonic vocalizations (USVs) toward low-frequency vocalizations (LFVs) and broadband "noisy" calls. While LFVs and noisy calls have been described previously, largely in aversive contexts, this study provides a detailed, systematic characterization of these vocalizations during social interactions, thereby extending prior work.

The authors explore several experimental manipulations and analyses, including divider hole size, strain and sex differences, anxiolytic drug treatment, and correlations with spatial proximity, to infer potential functions of these call types. Although the dataset is rich, the results are largely descriptive, and many conclusions remain tentative. Several experimental variables are not fully controlled, and in some cases, the interpretation exceeds what the data can clearly support. Nonetheless, with improved experimental framing, additional analyses of existing data, and a clearer discussion of limitations, this work has the potential to make a valuable contribution by broadening the field's focus beyond USVs to understand a wider vocal repertoire relevant to social context.

Strengths:

Much work on mouse vocal communication focuses almost exclusively on USVs. This manuscript convincingly demonstrates that non-USV vocalizations (LFVs and noisy calls) are prominent and systematically modulated by social context, highlighting an underappreciated dimension of mouse communication. Furthermore, the authors employ several experimental manipulations, including sensory access, strain, sex, and pharmacological treatment, to assess changes in vocalization repertoire. This provides a valuable resource for the field and reveals robust context dependence of vocalization. The discussion is thoughtful and integrative, particularly in its consideration of potential communicative roles of LFVs and noisy calls and their relationship to sensory constraints and signal propagation, although these ideas will require further experimental validation.

Weaknesses:

There are several concerns regarding experimental design and data interpretation that could be addressed to strengthen the manuscript.

(1) The terminology used for vocalization types is confusing and needs better clarification. The authors refer to Grimsley et al. (2016) multiple times, yet they use the same names for their vocalizations while applying different definitions. This makes it very difficult to compare the two papers. Since this study and Grimsley et al. use different mouse strains (FVB vs CBA), a direct comparison of absolute frequencies may also not be appropriate. Please explicitly clarify the definitions of the call types (e.g., frequency range, voiced vs. USV) and explain how they relate to those in the previous study earlier in the manuscript.

The existence and use of various distinct classification systems for mouse vocalizations is well known and the need to agree on a common classification system is consensus in the field. Thus, it was not our intention to complicate mouse call classification even more.

Grimsley at al. (2016) reserve the ‘low frequency’ band solely for squeaks (or “low frequency harmonics”). Hence, it appears straight forward to name mouse calls with “mean dominant frequencies” falling between squeaks and USVs, “mid-frequency tonal vocalizations (MFVs)” (Grimsley et al., 2016). We did not observe the emission of squeaks in our experiments, but instead we observed tonal vocalizations in a peak frequency spectrum encompassing both squeaks and Grimsley and colleagues’ ‘MFVs’, representing the lowest peak frequencies we observed (< 32 kHz). Furthermore, we observed vocalizations in the range of 32 – 50 kHz (which were not low frequency components of canonical USVs) and of > 50 kHz (corresponding to canonical USVs). Leaning on the terminology of Grimsley and colleagues (2016), we thought it to be straightforward to name these call classes according to their location on the frequency spectrum: low frequency vocalizations (LFVs; up to 32 kHz), encompassing squeaks, but also Grimsley and colleagues’ MFVs, middle frequency vocalizations (MFVs; 32 – 50 kHz), and finally canonical USVs (> 50 kHz). Admittedly, choosing ‘MFVs’ for mouse calls with different acoustic features than those described by Grimsley and colleagues (2016) has caused unnecessary confusion. We therefore consider adapting our classification scheme for the next version of the manuscript.

Regarding the comparison of call classes between different mouse strains, strain differences of spectral-temporal features of call classes have been described for canonical USVs (e.g. Scattoni et al., 2008). However, the acoustic features as well as call repertoire are still quite comparable. Furthermore, we have additionally tested both CBA/J and C57BL/6J mice in our study confirming the presence of both noisy calls, ‘LFVs’, ‘MFVs’, and ‘USVs’ in the vocal repertoire of these two strains.

We will provide a more detailed display and analysis of the acoustic features of the call classes with the next version of the manuscript.

(2) In the initial experiment, mice always experience separation first (15 minutes), followed by unification (5 minutes), using novel same-sex dyads. Multiple factors besides physical contact could influence vocalization across this sequence, including habituation to the arena, reduced anxiety over time, or increasing familiarity with the partner despite physical separation. It is unclear whether the authors have tested the reverse order (unification first, followed by separation). If not, this limitation should be explicitly acknowledged. In addition, examining whether vocalizations or behaviors change over the course of the 15-minute separation period, for example, by comparing early vs late phases, could help disentangle effects of habituation from those of physical separation per se.

We had not tested mice in the reverse order, beginning with 5 minutes of unification followed by 15 minutes of separation. Therefore, we acknowledge this limitation of our study and will address it explicitly in the next version of our manuscript. We appreciate the reviewer’s note regarding the inclusion of vocalizations over time and aim to provide this analysis in the next version of the manuscript.

(3) The conclusion that separation-induced LFVs are unlikely to be anxiety-driven may overinterpret the buspirone experiment (Figure 8). Vehicle injections themselves produced large changes in call rate and call-type distribution, raising concerns about stress or arousal induced by the injection procedure. Comparisons between buspirone-treated animals and untreated animals are therefore problematic, as these groups differ in their experimental histories, including the number of exposures. The manuscript would benefit from independent measures confirming the anxiolytic efficacy of buspirone compared to vehicle injection in this paradigm, such as behavioral readouts of anxiety. In addition, the experimental design requires a clearer description. It is not always clear whether the same dyads were tested twice, or how social familiarity, contextual familiarity, and habituation to injections were handled. Male data comparing first and second exposures should also be included as supplementary figures to allow direct comparison with the excluded female dataset.

We agree with the reviewer’s point that the injection procedure itself appeared to have an impact on vocalization behavior. In fact, we had included the ‘untreated’ cohort in Fig. 8 despite their different experimental history to appreciate the potential impact of injection onto vocal behavior.

Furthermore, we appreciate the reviewer’s point of confirming the anxiolytic effect of buspirone treatment with further behavioral readouts and aim to provide such analysis in the next version of the manuscript.

Regarding the reviewer’s query for clearer experimental design description, the same dyads were tested twice. All mice lived in groups in their home cage, however, they had not met the individual they would face during the experiment before the first experiment. We will improve the description of the experimental design addressing the reviewer’s points in the next version of the manuscript.

(4) The idea that noisy calls function to attract conspecific attention is intriguing. However, in Figure 5, all call types, including LFVs and USVs, are most likely to occur when mice are already in close proximity during separation, which seems inconsistent with a long-distance signaling role. Analyses of the temporal relationship between vocalizations and behavior would strengthen this claim. For example, it would be informative to test whether bouts of noisy calls precede approach behavior or a reduction in inter-animal distance. Examining whether calls occur before, during, or after orientation toward the partner could further clarify whether these vocalizations actively modulate social behavior.

We appreciate the reviewer’s remarks regarding the apparent inconsistencies between noisy calls as conspecific attraction calls and their occurrence in close mouse-to-mouse proximity. We must concede that the size of our testing arena limited the maximum distances mice could achieve. Thus, we aim to provide a more extensive analysis including approach behavior and changes of inter-animal distances for resubmission of the manuscript as suggested by the reviewer.

(5) The effects of divider hole size on vocal repertoire are striking but difficult to interpret. Unexpectedly, small holes and no holes yield similar call distributions, whereas large holes produce a markedly different profile dominated by LFVs, which also differs from free interactions. If large holes allow greater tactile or close-range interaction, the reduction in USVs and MFV is counterintuitive. Incorporating behavioral metrics such as distance, orientation, or specific interaction types alongside call classification would greatly aid interpretation and help link vocal output to interaction quality rather than divider type alone.

We agree with the reviewer that the interpretation of the divider-hole-size-experiment are difficult and following this reviewer’s input, aim to provide additional behavioral analysis for the effect of divider hole size with the next version of the manuscript.

(6) Throughout the study, vocalizations are pooled across both animals in the dyad. Because the arena is neutral rather than a home cage, either animal could be initiating vocalization. Assigning calls to individuals, where possible, using spatial or acoustic cues, would substantially strengthen functional interpretations. Even limited analyses, e.g., identifying which animal vocalizes first or whether calls precede approach by the partner, could provide important insight into the communicative role of different call types.

We agree with the points raised by the reviewer regarding the importance of assigning recorded calls to the respective individual for deciphering the communicative role of different call types. Unfortunately, our system was only equipped with one condenser microphone therefore we are not able to assign calls to individual mice.

Literature:

Grimsley, J. M. S., Sheth, S., Vallabh, N., Grimsley, C. A., Bhattal, J., Latsko, M., Jasnow, A., & Wenstrup, J. J. (2016). Contextual Modulation of Vocal Behavior in Mouse: Newly Identified 12 kHz „Mid-Frequency“ Vocalization Emitted during Restraint. Frontiers in Behavioral Neuroscience, 10, 38. https://doi.org/10.3389/fnbeh.2016.00038

Mahrt, E., Agarwal, A., Perkel, D., Portfors, C., & Elemans, C. P. H. (2016). Mice produce ultrasonic vocalizations by intra-laryngeal planar impinging jets. Current Biology: CB, 26(19), R880–R881. https://doi.org/10.1016/j.cub.2016.08.032

Park, J., Choi, S., Takatoh, J., Zhao, S., Harrahill, A., Han, B.-X., & Wang, F. (2024). Brainstem control of vocalization and its coordination with respiration. Science (New York, N.Y.), 383(6687), eadi8081. https://doi.org/10.1126/science.adi8081

Pasch, B., Tokuda, I. T., & Riede, T. (2017). Grasshopper mice employ distinct vocal production mechanisms in different social contexts. Proceedings. Biological Sciences, 284(1859), 20171158. https://doi.org/10.1098/rspb.2017.1158

Riede, T., Kobrina, A., Bone, L., Darwaiz, T., & Pasch, B. (2022). Mechanisms of sound production in deer mice (Peromyscus spp.). The Journal of Experimental Biology, 225(9), jeb243695. https://doi.org/10.1242/jeb.243695

Scattoni, M. L., Gandhy, S. U., Ricceri, L., & Crawley, J. N. (2008). Unusual repertoire of vocalizations in the BTBR T+tf/J mouse model of autism. PloS One, 3(8), e3067. https://doi.org/10.1371/journal.pone.0003067

Veerakumar, A., Head, J. P., & Krasnow, M. A. (2023). A brainstem circuit for phonation and volume control in mice. Nature Neuroscience, 26(12), 2122–2130. https://doi.org/10.1038/s41593-023-01478-2

Zheng, X. M., Harpole, C. E., Davis, M. B., & Banerjee, A. (2025). Vocal repertoire expansion in singing mice by co-opting a conserved midbrain circuit node. Current Biology: CB, 35(23), 5762-5778.e6. https://doi.org/10.1016/j.cub.2025.10.036

Ziobro, P., Woo, Y., He, Z., & Tschida, K. (2024). Midbrain neurons important for the production of mouse ultrasonic vocalizations are not required for distress calls. Current Biology: CB, 34(5), 1107-1113.e3. https://doi.org/10.1016/j.cub.2024.01.016

eLife Assessment

This important paper substantially advances our understanding of how Molidustat may work, beyond its canonical role, by identifying its therapeutic targets in cancer. This study presents a compelling and well-structured investigation into the therapeutic vulnerabilities of APC-mutant colorectal cancer. This work will be of broad interest to the cancer community in studying small molecules and their therapeutic targets.

Reviewer #1 (Public review):

Summary:

The authors aimed to uncover novel therapeutic vulnerabilities in APC-mutant colorectal cancer (CRC), which constitutes the majority of CRC cases. They hypothesized that modulating oxygen-sensing pathways (via PHD inhibition) could disrupt adaptive stress responses in these tumours.

Strengths:

The study employs a powerful, two-pronged approach to identify Molidustat's targets. By using both Thermal Proteome Profiling (TPP) and an orthogonal chemical proteomic competition assay, the authors provide compelling evidence that GSTP1 is a genuine, direct off-target, effectively addressing the common limitation of indirect effects in proteomic screens.

Weaknesses:

(1) In Figure 1, the current data rely on a single guide RNA (sgRNA). To make the data solid, at least two independent sgRNAs targeting different regions of PHD2 should be used.

(2) Figure 3E: Asn205 site should be mutated to prove that whether Molidustat inhibits GSTP1 activity via Asn205 or not.

(3) Figure 5B and 5C: The metabolic imbalance phenotype observed upon dual knockout of PHD2 and GSTP1 requires rescue experiments to confirm on-target specificity.

Reviewer #2 (Public review):

Summary:

The authors aimed to determine Molidustat targets and the potential utility of these findings. They clearly demonstrate that Molidustat interferes with GSTP1 and some other proteins on top of PHD2. They also demonstrate that PHD2 deletion is not sufficient to recapitulate Molidustat effects in cells and proteomes. Finally, they demonstrate synthetic lethality in organoids for Molidustat and APC deletion.

Strengths:

The data on Molidustat proteomes, GSTP1 binding, inhibition and metabolic health of organoids is really clear. All biochemical, docking and omic data are really strong. The potential impact of these findings could be the use of Molidustat in APC null tumours and awareness of potential off-target effects.

Weaknesses:

A main but minor weakness is that Molidustat also inhibits other PHDs, although these are less expressed. PHD1 has been shown to control the cell cycle and be expressed in the colon, where it is needed for viability. Although this does not explain the lack of effect of other PHD inhibitors, it does warrant some discussion. The use of MTT is not very good to detect viability when it measures metabolism; this also needs to be discussed and perhaps supplemented with colony or cell number measurements.

Reviewer #3 (Public review):

In this paper, the authors revealed that Molidustat can induce a dose-dependent increase in Caspase-3/7 activity in the HT29 cell line, which is an APC-mutant colorectal cancer cell line. More importantly, they found that targeting PHD2 alone cannot cause cell death. By using thermal proteome profiling (TPP) and orthogonal chemical proteomic competition assays, they determined GTSP1 as a previously undiscovered off-target of Molidustat. They also revealed that combined PHD2 and GSTP1 loss leads to an increase in intracellular ROS and apoptosis. Moreover, they evaluated the effects of Molidustat in colonic organoids and showed that Molidustat has a high selectivity for colonic organoids with activated WNT signaling and/or KRAS pathway alterations, and this effect is not reproduced by hydroxylase inhibition alone, providing a new potential approach to targeting both PHD2 and GTSP1 for the treatment of APC-mutant CRC.

Specific comments:

(1) What is the possible molecular mechanism of dual GSTP1/PHD2 loss, inducing cell death?

(2) Can the authors mutate the binding site of Molidustat on GTSP1 to verify the in silico docking results?

(3) Evidence for Molidustat inhibiting PHD2 activity or stabilising HIF-1α should be provided.

eLife Assessment

This study offers valuable insights into how humans detect and adapt to regime shifts, highlighting dissociable contributions of the frontoparietal network and ventromedial prefrontal cortex to sensitivity to signal diagnosticity and transition probabilities. The combination of an innovative instructed-probability task, Bayesian behavioural modelling, and model-based fMRI analyses provides solid support for the main claims. The addition of new model-comparison figures in revision effectively addresses the previously noted potential confound between posterior switch probability and time in the neuroimaging results. At the behavioural level, while the computational model captures the pattern of "system neglect" well, qualitatively distinct mechanisms, such as hyper-prior attraction toward experiment-wise mean parameters, reporting biases, or probability-outlier underweighting, could produce similar behavioural signatures and cannot be fully disambiguated with the current design alone; however, converging evidence from the authors' prior work partially mitigates this concern.

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

- The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

- The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

- The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Weaknesses:

The authors have adequately addressed my prior concerns.

Reviewer #3 (Public review):

This study concerns how observers (human participants) detect changes in the statistics of their environment, termed regime shifts. To make this concrete, a series of 10 balls are drawn from an urn that contains mainly red or mainly blue balls. If there is a regime shift, the urn is changed over (from mainly red to mainly blue) at some point in the 10 trials. Participants report their belief that there has been a regime shift as a % probability. Their judgement should (mathematically) depend on the prior probability of a regime shift (which is set at one of three levels) and the strength of evidence (also one of three levels, operationalized as the proportion of red balls in the mostly-blue urn and vice versa). Participants are directly instructed of the prior probability of regime shift and proportion of red balls, which are presented on-screen as numerical probabilities. The task therefore differs from most previous work on this question in that probabilities are instructed rather than learned by observation, and beliefs are reported as numerical probabilities rather than being inferred from participants' choice behaviour (as in many bandit tasks, such as Behrens 2007 Nature Neurosci).

The key behavioural finding is that participants over-estimate the prior probability of regime change when it is low, and under estimate it when it is high; and participants over-estimate the strength of evidence when it is low and under-estimate it when it is high. In other words participants make much less distinction between the different generative environments than an optimal observer would. This is termed 'system neglect'. A neuroeconomic-style mathematical model is presented and fit to data.

Functional MRI results how that strength of evidence for a regime shift (roughly, the surprise associated with a blue ball from an apparently red urn) is associated with activity in the frontal-parietal orienting network. Meanwhile at time-points where the probability of a regime shift is high, there is activity in another network including vmPFC. Both networks show individual differences effects, such that people who were more sensitive to strength of evidence and prior probability show more activity in the frontal-parietal and vmPFC-linked networks respectively.

Strengths

(1) The study provides a different task for looking at change-detection and how this depends on estimates of environmental volatility and sensory evidence strength, in which participants are directly and precisely informed of the environmental volatility and sensory evidence strength rather than inferring them through observation as in most previous studies

(2) Participants directly provide belief estimates as probabilities rather than experimenters inferring them from choice behaviour as in most previous studies

(3) The results are consistent with well-established findings that surprising sensory events activate the frontal-parietal orienting network whilst updating of beliefs about the word ('regime shift') activates vmPFC.

Weaknesses

(1) The use of numerical probabilities (both to describe the environments to participants, and for participants to report their beliefs) may be problematic because people are notoriously bad at interpreting probabilities presented in this way, and show poor ability to reason with this information (see Kahneman's classic work on probabilistic reasoning, and how it can be improved by using natural frequencies). Therefore the fact that, in the present study, people do not fully use this information, or use it inaccurately, may reflect the mode of information delivery.

In the response to this comment the authors have pointed out their own previous work showing that system neglect can occur even when numerical probabilities are not used. This is reassuring but there remains a large body of classic work showing that observers do struggle with conditional probabilities of the type presented in the task,

(2) Although a very precise model of 'system neglect' is presented, many other models could fit the data.

For example, you would get similar effects due to attraction of parameter estimates towards a global mean - essentially application of a hyper-prior in which the parameters applied by each participant in each block are attracted towards the experiment-wise mean values of these parameters. For example, the prior probability of regime shift ground-truth values [0.01, 0.05, 0.10] are mapped to subjective values of [0.037, 0.052, 0.069]; this would occur if observers apply a hyper-prior that the probability of regime shift is about 0.05 (the average value over all blocks). This 'attraction to the mean' is a well-established phenomenon and cannot be ruled out with the current data (I suppose you could rule it out by comparing to another dataset in which the mean ground-truth value was different).

More generally, any model in which participants don't fully use the numerical information they were given would produce apparent 'system neglect'. Four qualitatively different example reasons are: 1. Some individual participants completely ignored the probability values given. 2. Participants did not ignore the probability values given, but combined them with a hyperprior as above. 3. Participants had a reporting bias where their reported beliefs that a regime-change had occurred tend to be shifted towards 50% (rather than reporting 'confident' values such 5% or 95%). 4. Participants underweighted probability outliers resulting in underweighting of evidence in the 'high signal diagnosticity' environment (10.1016/j.neuron.2014.01.020 )

In summary I agree that any model that fits the data would have to capture the idea that participants don't differentiate between the different environments as much as they should, but I think there are a number of qualitatively different reasons why they might do this - of which the above are only examples.

Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

This study offers valuable insights into how humans detect and adapt to regime shifts, highlighting dissociable contributions of the frontoparietal network and ventromedial prefrontal cortex to sensitivity to signal diagnosticity and transition probabilities. The combination of an innovative instructed-probability task, Bayesian behavioural modeling, and model-based fMRI analyses provides a solid foundation for the main claims; however, major interpretational limitations remain, particularly a potential confound between posterior switch probability and time in the neuroimaging results. At the behavioural level, reliance on explicitly instructed conditional probabilities leaves open alternative explanations that complicate attribution to a single computational mechanism, such that clearer disambiguation between competing accounts and stronger control of temporal and representational confounds would further strengthen the evidence.

Thank you. In this revision, we addressed Reviewer 3’s remaining concern on the potential confound between posterior probability and time in neuroimaging results. First, as suggested by the reviewer, we provided images of activations for the effect of Pt and delta Pt after controlling for intertemporal prior in GLM-2. Second, we compared the effect of Pt and delta Pt between GLM-1 (without intertemporal prior) and GLM-2 (with intertemporal prior) and showed the results in a new figure (Figure 4).

Regarding issue on reliance on explicitly instructed probabilities, we wish to point out that most of the concerns such as response mode and regression to the mean were addressed in the original behavioral paper by Massey and Wu (2005). Please see our response to this point in detail in Weakness (2) posted by Reviewer 3.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

- The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

- The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

- The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Weaknesses:

The authors have adequately addressed my prior concerns.

Thank you for reviewing our paper and providing constructive comments that helped us improve our paper.

Reviewer #3 (Public review):

Thank you again for reviewing the manuscript. In this revision, we focused on addressing your concern on the potential confound between posterior probability and time in neuroimaging results. First, we presented whole-brain results of subjects’ probability estimates (Pt, their subjective posterior probability of switch) after controlling for the effect of time on probability of switch (the intertemporal prior). Second, we compared the effect of probability estimates (Pt) on vmPFC and ventral striatum activity—which we found to correlate with Pt—with and without including intertemporal prior in the GLM. These results will be summarized in a new figure (Figure 4) in the revised manuscript.

As suggested by the reviewer, we also added slice-by-slice images of the whole-brain results on Pt and delta Pt in the supplement in addition to the Tables of Activation so that the activated brain regions can be clearly seen through these images.

This study concerns how observers (human participants) detect changes in the statistics of their environment, termed regime shifts. To make this concrete, a series of 10 balls are drawn from an urn that contains mainly red or mainly blue balls. If there is a regime shift, the urn is changed over (from mainly red to mainly blue) at some point in the 10 trials. Participants report their belief that there has been a regime shift as a % probability. Their judgement should (mathematically) depend on the prior probability of a regime shift (which is set at one of three levels) and the strength of evidence (also one of three levels, operationalized as the proportion of red balls in the mostly-blue urn and vice versa). Participants are directly instructed of the prior probability of regime shift and proportion of red balls, which are presented on-screen as numerical probabilities. The task therefore differs from most previous work on this question in that probabilities are instructed rather than learned by observation, and beliefs are reported as numerical probabilities rather than being inferred from participants' choice behaviour (as in many bandit tasks, such as Behrens 2007 Nature Neurosci).

The key behavioural finding is that participants over-estimate the prior probability of regime change when it is low, and under estimate it when it is high; and participants over-estimate the strength of evidence when it is low and under-estimate it when it is high. In other words participants make much less distinction between the different generative environments than an optimal observer would. This is termed 'system neglect'. A neuroeconomic-style mathematical model is presented and fit to data.

Functional MRI results how that strength of evidence for a regime shift (roughly, the surprise associated with a blue ball from an apparently red urn) is associated with activity in the frontal-parietal orienting network. Meanwhile at time-points where the probability of a regime shift is high, there is activity in another network including vmPFC. Both networks show individual differences effects, such that people who were more sensitive to strength of evidence and prior probability show more activity in the frontal-parietal and vmPFC-linked networks respectively.

Strengths

(1) The study provides a different task for looking at change-detection and how this depends on estimates of environmental volatility and sensory evidence strength, in which participants are directly and precisely informed of the environmental volatility and sensory evidence strength rather than inferring them through observation as in most previous studies

(2) Participants directly provide belief estimates as probabilities rather than experimenters inferring them from choice behaviour as in most previous studies

(3) The results are consistent with well-established findings that surprising sensory events activate the frontal-parietal orienting network whilst updating of beliefs about the word ('regime shift') activates vmPFC.

Weaknesses

(1) The use of numerical probabilities (both to describe the environments to participants, and for participants to report their beliefs) may be problematic because people are notoriously bad at interpreting probabilities presented in this way, and show poor ability to reason with this information (see Kahneman's classic work on probabilistic reasoning, and how it can be improved by using natural frequencies). Therefore the fact that, in the present study, people do not fully use this information, or use it inaccurately, may reflect the mode of information delivery.

In the response to this comment the authors have pointed out their own previous work showing that system neglect can occur even when numerical probabilities are not used. This is reassuring but there remains a large body of classic work showing that observers do struggle with conditional probabilities of the type presented in the task.

Thank you. Yes, people do struggle with conditional probabilities in many studies. However, as our previous work suggested (Massey and Wu, 2005), system-neglect was likely not due to response mode (having to enter probability estimates or making binary predictions, and etc.).

(2) Although a very precise model of 'system neglect' is presented, many other models could fit the data.

For example, you would get similar effects due to attraction of parameter estimates towards a global mean - essentially application of a hyper-prior in which the parameters applied by each participant in each block are attracted towards the experiment-wise mean values of these parameters. For example, the prior probability of regime shift ground-truth values [0.01, 0.05, 0.10] are mapped to subjective values of [0.037, 0.052, 0.069]; this would occur if observers apply a hyper-prior that the probability of regime shift is about 0.05 (the average value over all blocks). This 'attraction to the mean' is a well-established phenomenon and cannot be ruled out with the current data (I suppose you could rule it out by comparing to another dataset in which the mean ground-truth value was different).

More generally, any model in which participants don't fully use the numerical information they were given would produce apparent 'system neglect'. Four qualitatively different example reasons are: 1. Some individual participants completely ignored the probability values given. 2. Participants did not ignore the probability values given, but combined them with a hyperprior as above. 3. Participants had a reporting bias where their reported beliefs that a regime-change had occurred tend to be shifted towards 50% (rather than reporting 'confident' values such 5% or 95%). 4. Participants underweighted probability outliers, resulting in underweighting of evidence in the 'high signal diagnosticity' environment (10.1016/j.neuron.2014.01.020 )

In summary I agree that any model that fits the data would have to capture the idea that participants don't differentiate between the different environments as much as they should, but I think there are a number of qualitatively different reasons why they might do this - of which the above are only examples - hence I find it problematic that the authors present the behaviour as evidence for one extremely specific model.

We thank the reviewer for this comment. We thank you for putting out that there are alternative models that can describe the over- and underreaction seen in the dataset. Massey and Wu (2005) dealt with this possibility in their original paper. Their concern was not so much about alternative ways of modeling their results, but in terms of alternative psychological processes. For example, asymmetric noise accounts have been posited in the judgment and decision making literature as possible accounts of phenomena like over-confidence. They addressed what might be crudely called “regression/attraction to the mean” in two ways. First, they looked at median responses as well as mean responses (because medians are less affected by the regressive effect) and found the same patterns of over- and underreactions. Second, they also generated sequences that matched particular posterior probabilities (so that over- and underreaction cannot be explained by regression to the mean) and still found under- and overreactions.

We also wish to point out in the judgment and decision making literature starting from Edwards (1968), there is a long history of using normative Bayesian model as the starting model and subsequently develop quasi-Bayesian models (like the system-neglect model) to describe systematic deviations from the normative Bayesian.

Finally, we want to clarify that our primary goal is not to engage in model fitting exercise that examines different possible models. To us, what is more important is that system neglect is a psychologically motivated hypothesis. It is built on the idea that the lack of sensitivity to the system parameters is due to the fact that people focus primarily on the signals and secondarily on the system parameters that generate the signals. Massey and Wu (2005) dealt with a host of other potential explanations through experimental manipulations and data analysis. In this paper, we built on Massey and Wu to examine the neurocomputational basis that gives rise to over- and underreactions.

(3) Despite efforts to control confounds in the fMRI study, including two control experiments, I think some confounds remain.

For example, a network of regions is presented as correlating with the cumulative probability that there has been a regime shift in this block of 10 samples (Pt). However, regardless of the exact samples shown, Pt always increases with sample number (as by the time of later samples, there have been more opportunities for a regime shift)? To control for this the authors include, in a supplementary analysis, an 'intertemporal prior.' I would have preferred to see the results of this better-controlled analysis presented in the main figure. From the tables in the SI it is very difficult to tell how the results change with the includion of the control regressors.

Thank you. In response, we added a new figure, now Figure 4, showing the results of Pt and delta Pt from GLM-2 where we added the intertemporal prior as a regressor to control for temporal confounds. We compared Pt and delta Pt results in vmPFC and ventral striatum between GLM-1 and GLM-2. We also showed the results on intertemporal prior on vmPFC and ventral striatum from GLM-2.

On the other hand, two additional fMRI experiments are done as control experiments and the effect of Pt in the main study is compared to Pt in these control experiments. Whilst I admire the effort in carrying out control studies, I can't understand how these particular experiment are useful controls. For example, in experiment 3 participants simply type in numbers presented on the screen - how can we even have an estimate of Pt from this task?

We thank the reviewer for this comment. On the one hand, the effect of Pt we see in brain activity can be simply due to motor confounds and the purpose of Experiment 3 was to control for them. Our question was, if subjects saw the similar visual layout and were just instructed to press buttons to indicate two-digit numbers, would we observe the vmPFC, ventral striatum, and the frontoparietal network like what we did in the main experiment (Experiment 1)?

On the other hand, the effect of Pt can simply reflect probability estimates of that the current regime is the blue regime, and therefore not particularly about change detection. In Experiment 2, we tested that idea, namely whether what we found about Pt was unique to change detection. In Experiment 2, subjects estimated the probability that the current regime is the blue regime (just as they did in Experiment 1) except that there were no regime shifts involved. In other words, it is possible that the regions we identified were generally associated with probability estimation and not particularly about probability estimates of change. We used Experiment 2 to examine whether this were true.

To make the purpose of the two control experiments clearer, we updated the paragraph describing the control experiments on page 9:

“To establish the neural representations for regime-shift estimation, we performed three fMRI experiments (n = 30 subjects for each experiment, 90 subjects in total). Experiment 1 was the main experiment, while Experiments 2 to 3 were control experiments that ruled out two important confounds (Fig. 1E). The control experiments were designed to clarify whether any effect of subjects’ probability estimates of a regime shift, P_t, in brain activity can be uniquely attributed to change detection. Here we considered two major confounds that can contribute to the effect of P_t. First, since subjects in Experiment 1 made judgments about the probability that the current regime is the blue regime (which corresponded to probability of regime change), the effect of P_t did not particularly have to do with change detection. To address this issue, in Experiment 2 subjects made exactly the same judgments as in Experiment 1 except that the environments were stationary (no transition from one regime to another was possible), as in Edwards (1968) classic “bookbag-and-poker chip” studies. Subjects in both experiments had to estimate the probability that the current regime is the blue regime, but this estimation corresponded to the estimates of regime change only in Experiment 1. Therefore, activity that correlated with probability estimates in Experiment 1 but not in Experiment 2 can be uniquely attributed to representing regime-shift judgments. Second, the effect of P_t can be due to motor preparation and/or execution, as subjects in Experiment 1 entered two-digit numbers with button presses to indicate their probability estimates. To address this issue, in Experiment 3 subjects performed a task where they were presented with two-digit numbers and were instructed to enter the numbers with button presses. By comparing the fMRI results of these experiments, we were therefore able to establish the neural representations that can be uniquely attributed to the probability estimates of regime-shift.”

To further make sure that the probability-estimate signals in Experiment 1 were not due to motor confounds, we implemented an action-handedness regressor in the GLM, as we described below on page 19:

“Finally, we note that in GLM-1, we implemented an “action-handedness” regressor to directly address the motor-confound issue, that higher probability estimates preferentially involved right-handed responses for entering higher digits. The action-handedness regressor was parametric, coding -1 if both finger presses involved the left hand (e.g., a subject pressed “23” as her probability estimate when seeing a signal), 0 if using one left finger and one right finger (e.g., “75”), and 1 if both finger presses involved the right hand (e.g., “90”). Taken together, these results ruled out motor confounds and suggested that vmPFC and ventral striatum represent subjects’ probability estimates of change (regime shifts) and belief revision.”

(4) The Discussion is very long, and whilst a lot of related literature is cited, I found it hard to pin down within the discussion, what the key contributions of this study are. In my opinion it would be better to have a short but incisive discussion highlighting the advances in understanding that arise from the current study, rather than reviewing the field so broadly.

Thank you. We thank the reviewer for pushing us to highlight the key contributions. In response, we added a paragraph at the beginning of Discussion to better highlight our contributions:

“In this study, we investigated how humans detect changes in the environments and the neural mechanisms that contribute to how we might under- and overreact in our judgments. Combining a novel behavioral paradigm with computational modeling and fMRI, we discovered that sensitivity to environmental parameters that directly impact change detection is a key mechanism for under- and overreactions. This mechanism is implemented by distinct brain networks in the frontal and parietal cortices and in accordance with the computational roles they played in change detection. By introducing the framework in system neglect and providing evidence for its neural implementations, this study offered both theoretical and empirical insights into how systematic judgment biases arise in dynamic environments.”

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

Thank you for pointing out the inclusion of the intertemporal prior in glm2, this seems like an important control that would address my criticism. Why not present this better-controlled analysis in the main figure, rather than the results for glm1 which has no effective control of the increasing posterior probability of a reversal with time?

Thank you for this suggestion. We added a new figure (Figure 4) that showed results of Pt and delta Pt from GLM-2. We also compared the effect of Pt and delta Pt between GLM-1 and GLM-2. We found that the effect of Pt and delta Pt did not differ between GLM-1 and GLM-2. GLM-1 and GLM-2 differed on whether various task-related regressors contributing to Pt, including the intertemporal prior, were included in the model. In GLM-1, those task-related regressors were not included. In GLM-2, the task-related regressors were included in addition to Pt and delta P.

The reason we kept results from GLM-1 (Figure 3) was primarily because we wanted to compare the effect of Pt between experiments under identical GLM. In other words, the regressors in GLM-1 was identical across all 3 experiments. In Experiments 1 and 2, Pt and delta Pt were respectively probability estimates and belief updates that current regime was the Blue regime. In Experiment 3, Pt and delta Pt were simply the number subjects were instructed to press (Pt) and change in number between successive periods (delta Pt).

Here is the section in the main text where we discussed the new Figure 4 on page 19-22:

We further examined the robustness of P_t and ∆P_t representations in vmPFC and ventral striatum in three follow-up analyses. In the first analysis, we implemented a GLM (GLM-2 in Methods) that, in addition to P_t and ∆P_t, included various task-related variables contributing to P_t as regressors. Specifically, to account for the fact that the probability of regime change increased over time, we included the intertemporal prior as a regressor in GLM-2. The intertemporal prior is the natural logarithm of the odds in favor of regime shift in the t-th period, , where q is transition probability and t = 1, …, 10is the period (Eq. 1 in Methods). It describes normatively how the prior probability of change increased over time regardless of the signals (blue and red balls) the subjects saw during a trial. Including it along with P_t would clarify whether any effect of P_t can otherwise be attributed to the intertemporal prior. We found that the results of P_t and ∆P_t in the vmPFC and ventral striatum in GLM-2 were identical to those in GLM-1 (Fig. 4): Fig. 4A was meant to depict the results in slices identical to those shown in Fig. 3B for results based on GLM-1. For slice-by-slice results, see Fig. S7 in SI for results based on GLM-1 and Fig. S9 for GLM-2. For Tables of activations, see Tables S1-S3 in SI for GLM-1 and Tables S7-S9 for GLM-2. In a separate, independent region-of-interest (ROI) analysis on vmPFC and ventral striatum (Fig. 4BC; see Independent regions-of-interest (ROIs) analysis in Methods for details), we further compared the effect of both P_t and ∆P_t between GLM-1 and GLM-2. For P_t, the difference between GLM-1 and GLM-2 was not significant (paired t-test, t(58) = −0.72, p = 0.47 in vmPFC, t(58) = −0.21, p = 0.83 in ventral striatum), while the effect of P_t from GLM-1 (one sample t-test, t(29) = −3,82, p <.01 in vmPFC; t(29) = −3.06, p <.01 in ventral striatum) and GLM-2 was significant (one-sample t-test, t(29) = −2.69, p =.01 in vmPFC; t(29) = −2.50, p .02 in ventral striatum). For ∆P_t, the difference between GLM-1 and GLM-2 was not significant (paired t-test, t(58) = −0.07, p =0.94 in vmPFC; t(58) = −0.14, p =0.88 in ventral striatum), while the effect of  from GLM-1 (one-sample t-test, t(29) = −3.12, p <.01 in vmPFC; t(29) = −4.14, p <.01 in ventral striatum) and GLM-2 was significant (one-sample t-test, t(29) = −2.92, p <.01 in vmPFC; t(29) = −3.59, p <.01 in ventral striatum). For the intertemporal prior, activity in both vmPFC and ventral striatum did not correlate significantly with the intertemporal prior (one-sample t-test, t(29) = −0.07, p =0.95 in vmPFC; t(29) = −0.53, p =0.60 in ventral striatum). All the t-tests described above were two-tailed. Taken together, these results suggest that vmPFC and ventral striatum represented P_t and ∆P_t regardless of whether the intertemporal prior and other task-related regressors contributing to P_t were included in the GLM. We also did not find that vmPFC and ventral striatum to represent the intertemporal prior. In the second analysis, we implemented a GLM that replaced P_t with the log odds of P_t, 1n (P_t/(1 - P_t)) (Fig. S10 in SI). In the third analysis, we implemented a GLM that examined P_t separately on periods when change-consistent (blue balls) and change-inconsistent (red balls) signals appeared (Fig. S11 in SI). Each of these analyses showed significant correlation with P_t in vmPFC and ventral striatum, further establishing the robustness of the P_t findings.

As a further point I could not navigate the tables of fMRI activations in SI and recommend replacing or supplementing these with images. For example I cannot actually find a vmPFC or ventral striatum cluster listed for the effect of Pt in GLM1 (version in table S1), which I thought were the main results? Beyond that, comparing how much weaker (or not) those results are when additional confound regressors are included in GLM2 seems impossible.

As suggested by the reviewer, we added slice-by-slice images showing the effect of Pt and delta Pt (Figure S9 in SI for GLM-2 and Figure S7 for GLM-1). The clusters in blue represent Pt effect, the clusters in orange represent delta Pt effect. As can be seen, both Pt and delta Pt are represented in the vmPFC and ventral striatum.

eLife Assessment

This study represents an important advance in our understanding of how certain inhibitors affect the behavior of voltage gated potassium channels. Robust molecular dynamics simulation and analysis methods lead to a new proposed inhibition mechanism with convincing strength of support. This study has considerable significance for the fields of ion channel physiology and pharmacology and could aid in development of selective inhibitors for protein targets.

Reviewer #3 (Public review):

Summary

In this manuscript, Zhang et al. investigate the conduction and inhibition mechanisms of the Kv2.1 channel, with a particular focus on the distinct effects of TEA and RY785 on Kv2 potassium channels. Using microsecond-scale molecular dynamics simulations, the authors characterize K⁺ ion permeation and RY785-mediated inhibition within the central pore. Their results reveal an inhibition mechanism that differs from those described for other Kv channel inhibitors.

Strengths

The study identifies a distinctive inhibitory mode for RY785, which binds along the channel walls in the open-state structure while still permitting a reduced level of K⁺ conduction. In addition, the authors propose a long-range allosteric coupling between RY785 binding in the central pore and changes in the structural dynamics of Kv2.1. Overall, this is a well-organized and carefully executed study, employing robust simulation and analysis methodologies. The work provides novel mechanistic insights into voltage-gated potassium channel inhibition and may offer useful guidance for future structure-based drug design efforts.

Weaknesses:

As noted in the Discussion, this study focuses primarily on the major binding site within the central pore and was not designed to systematically assess other potential allosteric binding sites for RY785. A more comprehensive structural and biophysical evaluation of possible additional binding sites would be a valuable direction for future investigations.

Comments on revisions:

The authors have addressed my comments.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors were seeking to identify a molecular mechanism whereby the small molecule RY785 selectively inhibits Kv2.1 channels. Specifically, the authors sought to explain some of the functional differences that RY785 exhibits in experimental electrophysiology experiments as compared to other Kv inhibitors, namely the charged and non-specific inhibitor tetraethylammonium (TEA). The authors used a recently published cryo-EM Kv2.1 channel structure in the open activated state and performed a series of multi-microsecond-long all-atom molecular dynamics simulations to study Kv2.1 channel conduction under the applied membrane voltage with and without RY785 or TEA present. They observed that while TEA directly blocks K+ permeation by occluding ion permeation pathway, RY785 binds to multiple non-polar residues near the hydrophobic gate of the channel driving it to a semi-closed non-conductive state. They confirmed this mechanism using an additional set of simulations and used it to explain experimental electrophysiology data,

Strengths:

The total length of simulation time is impressive, totaling many tens of microseconds. The authors develop their own forcefield parameters for the RY785 molecule based on extensive QM based parameterization. The computed permeation rate of K+ ions through the channel observed under applied voltage conditions is in reasonable agreement with experimental estimates of the single channel conductance. The authors have performed extensive simulations with the apo channel as well as both TEA and RY785. The simulations with TEA reasonably demonstrate that TEA directly blocks K+ permeation by binding in the center of the Kv2.1 channel cavity, preventing K+ ions from reaching the SCav site. The authors conclude that RY785 likely stabilizes a partially closed conformation of the Kv2.1 channel and thereby inhibits K+ current. This conclusion is plausible given that RY785 makes stable contacts with multiple hydrophobic residues in the S6 helix, which they can also validate using a recently published closed-state Kv2.1 channel cryo-EM structure. This further provides a possible mechanism for the experimental observations that RY785 speeds up the deactivation kinetics of Kv2 channels from a previous experimental electrophysiology study.

Weaknesses:

The authors, however, did not directly observe this semi-closed channel conformation and in fact acknowledge that more direct simulation evidence would require extensive enhanced-sampling simulations beyond the scope of this study. They have not estimated the effect of RY785 binding on the protein-based hydrophobic pore constriction, which may further substantiate their proposed mechanism. And while the authors quantified K+ permeation, they have not made any estimates of the ligand binding affinities or rates, which could have been potentially compared to experiment and used to validate their models.

However, despite those relatively minor weaknesses, the conclusions of the study are convincing, and overall this is a solid study helping us to understand two distinct molecular mechanisms of the voltage-gated potassium channel Kv2.1 inhibition by TEA and RY785, respectively.

Reviewer #2 (Public review):

Summary

In this manuscript, Zhang et al. investigate the conduction and inhibition mechanisms of the Kv2.1 channel, with a particular focus on the distinct effects of TEA and RY785 on Kv2 potassium channels. Using microsecond-scale molecular dynamics simulations, the authors characterize K⁺ ion permeation and RY785-mediated inhibition within the central pore. Their results reveal an inhibition mechanism that differs from those described for other Kv channel inhibitors.

Strengths

The study identifies a distinctive inhibitory mode for RY785, which binds along the channel walls in the open-state structure while still permitting a reduced level of K⁺ conduction. In addition, the authors propose a long-range allosteric coupling between RY785 binding in the central pore and changes in the structural dynamics of Kv2.1. Overall, this is a well-organized and carefully executed study, employing robust simulation and analysis methodologies. The work provides novel mechanistic insights into voltage-gated potassium channel inhibition and may offer useful guidance for future structure-based drug design efforts.

Weaknesses:

The study needs to consider the possibility of multiple binding sites for PY785, particularly given its impact on voltage sensors and gating currents. Specifically, the potential for allosteric binding sites in the voltage-sensing domain (VSD) should be assessed, as some allosteric modulators with thiazole moieties are known to bind VSD domains in multiple voltage-gated sodium channels (Ahuja et al., 2015; Li et al., 2022; McCormack et al., 2013; Mulcahy et al., 2019). Increasing structural and functional evidence supports the existence of multiple ligand-binding modes in voltage-gated ion channels. For example, polyunsaturated fatty acids have been shown to bind to KCNQ1 at both the voltage sensor domain and the pore domain (https://doi.org/10.1085/jgp.202012850). Similarly, cannabidiol has been structurally resolved in Nav1.7 at two distinct sites, one in a fenestration and another near the IFM-binding pocket (https://doi.org/10.1038/s41467-023-39307-6). These advances illustrate that ligand effects cannot always be interpreted based solely on a single binding site identified previously.

Reviewing Editor: 

The comments of the reviewers seem thoughtful and constructive. The weaknesses noted in reviews mainly concern mismatch between expectations, created by reading the Abstract, and data in the manuscript. The mismatch could be reconciled by either new simulations examining a semi-open state of the gate and additional RY785 binding sites, or by adjusting wording of the Abstract and Discussion to make it more clear that such simulations were not done. 

The Abstract and Discussion have been revised to make clear the computer-simulations presented in our study were designed to specifically validate or refute the hypothesis that RY785 is recognized by the pore domain, not the voltage sensors. 

Recommendations for the authors: 

Reviewer #1 (Recommendations for the authors): 

The authors addressed all the major issues in the original submission identified by the reviewers. I noticed a few minor issues, listed below, which can potentially fix small errors and further improve the readability of the manuscript. 

p.3 tetramethyl-ammonium -> tetraethylammonium 

p.7 "Snapshot of the final snapshot" -> "Snapshot of the final simulation coordinates" 

p. 8 "sigma value" - please spell out what it is. 

p. 9 "one or other subunit of the tetramer" -> "one or another subunit of the tetramer" or "one or more subunits of the tetramer" 

p 15 "(the net charge of these constructs is thus zero)." -> ""(the net charge of these constructs is zero for these systems)." Please note that using ionizable amino acid residues in their default protonation state does not guarantee net zero charge of the system since the number of cationic and anionic residues is generally not the same. 

p. 15 "Two K+ ions were initially positioned in the selectivity filter, one coordinated by residues 373..." Please indicate at which ion binding sites S_1, S_2, e.g. K+ were located and what the residue names are . 

SI Figs. S3-S20. Please indicate in the figure captions that all those data are for RY785 

SI Fig. S22 and SI Table S1 captions "shown in Fig. S20" -> "shown in Fig. S21" 

We thank the Reviewer for this thorough proofreading. We have made the necessary corrections. 

Reviewer #2 (Recommendations for the authors): 

The authors have addressed most of my comments satisfactorily, with the exception of the first point. Below, I provide further clarification regarding my concern. 

First, it appears that the authors may have misunderstood what is meant by the possibility of multiple binding sites for RY785. This does not imply that the central pore is excluded as a binding site. Rather, it refers to the possibility that, in addition to a pore-domain site, the ligand may interact with additional binding sites, either simultaneously or in a statedependent manner. Increasing structural and functional evidence supports the existence of multiple ligand-binding modes in voltage-gated ion channels. For example, polyunsaturated fatty acids have been shown to bind to KCNQ1 at both the voltage sensor domain and the pore domain (https://doi.org/10.1085/jgp.202012850). Similarly, cannabidiol has been structurally resolved in Nav1.7 at two distinct sites, one in a fenestration and another near the IFM-binding pocket (https://doi.org/10.1038/s41467-02339307-6). These advances illustrate that ligand ecects cannot always be interpreted based solely on a single binding site identified previously. Therefore, even if one assumes that there is no precedent for a small-molecule inhibitor that simultaneously acts on both the voltage sensor and pore domain, this does not exclude the possibility that a ligand may bind to both regions in dicerent functional states.  

The Reviewer’s opinion came across clearly in the previous version. We however disagree that a computational investigation of the possibility that RY785 binds to the voltagesensors is well-advised at this point, given that the model we propose seemingly ocers a rationale for the inhibitory ecects observed experimentally. Our opinion is also that there is no compelling precedent for the mechanism of inhibition envisaged by the Reviewer – and would argue that neither of the two studies referenced above are compelling examples.  As we stated in our previous response to the Reviewer, we believe that the logical next step in this research will be to validate or refute the computational prediction we have put forward, experimentally. 

In addition, the present computational study does not provide direct mechanistic evidence to explain the statement that RY785 accelerates voltage-sensor deactivation. Specifically, no simulations were performed to model pore-domain closure or voltage-sensor motion upon RY785 binding. Moreover, alternative binding sites were neither explored nor explicitly excluded, as the simulations only involved placing a single molecule of TEA or RY785 approximately 10 Å below the cytoplasmic gate. Under these conditions, conclusions regarding ecects on voltage-sensor dynamics remain speculative. 

That is a fair characterization. 

These concerns do not detract from the overall quality of this otherwise strong computational study. There are several straightforward ways to address this issue. For example: 

(1) Perform molecular docking or related screening approaches to evaluate potential ligand-binding sites beyond the central pore, particularly in regions proximal to the voltage sensor. This should not impose a substantial additional computational burden for a computational chemistry group. 

(2) Revise the abstract and discussion to clarify that the current work focuses exclusively on pore-domain binding and does not explore possible additional binding sites near the voltage sensor. Explicitly stating this limitation would help prevent potential overinterpretation by readers.

We have opted for (2), as noted above.

eLife Assessment

In this manuscript, based on electron microscopy observations of C. elegans embryos, the authors make the bold claim that the plasma membrane ruptures during cell division and that closure of this opening by membrane extension contributes to cytokinesis. Although the findings are potentially valuable, the evidence in support of the authors' claims is inadequate.

Reviewer #1 (Public review):

Summary:

Using electron microscopy, the authors report discontinuities in the plasma membrane of C. elegans embryos. They associate these discontinuities with cell division and speculate that membrane rupture and subsequent resealing contribute to cytokinesis. They further discuss the proximity of these sites to vesicles and propose a role for vesicle-mediated membrane extension.

Weaknesses:

(1) The possibility that the membrane discontinuity is an artifact

Although the authors focus on discontinuities in the plasma membrane, similar discontinuities are also observed in mitochondria, the nuclear envelope, and yolk granules. This raises concerns about whether the electron micrographs presented are suitable for assessing membrane continuity.

Electron micrographs result from a lengthy sample preparation process, including high-pressure freezing, freeze substitution in acetone containing OsO4, gradual warming, uranyl acetate staining, resin embedding, and ultrathin sectioning. In general, lipids are soluble in acetone at temperatures above −30 {degree sign}C, and preservation of membrane structures relies heavily on efficient OsO4 fixation. Insufficient OsO4 treatment would be expected to reduce membrane contrast.

C. elegans embryos are encapsulated by an eggshell that forms at fertilization and gradually develops during the first few cell divisions. It is unclear how efficiently OsO4 in acetone penetrates the eggshell during freeze substitution, raising further concern about plasma membrane preservation under the conditions used.

(2) Lack of evidence linking membrane discontinuity to cell division

The reported plasma membrane discontinuities are not specific to mitotic cells. If this were a physiological process playing an important role in cytokinesis, it should occur in a temporally and spatially coordinated manner with nuclear division. However, it remains unclear at what stage of the cell cycle the membrane rupture occurs and where it is located relative to chromosomes and the mitotic spindle.

(3) Lack of evidence for extension of the separated membrane

Although the authors speculate that resealing of the ruptured membrane occurs via extension of the separated membrane, no direct evidence supporting this mechanism is presented. Proximity to vesicles alone does not demonstrate that membrane extension occurs through vesicle fusion. More direct evidence is required to support this claim.

(4) Inconsistency with published work

Numerous studies have examined cell division in developing C. elegans embryos using the GFP::PH(PLC1δ1) marker expressed from the ltIs38 transgene [pAA1; pie-1::GFP::PH(PLC1δ1) + unc-119(+)], generated by the Oegema lab (https://wormbase.org/species/c_elegans/transgene/WBTransgene00000911#01--10 ). To date, no study has reported membrane ruptures of the magnitude described here. The complexity of cell surface morphology from the 8- to 12-cell stages onward has been well documented, for example, by Fu et al. (2016) using light-sheet microscopy and 3D reconstruction (doi:10.1038/ncomms11088).

Supplementary Movies 5, 6, and 10 of this paper illustrate how single-plane images can easily produce apparent membrane discontinuities, for example, due to membrane orientations nearly parallel to the imaging plane.

The three single-plane images from only three embryos presented in Figure 6 are insufficient to support the authors' strong conclusions. Raw 3D data should be provided.

Reviewer #2 (Public review):

Summary:

Liang et al. explore an unusual observation of membrane discontinuities in dividing C. elegans embryonic cells. This report is the first to demonstrate that, instead of the classical invagination of membranes during cytokinesis, cells in the early embryos of C. elegans exhibit separation of sister membranes that extend independently. TEM images of high-pressure-frozen samples provide strong evidence for the presence of Membrane Openings (MOs) in cells at various stages of the cell cycle, predominantly during mitosis. High-resolution images (x 30,000) clearly show the wrinkled plasma membrane and smooth MOs.<br /> The electron microscopy data are supported by the live cell imaging of strains with fluorescently tagged membrane markers. This study opens up the possibility of tracking MOs at other stages of C. elegans development, and also asks if it might be a common phenomenon in other species that exhibit rapid embryonic growth and divisions.

Strengths:

(1) Thorough verification of Membrane Openings (MO) by several methods:

(a) 4 independent sample batches.

(b) Examined historical collections.

(c) Analysed embryos at different stages of development. The absence of MOs in later stages (comma) serves as a negative control and gives confidence that MOs are genuine and not technical artifacts.

(2) Live cell imaging of strain with fluorescently labelled membranes provides real-time dynamics of membrane rupture.

(3) After observing the membrane rupture, the next obvious question is - what prevents the cytosol from leaking out? The EM images showing PBL and PEL - extracellular matrix serving as barriers for the cytosol are convincing.

Weakness:

(1) The association of membrane discontinuities with cell division is not convincing, as there are 159 cells out of 425 showing MOs, but it is not mentioned clearly how many of these are undergoing cell division. Also, it's not clear whether the 20 dividing cells analysed for MOs are a part of the 159 cells or a separate dataset. A graphical representation of the number of samples and observed frequencies would be helpful to understand the data collection workflow.

(2) In Figures 3A and 3B, the resolution of the images is not enough to verify 3A as classical membrane invagination and 3B as detached sister membranes.

(3) Figure 6 lacks controls. How does the classical invagination look in this strain? Also, adding nuclear dye would be informative, in order to correlate the nuclear division with membrane rupture, as claimed.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors challenge a dogma in cell biology, namely that cells are at any time point engulfed by a continuous plasma membrane. Liang et al. find that during C elegans embryogenesis, a high number of cells are not entirely surrounded by a plasma membrane but show membrane openings (MOs). These openings are enriched at the embryo's periphery, towards the eggshell. The authors propose that plasma membrane discontinuities emerge during metaphase of mitosis and that independent extension of "sister membranes" engulfs the daughter cells.

Strengths:

On the positive side, the authors find plasma membrane discontinuities not only by electron microscopy but also by fluorescence microscopy and provide information about the dynamics of membrane openings and their emergence. While this is assuring, the authors conclude that MOs emerge during metaphase. From what the authors show, this particular information cannot be deduced, as there is no dynamic capture of a membrane scission event together with a chromatin marker that would indicate mitosis. The authors could, however, attempt to find such events in live movies, given the high incidence of MOs reported from their EM data.

Weaknesses:

In order to convincingly demonstrate the absence of any plasma membrane in the respective regions of the embryonic periphery or between cells of the embryo, the authors would have to show consecutive serial TEM sections where MOs are detected over more z-planes, beyond the mere 3D reconstructions. Although the authors state in the methods section that continuous ultrathin sections were cut for the metaphase sample (page 21, line 472), consecutive sections are never shown in TEM. While we do see the 3D reconstructions, better documentation of the underlying TEM data is missing. It would be necessary to show a membrane opening in consecutive z sections. Alternatively, the authors could seek the possibility to convincingly back up their claims with volume imaging by focused ion beam scanning EM (FIBSEM), where cellular volumes can be sectioned in almost isotropic resolution.

Another critical issue concerns the detection of the membrane discontinuities in electron micrographs, which, in my opinion, is ambiguous. How do the authors reliably discriminate in their TEM images whether there is a plasma membrane or not? The absence - or weak appearance - of the stain of the electron dense material at membranes, which seems to be their criterion for MOs, is also apparent at other, intracellular membranes, like at the NE or at the ER (for example, see Figure 1C). Also, the plasma membrane itself appears unevenly stained in regions that the authors delineate as intact (for example, Figure 1C, 2B/1).

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Using electron microscopy, the authors report discontinuities in the plasma membrane of C. elegans embryos. They associate these discontinuities with cell division and speculate that membrane rupture and subsequent resealing contribute to cytokinesis. They further discuss the proximity of these sites to vesicles and propose a role for vesicle-mediated membrane extension. 

Weaknesses:

(1) The possibility that the membrane discontinuity is an artifact

Although the authors focus on discontinuities in the plasma membrane, similar discontinuities are also observed in mitochondria, the nuclear envelope, and yolk granules. This raises concerns about whether the electron micrographs presented are suitable for assessing membrane continuity.

Electron micrographs result from a lengthy sample preparation process, including high-pressure freezing, freeze substitution in acetone containing OsO4, gradual warming, uranyl acetate staining, resin embedding, and ultrathin sectioning. In general, lipids are soluble in acetone at temperatures above −30 {degree sign}C, and preservation of membrane structures relies heavily on efficient OsO4 fixation.

Insufficient OsO4 treatment would be expected to reduce membrane contrast.

C. elegans embryos are encapsulated by an eggshell that forms at fertilization and gradually develops during the first few cell divisions. It is unclear how efficiently OsO4 in acetone penetrates the eggshell during freeze substitution, raising further concern about plasma membrane preservation under the conditions used.

We thank the reviewer for raising this important technical concern. We have taken this question seriously since first observing membrane discontinuities six years ago, and we have since conducted extensive controls to rule out fixation artifacts. Below, we present multiple lines of evidence—ranging from technical reproducibility to orthogonal imaging approaches—that collectively demonstrate the biological reality of these structures.

(1) Technical expertise and standard protocols

Our laboratory has extensive experience with electron microscopy across diverse biological systems, including neurons, muscle cells, and hypodermis in C. elegans, as well as tissues from Drosophila, mouse, bacteria, and cultured cells (Chen et al., 2013; Ding et al., 2018; Guan et al., 2022; Y. Li et al., 2018; Miao et al., 2024; Qin et al., 2014; Wang et al., 2026; J. Xu et al., 2022; M. Xu et al., 2021; L. Yang et al., 2020; X. Yang et al., 2019; Zhu et al., 2022). Importantly, we did not introduce any novel or unconventional steps in our EM preparation; all protocols were standard and well-established. Thus, the observed membrane discontinuities are unlikely to stem from technical inexperience or idiosyncratic methods.

In addition to membrane discontinuities, we would like to emphasize that a large number of single plasma membranes separating adjacent cytoplasmic domains were also detected under EM (Figure 1, 3 and 4, for instance). This observation is particularly significant because the invagination model cannot generate single plasma membrane barriers between adjacent cytoplasmic domains. Instead, independent extension of detached sister membranes could explain the formation of cytoplasm-enclosed membranes. Furthermore, as the morphology and continuity of these single cytoplasm-immersed membrane structures are well preserved, this indicates successful EM processing and argues against inefficient fixation or other technical issues.

(2) Reproducibility across independent preparations and techniques

To test whether the discontinuities were preparation-specific, we examined four independent sample batches collected in the lab over the years. Membrane discontinuities, as well as cytoplasm-immersed membranes, on embryonic cells were consistently observed across all batches, indicating that the phenomenon is not dependent on a single preparation method. Furthermore, we validated our findings using two EM techniques: transmission electron microscopy (HPF-TEM) and dualbeam scanning electron microscopy (SEM). Membrane discontinuities were clearly identifiable with both techniques, further supporting their robustness.

(3) Validation using an independent public dataset

We examined the publicly available C. elegans embryo EM collection (WormAtlas). In several instances, particularly at the embryonic periphery where plasma membrane discontinuities are more readily visualized (https://www.wormimage.org/image.php?id=140265&page=1), we identified similar structures. The presence of these features in an independent dataset generated by different researchers confirms that they are not artifacts unique to our sample preparation.

(4) Developmental regulation of membrane discontinuities

We analyzed embryos across multiple developmental stages. Membrane discontinuities were observed in both intrauterine and laid embryos at early stages. However, as embryos reached the comma stage—a period marked by the onset of elongation and reduced cell proliferation—the incidence of discontinuities dropped dramatically (0/13, 0/17, and 0/30 cells examined). This developmental specificity argues strongly against a general fixation artifact, which would be expected to occur randomly across stages. Additionally, the eggshell is present throughout the embryonic stage of C. elegans; therefore, the dramatic reduction of membrane discontinuities in comma-stage of embryo argues against the possibility that the eggshell poses a fixation problem.

(5) Rigorous criteria for identifying membrane discontinuities

To ensure unbiased analysis, we systematically collected images from early embryonic cells using the following criteria:

(1) Random section selection: For each sample, we randomly selected one section containing the largest number of embryos or cells (Sup Figure 2) for initial analysis. We found membrane discontinuities in 159 cells distributed across 57 embryos, representing 95% of the total sampled embryos This portion of the data is summarized in Figure 1.

(2) Whole-membrane examination: Each putative membrane discontinuity was identified only after examining the entire plasma membrane of the cell on a given section. Importantly, aside from the discontinuity, the remainder of the plasma membrane remained intact. Moreover, in most cells, only a single discontinuity was present per section, arguing against random, widespread membrane tearing during preparation.

(3) Neighboring section verification: Because EM preparation yields serial sections, we verified nearly all membrane discontinuities by examining adjacent sections. Again, the same membrane discontinuity was confirmed only after inspecting the entire plasma membrane on those neighboring sections as well. We will include this verification protocol in the revised Methods and additional imaging of consecutive sections would be provided if needed.

(4) Serial section reconstruction: To further determine whether a dividing cell indeed contains one membrane rupture, we performed two serial reconstruction experiments.

First, we used HPF-TEM to analyze 105 consecutive sections of a metaphase cell, reconstructing the entire plasma membrane and chromosome configuration. We found that one membrane rupture largely encircled the chromosomal disc (Figure 2 and Video S1), spatially aligning with the future segregation zone. Second, we used AutoCUTS-SEM to collect approximately 600 sections covering ~95% of a telophase cell containing three nuclei sharing a common cytoplasm. This tri-nucleated cell was enclosed by three distinct plasma membranes, each harboring a single rupture site. These three ruptures converged to form a Y-shaped exposed cytoplasmic region spanning >351 sections (Figure 5). Collectively, these reconstructions demonstrate that each cell contains only one discontinuity from a 3D point of view, further supporting that the phenomenon is not due to random sample preparation damage.

(6) Orthogonal validation by live imaging: In addition to EM, we performed live imaging of plasma membrane dynamics. While live imaging provides important temporal context, we recognize its limitations in resolving membrane ultrastructure. The rapid kinetics of membrane extension (approximately 20–30 seconds for metaphase and less than 3 minutes for cytokinesis), combined with embryo motility, introduces spatiotemporal ambiguities. To capture dynamic membrane events, our live imaging using the GFP::PH membrane marker was performed at 4-second intervals, approaching the practical limit for single-section scanning of the embryo. With single-plane live imaging, nevertheless, both membrane ruptures and free-ended sister membrane structures could be detected (Figures 6), providing additional evidence that membrane rupture and independent extension of detached sister membranes underlie cytokinesis in C. elegans embryos. Notably, 3D membrane dynamics analysis using light-sheet microscopy (Fu et al. Imaging multicellular specimens with real-time optimized tiling light-sheet selective plane illumination microscopy. Nature Communications. 2016. DOI:10.1038/ncomms11088) revealed membrane ruptures in dividing early C. elegans embryonic cells, including during telophase or metaphase. Therefore, live imaging further validates the membrane rupture phenomena in dividing embryonic cells in C. elegans. 

While future advances in imaging technology may enable real-time visualization at near-EM resolution, our extensive, multi-year effort to test the artifact hypothesis has convinced us that these membrane discontinuities are genuine biological features of dividing C. elegans embryonic cells.

We are confident that the cumulative evidence presented here addresses the reviewer's concerns and demonstrates that the observed membrane discontinuities, as well as cytoplasm-immersed membranes, are not procedural artifacts but rather reflect a previously underappreciated aspect of plasma membrane dynamics during embryonic cell division.

(2) Lack of evidence linking membrane discontinuity to cell division 

The reported plasma membrane discontinuities are not specific to mitotic cells. If this were a physiological process playing an important role in cytokinesis, it should occur in a temporally and spatially coordinated manner with nuclear division. However, it remains unclear at what stage of the cell cycle the membrane rupture occurs and where it is located relative to chromosomes and the mitotic spindle.

Thank you for this insightful comment. We agree that establishing a direct link between plasma membrane discontinuities and mitotic progression is critical, and we appreciate the opportunity to clarify this point.

In C. elegans embryos, the early stages of development are characterized by rapid and extensive cell division. Within approximately 100 minutes, a two-cell embryo develops into an embryo containing nearly 30 cells. The majority of the electron microscopy analyses in our study were performed on embryos at stages with fewer than 30 cells, where most cells are actively dividing. Thus, it is reasonable to infer that the cells exhibiting membrane discontinuities are predominantly mitotic cells.

Supporting this notion, as embryos reached the comma stage—a period marked by the onset of elongation and reduced cell proliferation—the incidence of membrane discontinuities dropped dramatically (0/13, 0/17, and 0/30 cells examined). This developmental specificity strongly suggests that membrane discontinuities are tightly linked to cell division.

Importantly, mitotic features such as metaphase chromosomes aligned at the equatorial plane or two (or more) nuclei sharing common cytoplasm can be identified in EM images. In our single random EM section analysis, we captured membrane discontinuities in cells at metaphase, anaphase (characterized by fewer than 10 chromosomal clumps), and telophase (defined by two nuclei sharing cytoplasm). Hence, membrane discontinuities are indeed present on mitotic cells. In addition, a published work by Fu et al (Fu et al. Imaging multicellular specimens with real-time optimized tiling light-sheet selective plane illumination microscopy. Nature Communications. 2016. DOI:10.1038/ncomms11088) using light-sheet microscopy captured similar membrane discontinuities in cells displaying classical mitotic features, including anaphase or telophase.

To further investigate the spatial relationship between membrane ruptures and chromosome organization, we performed three-dimensional reconstructions on a metaphase cell. As shown in Figure 2 and Video S1, the membrane discontinuities largely encircled the condensed chromosome disc and were spatially aligned with the future segregation zone, further revealing the relative location of membrane discontinuities to chromosomes, at least at metaphase.

We further collected 3D information for a telophase cell containing three nuclei. This tri-nucleated cell was enclosed by three distinct plasma membranes, each harboring a single rupture site that merged to form a single rupture. The observation that membrane ruptures are present in a tri-nucleated cell is particularly informative. The tri-nucleated feature indicates that this cell underwent two rounds of cell division and that both divisions were at telophase. The presence of a single membrane rupture suggests that membrane discontinuities may persist throughout the cell cycle, as the second cell cycle began from a mother cell that still shared cytoplasm with its sister cell and already had one membrane rupture. Therefore, in addition to the mitotic phase, membrane discontinuities—at least in this context—also exist during the DNA synthesis stage.

(3) Lack of evidence for extension of the separated membrane 

Although the authors speculate that resealing of the ruptured membrane occurs via extension of the separated membrane, no direct evidence supporting this mechanism is presented. Proximity to vesicles alone does not demonstrate that membrane extension occurs through vesicle fusion. More direct evidence is required to support this claim.

Thank you for raising this important point. We appreciate the opportunity to clarify our conclusion.

In our study, EM analysis revealed the presence of cellular vesicles in close proximity to both free membrane edges and the already separated sister plasma membranes (Figure 4). However, we acknowledge that without advanced live-cell imaging, it is not possible to conclusively determine whether the extension of these separated sister membranes occurs through vesicle fusion.

We realize that a statement in the Discussion section—“The expansion of the plasma membrane is generally driven by vesicle fusion”(page 16)—may have inadvertently led the reviewer to interpret this as our own conclusion regarding the mechanism of membrane extension in this context. In fact, that statement was intended to reflect the current general understanding of membrane expansion, not to imply that we had demonstrated such a mechanism for the free-ended sister membranes. As we subsequently noted, “However, this remains speculative and requires further experimental validation.”

To avoid any misunderstanding, we will revise this section to clearly state that the mechanism by which the separated sister membranes extend remains unknown and that further investigation is needed to determine how existing models of membrane expansion may apply to or be adapted for this novel context.

We thank the reviewer again for their thoughtful comment, which has helped us improve the clarity of our manuscript

(4) Inconsistency with published work

Numerous studies have examined cell division in developing C. elegans embryos using the GFP::PH(PLC1δ1) marker expressed from the ltIs38 transgene [pAA1; pie-1::GFP::PH(PLC1δ1) + unc-119(+)], generated by the Oegema lab (https://wormbase.org/species/c_elegans/transgene/WBTransgene00000911#01--10 ). To date, no study has reported membrane ruptures of the magnitude described here. The complexity of cell surface morphology from the 8- to 12-cell stages onward has been well documented, for example, by Fu et al. (2016) using light-sheet microscopy and 3D reconstruction (doi:10.1038/ncomms11088).

Supplementary Movies 5, 6, and 10 of this paper illustrate how single-plane images can easily produce apparent membrane discontinuities, for example, due to membrane orientations nearly parallel to the imaging plane.

The three single-plane images from only three embryos presented in Figure 6 are insufficient to support the authors' strong conclusions. Raw 3D data should be provided.

Thank you for this important comment. We fully agree that the GFP::PH(PLC1δ1) marker, generated by the Oegema lab, has been widely and effectively used to study various aspects of C. elegans embryonic development. In fact, we also employed this same marker in our study to assess membrane integrity.

However, while live imaging provides invaluable temporal resolution, its limitations in resolving membrane ultrastructure are substantial. In C. elegans embryos, early development is marked by rapid and extensive cell divisions. Within approximately 100 minutes, a two-cell embryo develops into one containing nearly 30 cells. During this fast-dividing stage, the rapid kinetics of membrane extension—approximately 20–30 seconds during metaphase and less than 3 minutes during cytokinesis— combined with embryo motility, introduce considerable spatiotemporal ambiguities. Furthermore, the longstanding invagination model of cytokinesis has shaped interpretations in the field, which may have led to ambiguous structures such as free-ended extensions being dismissed as potential artifacts rather than recognized as alternative morphological features. Theoretical and computational models have largely been built upon invagination-centric assumptions, which may have further constrained conceptual frameworks. Therefore, fluorescence protein-based live imaging analysis alone could not serve as a convincing approach to challenge the current dogma of cell division, nor did we intend it to.

However, when reexamined in light of our findings, previous studies using this same GFP marker have in fact revealed membrane discontinuities that went unnoticed. For example, Fu et al (Fu et al. Imaging multicellular specimens with real-time optimized tiling light-sheet selective plane illumination microscopy. Nature Communications. 2016. DOI:10.1038/ncomms11088) using light-sheet microscopy and 3D reconstruction, captured membrane discontinuities in cells undergoing mitotic phases such as anaphase or telophase. Similarly, an earlier study by Harrell and Goldstein (Harrell and Goldstein. 2011. Internalization of multiple cells during C. elegans gastrulation depends on common cytoskeletal mechanisms but different cell polarity and cell fate regulators. Developmental Biology. DOI:10.1016/j.ydbio.2010.09.012) showed regions where the GFP::PH signal appeared fuzzy and discontinuous.

Nevertheless, given the inherent limitations of fluorescence microscopy in resolving membrane ultrastructure, high-resolution electron microscopy—supported by rigorous controls and serial section analysis—remains the gold standard for definitively identifying such membrane discontinuities.

We acknowledge that our findings are surprising. We did not set out to challenge the long-held view of membrane integrity during cell division. In fact, this study began when our dedicated EM technician, Jingjing Liang, first observed membrane discontinuity phenomena in control samples—wild-type embryos. Had she not come across this observation, we likely would never have pursued this line of inquiry.

We appreciate the opportunity to clarify these points and thank the reviewer for thoughtful engagement with our work.

Reviewer #2 (Public review):

Summary:

Liang et al. explore an unusual observation of membrane discontinuities in dividing C. elegans embryonic cells. This report is the first to demonstrate that, instead of the classical invagination of membranes during cytokinesis, cells in the early embryos of C. elegans exhibit separation of sister membranes that extend independently. TEM images of high-pressure-frozen samples provide strong evidence for the presence of Membrane Openings (MOs) in cells at various stages of the cell cycle, predominantly during mitosis. High-resolution images (x 30,000) clearly show the wrinkled plasma membrane and smooth MOs.

The electron microscopy data are supported by the live cell imaging of strains with fluorescently tagged membrane markers. This study opens up the possibility of tracking MOs at other stages of C. elegans development, and also asks if it might be a common phenomenon in other species that exhibit rapid embryonic growth and divisions. 

Strengths:

(1) Thorough verification of Membrane Openings (MO) by several methods: 

(a) 4 independent sample batches.

(b) Examined historical collections.

(c) Analysed embryos at different stages of development. The absence of MOs in later stages (comma) serves as a negative control and gives confidence that MOs are genuine and not technical artifacts. 

(2) Live cell imaging of strain with fluorescently labelled membranes provides realtime dynamics of membrane rupture.

(3) After observing the membrane rupture, the next obvious question is - what prevents the cytosol from leaking out? The EM images showing PBL and PEL - extracellular matrix serving as barriers for the cytosol are convincing.

Thanks to the reviewer for the encouragement. Highly appreciated.

Weakness:

(1) The association of membrane discontinuities with cell division is not convincing, as there are 159 cells out of 425 showing MOs, but it is not mentioned clearly how many of these are undergoing cell division. Also, it's not clear whether the 20 dividing cells analysed for MOs are a part of the 159 cells or a separate dataset. A graphical representation of the number of samples and observed frequencies would be helpful to understand the data collection workflow.

We sincerely thank the reviewer for raising this important question and appreciate the opportunity to clarify these points.

(1) Relationship between membrane discontinuities and cell division

In C. elegans embryos, early development is characterized by rapid and extensive cell division: within approximately 100 minutes, a two-cell embryo develops into one containing nearly 30 cells. Most of our electron microscopy (EM) analyses were performed on embryos at stages with fewer than 30 cells, in which the majority of cells are actively dividing. Therefore, it is reasonable to infer that the cells exhibiting membrane discontinuities (MOs) are predominantly mitotic. Supporting this, as embryos reached the comma stage—when cell proliferation declines and elongation begins—the incidence of MOs dropped sharply (0/13, 0/17, and 0/30 cells examined. This developmental specificity strongly links MOs to cell division.

Moreover, in single random EM sections, we observed MOs in cells displaying clear mitotic features, such as metaphase chromosomes aligned at the equatorial plate, or anaphase/telophase configurations (fewer than 10 chromosomal clumps or two nuclei sharing common cytoplasm). Thus, MOs are indeed present in mitotic cells.

From our 3D reconstruction (Figure 5), we identified a telophase cell containing three nuclei, each enclosed by its own plasma membrane, with each membrane harboring a single rupture that converged into a single opening. This tri-nucleated configuration indicates that the cell had undergone two rounds of division and was at telophase in both. The presence of a single membrane rupture in this context suggests that MOs can persist beyond mitosis, as the second cell cycle initiated from a mother cell that already shared cytoplasm with its sister and already contained a rupture. Thus, in this case, MOs were also present during DNA synthesis stage.

(2) Clarification of sample numbers and datasets

In Figure 1, we present results from a single EM section per embryonic cell, with sections randomly selected per embryo as detailed in Sup Figure 2. This initial dataset (425 cells) forms the basis of Figure 1.

From the same pool of 425 cells, we used additional EM sections—distinct from those shown in Sup Figure 2—to locate 20 dividing cells for analysis of membrane discontinuities. Thus, while these 20 cells originated from the same set of embryos, they were not derived from the sections used in Figure 1 or Sup Figure 2.

A graphical summary of sample numbers from the single-section analysis is already provided in Figure 1. Notably, cells with two clearly visible nuclei are more likely to be sectioned through or near their maximal diameter. In contrast, the randomly selected sections used for Figure 1 captured cells at variable planes, reducing the likelihood of observing MOs. Consistent with this, in the three embryos where no MOs were detected (one example is Sup Figure 2N), the sections likely passed through peripheral regions of the cells. Consequently, the frequency of MOs in randomly sectioned cells (Figure 1) is not directly comparable to that observed in the 20 dividing cells, which were analyzed using sections more likely to capture cells near their maximal diameter. These 20 dividing cells should therefore be considered a separate analysis. We will add detailed explanations in the Methods section to ensure this distinction is clearly understood.

We are grateful for the reviewer’s thoughtful feedback and believe these clarifications will improve the clarity and rigor of the manuscript.

(2) In Figures 3A and 3B, the resolution of the images is not enough to verify 3A as classical membrane invagination and 3B as detached sister membranes.

Thank you for your valuable comment. In the revised manuscript, we will provide additional images at higher magnification to better illustrate the classical membrane invagination in Figure 3A and the detached sister membranes in Figure 3B.

(3) Figure 6 lacks controls. How does the classical invagination look in this strain? Also, adding nuclear dye would be informative, in order to correlate the nuclear division with membrane rupture, as claimed. 

Thank you for this important comment. As we addressed how we correlated nuclear division with membrane rupture in response to weakness (1), below we will focus on how we may distinguish classical invagination from membrane rupture.

While live imaging provides invaluable temporal resolution, its limitations in resolving membrane ultrastructure are substantial. In C. elegans embryos, early development is marked by rapid and extensive cell divisions. Within approximately 100 minutes, a two-cell embryo develops into one containing nearly 30 cells. During this fast-dividing stage, the rapid kinetics of membrane extension—approximately 20–30 seconds during metaphase and less than 3 minutes during cytokinesis— combined with embryo motility, introduce considerable spatiotemporal ambiguities. Furthermore, the longstanding invagination model of cytokinesis has shaped interpretations in the field, which may have led to ambiguous structures such as free-ended extensions being dismissed as potential artifacts rather than recognized as alternative morphological features. Theoretical and computational models have largely been built upon invagination-centric assumptions, which may have further constrained conceptual frameworks. Therefore, fluorescence protein-based live imaging analysis alone could not serve as a convincing approach to challenge the current dogma of cell division, nor did we intend it to.

However, when reexamined in light of our findings, previous studies using GFP::PH or similar markers have in fact revealed membrane discontinuities that went unnoticed. For example, using light-sheet microscopy and 3D reconstruction, Fu et al captured membrane discontinuities in cells undergoing division such as anaphase or telophase (Fu et al. Imaging multicellular specimens with real-time optimized tiling light-sheet selective plane illumination microscopy. Nature Communications. 2016.DOI:10.1038/ncomms11088)

Similarly, an earlier study by Goldstein et al. (Harrell and Goldstein. 2011. Internalization of multiple cells during C. elegans gastrulation depends on common cytoskeletal mechanisms but different cell polarity and cell fate regulators. Developmental Biology. DOI:10.1016/j.ydbio.2010.09.012) showed regions where the GFP::PH signal appeared fuzzy and discontinuous.

Here, to capture dynamic membrane events, our live imaging using the GFP::PH membrane marker was performed at 4-second intervals, approaching the practical limit for single-section scanning of the embryo. With single-plane live imaging, both membrane ruptures and free-ended sister membrane structures (Figures 6) could be detected, providing additional evidence that membrane rupture and independent extension of detached sister membranes underlie cytokinesis in C. elegans embryos.

However, given the inherent limitations of fluorescence microscopy in resolving membrane ultrastructure, high-resolution electron microscopy—supported by rigorous controls and serial section analysis—remains the gold standard for definitively distinguishing invagination from membrane discontinuities.

While future advances in imaging technology may enable real-time visualization at near-EM resolution, our extensive, multi-year effort to test the artifact hypothesis has convinced us that these membrane discontinuities are genuine biological features of dividing C. elegans embryonic cells.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors challenge a dogma in cell biology, namely that cells are at any time point engulfed by a continuous plasma membrane. Liang et al. find that during C elegans embryogenesis, a high number of cells are not entirely surrounded by a plasma membrane but show membrane openings (MOs). These openings are enriched at the embryo's periphery, towards the eggshell. The authors propose that plasma membrane discontinuities emerge during metaphase of mitosis and that independent extension of "sister membranes" engulfs the daughter cells.

Strengths:

On the positive side, the authors find plasma membrane discontinuities not only by electron microscopy but also by fluorescence microscopy and provide information about the dynamics of membrane openings and their emergence. While this is assuring, the authors conclude that MOs emerge during metaphase. From what the authors show, this particular information cannot be deduced, as there is no dynamic capture of a membrane scission event together with a chromatin marker that would indicate mitosis. The authors could, however, attempt to find such events in live movies, given the high incidence of MOs reported from their EM data.

Thanks to the reviewer for the encouragement. Highly appreciated.

Weaknesses:

In order to convincingly demonstrate the absence of any plasma membrane in the respective regions of the embryonic periphery or between cells of the embryo, the authors would have to show consecutive serial TEM sections where MOs are detected over more z-planes, beyond the mere 3D reconstructions. Although the authors state in the methods section that continuous ultrathin sections were cut for the metaphase sample (page 21, line 472), consecutive sections are never shown in TEM. While we do see the 3D reconstructions, better documentation of the underlying TEM data is missing. It would be necessary to show a membrane opening in consecutive z sections. Alternatively, the authors could seek the possibility to convincingly back up their claims with volume imaging by focused ion beam scanning EM (FIBSEM), where cellular volumes can be sectioned in almost isotropic resolution

We Thank the reviewer for raising these important technical concerns. We have taken this question seriously since first observing membrane discontinuities six years ago, and we have since conducted extensive controls to rule out fixation artifacts.

First of all, in addition to membrane discontinuities, we would like to highlight that a large number of single plasma membranes separating adjacent cytoplasmic domains were detected by EM (Figure 1, 3 and 4). This observation is particularly significant because the invagination model cannot account for the formation of single plasma membrane barriers between adjacent cytoplasmic domains. Instead, independent extension of detached sister membranes offers a plausible explanation for the generation of cytoplasm-immersed membranes. Furthermore, the morphology and continuity of these single cytoplasm-immersed membrane structures are well preserved, indicating successful EM processing and arguing against potential issues such as inadequate fixation or other technical limitations.

Second, we applied rigorous criteria for identifying membrane discontinuities:

(1) To test whether the discontinuities were preparation specific, we examined four independent sample batches and validated our findings using two EM techniques: transmission electron microscopy (HPF-TEM) and dual-beam scanning electron microscopy (SEM).

(2) We analyzed embryos across multiple developmental stages. Membrane discontinuities were observed in both intrauterine and laid embryos at early stages. However, as embryos reached the comma stage—a period marked by the onset of elongation and reduced cell proliferation—the incidence of discontinuities dropped dramatically (0/13, 0/17, and 0/30 cells examined). This developmental specificity argues strongly against a general fixation artifact, which would be expected to occur randomly across stages. Additionally, the eggshell is present throughout the embryonic stage of C. elegans; therefore, the dramatic reduction of membrane discontinuities in comma-stage of embryo argues against the possibility that the eggshell poses a fixation problem.

(3) Each putative membrane discontinuity was identified only after examining the entire plasma membrane of the cell on a given section. Importantly, aside from the discontinuity, the remainder of the plasma membrane remained intact. Moreover, in most cells, only a single discontinuity was present per section, arguing against random, widespread membrane tearing during preparation. Because EM preparation yields serial sections, we verified nearly all membrane discontinuities by examining adjacent sections. Again, the same membrane discontinuity was confirmed only after inspecting the entire plasma membrane on those neighboring sections as well. We will include this verification protocol in the revised Methods and additional imaging of consecutive sections would be provided if needed.

To further determine whether a dividing cell indeed contains one membrane rupture, we performed two serial reconstruction experiments using consecutive sections, as the reviewer suggested. First, we used HPF-TEM to analyze 105 consecutive sections of a metaphase cell, reconstructing the entire plasma membrane and chromosome configuration. We found that one membrane rupture largely encircled the chromosomal disc (Figure 2 and Video S1), spatially aligning with the future segregation zone. Second, we used AutoCUTS-SEM to collect approximately 600 sections covering ~95% of a telophase cell containing three nuclei sharing a common cytoplasm. This tri-nucleated cell was enclosed by three distinct plasma membranes, each harboring a single rupture site. These three ruptures converged to form a Yshaped exposed cytoplasmic region spanning >351 sections (Figure 5). Collectively, these reconstructions demonstrate that each cell contains only one discontinuity from a 3D point of view, further supporting that the phenomenon is not due to random sample preparation damage.

(4) In addition to EM, we performed live imaging of plasma membrane dynamics. While live imaging provides important temporal context, we recognize its limitations in resolving membrane ultrastructure. The rapid kinetics of membrane extension (approximately 20–30 seconds for metaphase and less than 3 minutes for cytokinesis), combined with embryo motility, introduces spatiotemporal ambiguities. To capture dynamic membrane events, our live imaging using the GFP::PH membrane marker was performed at 4-second intervals, approaching the practical limit for single-section scanning of the embryo. With single-plane live imaging, nevertheless, both putative membrane ruptures (Figure 6A) and free-ended sister membrane structures could be detected (Figures 6B and 6C), providing additional evidence that membrane rupture and independent extension of detached sister membranes underlie cytokinesis in C. elegans embryos. Notably, 3D membrane dynamics analysis using light-sheet microscopy (Fu et al. Imaging multicellular specimens with real-time optimized tiling light-sheet selective plane illumination microscopy. Nature Communications. 2016. DOI:10.1038/ncomms11088). revealed membrane ruptures in dividing early C. elegans embryonic cells, including during telophase and metaphase. Therefore, live imaging further validates the membrane rupture phenomena in dividing embryonic cells in C. elegans. 

We are confident that the cumulative evidence presented here addresses the reviewer's concerns and demonstrates that the observed membrane discontinuities, as well as cytoplasm-immersed membranes, are not procedural artifacts but rather reflect a previously underappreciated aspect of plasma membrane dynamics during embryonic cell division.

Another critical issue concerns the detection of the membrane discontinuities in electron micrographs, which, in my opinion, is ambiguous. How do the authors reliably discriminate in their TEM images whether there is a plasma membrane or not? The absence - or weak appearance - of the stain of the electron dense material at membranes, which seems to be their criterion for MOs, is also apparent at other, intracellular membranes, like at the NE or at the ER (for example, see Figure 1C). Also, the plasma membrane itself appears unevenly stained in regions that the authors delineate as intact (for example, Figure 1C, 2B/1).

We thank the reviewer for raising this important concern.

First, our laboratory has extensive experience with electron microscopy across diverse biological systems, including neurons, muscle cells, and hypodermis in C. elegans, as well as tissues from Drosophila, mouse, bacteria, and cultured cells (Chen et al., 2013; Ding et al., 2018; Guan et al., 2022; Y. Li et al., 2018; Miao et al., 2024; Qin et al., 2014; Wang et al., 2026; J. Xu et al., 2022; M. Xu et al., 2021; L. Yang et al., 2020; X. Yang et al., 2019; Zhu et al., 2022). Importantly, we did not introduce any novel or unconventional steps in our EM preparation; all protocols were standard and well established. Thus, the observed membrane discontinuities are unlikely to result from technical inexperience or idiosyncratic methods.

Second, because EM preparation yields serial sections, we verified nearly all membrane discontinuities by examining adjacent sections. Specifically, a membrane discontinuity was confirmed only after inspecting the entirety of the plasma membrane in neighboring sections. We will include this verification protocol in the revised Methods section, and additional images of consecutive sections can be provided if needed.

Third, in addition to membrane discontinuities, a large number of single plasma membranes separating adjacent cytoplasmic domains were detected by EM (Figure 1, 3 and 4). This observation is particularly significant because the invagination model cannot account for the formation of single plasma membrane barriers between adjacent cytoplasmic domains. Instead, independent extension of detached sister membranes offers a plausible explanation for the generation of cytoplasm-immersed membranes. Furthermore, the morphology and continuity of these single cytoplasm-immersed membrane structures are well preserved, indicating successful EM processing and arguing against potential issues such as inadequate fixation or other technical limitations.

EM-related publications by Jingjing Liang:

Chen D, Jian Y, Liu X, Zhang Y, Liang J, Qi X, Du H, Zou W, Chen L, Chai Y, Ou G, Miao L, Wang Y, Yang C. 2013. Clathrin and AP2 Are Required for Phagocytic Receptor-Mediated Apoptotic Cell Clearance in Caenorhabditis elegans. PLoS Genetics 9:e1003517. DOI: https://doi.org/10.1371/journal.pgen.1003517

Ding L, Yang X, Tian H, Liang J, Zhang F, Wang G, Wang Y, Ding M, Shui G, Huang X. 2018. Seipin regulates lipid homeostasis by ensuring calcium‐dependent mitochondrial metabolism. The EMBO Journal 37:e97572. DOI: https://doi.org/10.15252/embj.201797572

Guan L, Yang Y, Liang J, Miao Y, Shang A, Wang B, Wang Y, Ding M. 2022. ERGIC2 and ERGIC3 regulate the ER‐to‐Golgi transport of gap junction proteins in metazoans. Traffic 23:140–157. DOI: https://doi.org/10.1111/tra.12830

Li Y, Zhang Y, Gan Q, Xu M, Ding X, Tang G, Liang J, Liu K, Liu X, Wang X, Guo L, Gao Z, Hao X, Yang C. 2018. C . elegans -based screen identifies lysosome-damaging alkaloids that induce STAT3-dependent lysosomal cell death. Protein & Cell 9:1013–1026. DOI: https://doi.org/10.1007/s13238-018-0520-0

Miao Y, Du Y, Wang B, Liang J, Liang Y, Dang S, Liu J, Li D, He K, Ding M. 2024. Spatiotemporal recruitment of the ubiquitin-specific protease USP8 directs endosome maturation. eLife 13:RP96353. DOI: https://doi.org/10.7554/eLife.96353

Qin J, Liang J, Ding M. 2014. Perlecan Antagonizes Collagen IV and ADAMTS9/GON-1 in Restricting the Growth of Presynaptic Boutons. Journal of Neuroscience 34:10311–10324. DOI: https://doi.org/10.1523/JNEUROSCI.5128-13.2014

Wang Z, Zhang L, Zhou B, Liang J, Tian Y, Jiang Z, Tao J, Yin C, Chen S, Zhang W, Zhang J, Wei W. 2026. A single MYB transcription factor GmMYB331 regulates seed oil accumulation and seed size/weight in soybean. Journal of Integrative Plant Biology 68:470– 485. DOI: https://doi.org/10.1111/jipb.70101

Xu J, Chen S, Wang W, Man Lam S, Xu Y, Zhang S, Pan H, Liang J, Huang Xiahe, Wang Yu, Li T, Jiang Y, Wang Yingchun, Ding M, Shui G, Yang H, Huang Xun. 2022. Hepatic CDP-diacylglycerol synthase 2 deficiency causes mitochondrial dysfunction and promotes rapid progression of NASH and fibrosis. Science Bulletin 67:299–314. DOI: https://doi.org/10.1016/j.scib.2021.10.014

Xu M, Ding L, Liang J, Yang X, Liu Y, Wang Y, Ding M, Huang X. 2021. NAD kinase sustains lipogenesis and mitochondrial metabolism through fatty acid synthesis. Cell Reports 37:110157. DOI: https://doi.org/10.1016/j.celrep.2021.110157

Yang L, Liang J, Lam SM, Yavuz A, Shui G, Ding M, Huang X. 2020. Neuronal lipolysis participates in PUFA‐mediated neural function and neurodegeneration. EMBO reports 21:e50214. DOI: https://doi.org/10.15252/embr.202050214

Yang X, Liang J, Ding L, Li X, Lam S-M, Shui G, Ding M, Huang X. 2019. Phosphatidylserine synthase regulates cellular homeostasis through distinct metabolic mechanisms. PLOS Genetics 15:e1008548. DOI: https://doi.org/10.1371/journal.pgen.1008548

Zhu J, Lam SM, Yang L, Liang J, Ding M, Shui G, Huang X. 2022. Reduced phosphatidylcholine synthesis suppresses the embryonic lethality of seipin deficiency. Life Metabolism 1:175–189. DOI: https://doi.org/10.1093/lifemeta/loac02

eLife Assessment

This manuscript uncovers the importance of Vinculin in the maintenance of junctional integrity during neural tube closure in regions of increased mechanical stress, by using sophisticated methods such as laser ablation and live imaging. The manuscript also reports a novel application of an established embryonic stem cell protocol to efficiently generate mutant and transgenic embryos for analysis. The findings are fundamental in nature, significantly improve our understanding of a major research question, and are backed by compelling evidence. Whilst there is much to appreciate in this work, exactly how Vinculin mediates neural fold elevation remains unclear, and addressing this lacuna will significantly improve the strength of the manuscript; in addition, some rewriting for better clarity (including technical/methodological details) and inclusion of possible consequences of the increased number of tight junction gaps in the vinculin mutant would be pertinent.

Reviewer #1 (Public review):

Summary:

In many vertebrates, the neural tube closes by folding, elevation, and fusion of bilateral neural folds. Loss of the actin-binding protein Vinculin causes failed cranial neural tube closure in mice and is associated with neural tube defects in human patients, but it was not known how Vinculin contributes to neural tube closure. Here, Prudhomme and colleagues find that neural fold elevation and the apical constriction that drives it initiate normally in Vinculin-deficient mouse embryos, but both arrest before the neural folds fuse. The time of failure coincides with increased mechanical tension within the cranial neural plate. They find that Vinculin localizes to areas of high mechanical stress in the WT neural plate, including multi-cellular junctions and dividing cells, and in the absence of Vinculin, recruitment of Myosin and Apical junction proteins is reduced at these sites. These data support a model in which Vinculin recruits junctional proteins to high-stress areas to maintain junctional integrity during neural tube closure.

Strengths:

The data presented are thorough, rigorous, and convincing. The combination of live imaging and transgenic fluorescent reporters enables direct observation of junctional behaviors within the mouse cranial neural plate and detailed analysis of how these behaviors are disrupted upon loss of Vinculin. The authors make good use of an ESC transplant approach to efficiently generate mutant and transgenic embryos for analysis.

Weaknesses:

Although the loss of junctional integrity, especially at multi-cellular junctions, is clearly and convincingly demonstrated in Vinculin-deficient embryos, it is not clear precisely how this disrupts the elevation of the neural folds to cause exencephaly.

Reviewer #2 (Public review):

Summary

Using mouse embryos early in development, this excellent paper from Prudhomme et al. shows that Vinculin's recruitment to adherens junctions during mammalian cranial neural tube closure is essential for maintaining junctional integrity in response to increased tension during this process. Previous work had shown that during neural tube elevation, planar polarity of Myosin II and mechanical forces in the tissue are increased. Additionally, mouse embryos lacking Vinculin were known to display neural tube closure failure, and mutations in human Vinculin had been associated with increased risk of neural tube defects, but the mechanism remained unclear. Here, the authors utilize a high-throughput embryonic stem cell (ESC)-based pipeline to generate Vinculin-depleted embryos, complemented by a conditional mutant lacking Vinculin in the embryonic lineages, to investigate this question. The authors show that Vinculin is not required for force generation, but Vinculin is recruited to cell-cell junctions in a tension-dependent manner and is needed to transmit actomyosin-mediated tension to junctions - particularly tricellular and higher-order multicellular junctions - so that apical constriction can happen during neural fold elevation. Furthermore, they find that Vinculin is required to maintain adhesion during high force events (e.g., rosette resolution and cell division) during neural tube closure. The research builds on previous studies about Vinculin's role in mechanotransduction at cell-cell junctions carried out in cultured epithelial cells, zebrafish cardiomyocytes, or early Xenopus embryos, and investigates how physiological forces required for mouse neural tube closure challenge junction integrity and the important role that Vinculin plays in maintenance of junction integrity and translation of mechanical forces into changes in tissue structure during this process.

Strengths:

This study stands out for its sophisticated use of laser ablation and live imaging in neurulating mouse embryos, enabling quantification of junctional tension, Vinculin recruitment to multicellular junctions, and assessment of junction integrity during neural tube elevation. The authors' use of both ESC-derived Vinculin mutant embryos complemented by a second conditional mutant of Vinculin convincingly demonstrates that their findings are specific to the loss of Vinculin. Additionally, the authors demonstrated proof-of-principle for their ESC-based pipeline with a Shroom3 mutant known to be important for neural tube closure. The Zallen lab's application of the genetically engineered ESC-derived mouse embryo pipeline to efficiently generate larger numbers of mutant mouse embryos exhibiting neural tube closure defects (compared with traditional genetic crossing strategies) that can be utilized for live imaging and mechanical perturbations like laser ablation will be valuable for future work in the field. The authors show that Vinculin depletion disrupts tricellular and multicellular junctions. Notably, over 75% of higher-order (5+) vertices in Vinculin mutant embryos display gaps, but interestingly, about one third of 5+ cell junctions in Control embryos also display gaps, indicating that transient vertex remodeling events are needed for normal neural tube closure. Overall, this is a well-written paper that places the authors' findings within the context of prior literature; their beautiful data that is robustly analyzed and clear figure presentation will make the authors' exciting findings accessible to readers.

Weaknesses:

The criteria for selection of junctions targeted by laser ablation, including specifics of location, Myosin II intensity, and initial junction length, should be more clearly described in the Methods, especially given the use of different reporter strains (MyoIIB-GFP vs. GFP-Plekha7) across figures, which may influence junction selection for laser ablation. Analysis of Myosin II in Vinculin mutant embryos would benefit from staining for active Myosin II (pMRLC), and further examination of actomyosin organization at different stages of neural fold elevation in controls vs. Vinculin mutants would be informative. Although the authors note that ZO-1 gaps are limited to a subset of vertices where adherens junction gaps are detected, the increased frequency of tight junction gaps in Vinculin mutants could have functional significance that should be noted. Finally, inclusion of schematics to detail how the adherens and tight junction gaps were defined and measured at cell vertices, as well as how cell division completion was defined, would improve transparency and strengthen readers' understanding of how the data were quantified.

Reviewer #3 (Public review):

Summary:

Prudhomme et al report a detailed analysis of the role of vinculin in maintaining neuroepithelial integrity during cranial neurulation.

Strengths:

The authors use complementary experiments involving super-resolution microscopy, laser ablation, and live imaging of conditional knockout and ESC-derived embryos to demonstrate that loss of vinculin produces wide gaps between the adherens junctions of neuroepithelial cells at later stages of cranial neural fold elevation. The data presented are of extremely high quality, logically presented in a compelling story, and represent a very substantial contribution.

Weaknesses:

The authors are invited to consider the largely minor questions recommended below.

(1) The laser ablations reported are a correlate of cell border, or 'junctional' tension. Please avoid broad statements such as 'mechanical forces are upregulated' (abstract), which invoke gene-like regulation of tissue-level forces (in Newtons). Changes in junctional tension are likely to relate to changes in force generated, but their relationship is not simple: higher tensile stress withstood by the shorter length of junctions in cells with smaller apical surfaces does not necessarily translate into greater force being produced by that cell. The junctional tension readout measured is perfectly relevant to the paper, more so than tissue-level forces would have been.

(2) What is the mechanical mechanism by which loss of vinculin prevents neural fold elevation? The authors present exciting findings about the cellular consequences of losing Vcl at the late elevation stages when the tissue is quantifiably dysmorphic. A clear argument of how Vcl loss could lead to this dysmorphology would strengthen the paper, particularly given that junctional tension defects are excluded and apical non-constriction at the late stage is only mild.

(3) Can the authors comment on the likely impacts of Vcl deletion on the basal domain of the cell? For example, they could cite live-imaging of distinct behaviours in Williams et al Dev Cell 2014, and the NTD phenotypes of some integrin/focal adhesion mutant mice.

(4) The apparent uncoupling of apical area (larger in Vcl KO) from junctional tension (equivalent) in this model is noteworthy. Can the authors speculate on its potential basis?

(5) Live imaging in Figure 7C appears to show a marked reduction in apical area before cleavage furrow formation (T0-18min), suggesting a large apical constriction event (post-mitotic?), as previously reported (e.g., Ampartzidis et al Dev Biol 2023). Do junctional gaps appear during these constrictions?

(6) The live imaging setup used is clearly sufficient to identify differences between genotypes, so this is only a minor point. The gassing conditions listed in the methods specify 5% CO2, but E8.5 embryos also need low O2 to complete cranial closure. Was the O2 level controlled? Was tissue-level shape change observed to be consistent with ongoing neurulation during live-imaging?

(7) Neither the multi-cell laser ablations in the pre-print by De La O cited here, nor the narrower junctional ablations in Bocanegra-Moreno et al., Nat Phys, (2023), identified differences in recoil between developmental stages. Why might those results be different from the findings reported here (e.g., analysis region - not specified in the latter paper)? Limitations to interpreting junctional ablations between cells with different junction lengths include more of the recoil being dissipated by retraction of the longer ablated border.

(8) Is a truncated Vcl expressed in the ESC model, which could bind catenin without an F-actin anchor? The very high-contrast western shown is cropped so it is not clear whether the catenin-binding N-terminus is present. Does the antibody used recognise the head domain (this reviewer could not readily find the information)?

eLife Assessment

This important study explores how the phase of neural oscillations in the alpha band affects visual perception, indicating that perceptual performance varies due to changes in sensory precision rather than decision bias. The evidence is convincing in its experimental design and analytical approach. This work should interest cognitive neuroscientists who study perception and decision-making.

Reviewer #1 (Public review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

In their paper entitled "Alpha-Band Phase Modulates Perceptual Sensitivity by Changing Internal Noise and Sensory Tuning," Pilipenko et al. investigate how pre-stimulus alpha phase influences near-threshold visual perception. The authors aim to clarify whether alpha phase primarily shifts the criterion, multiplicatively amplifies signals, or changes the effective variance and tuning of sensory evidence. Six observers completed many thousands of trials in a double-pass Gabor-in-noise detection task while an EEG was recorded. The authors combine signal detection theory, phase-resolved analyses, and reverse correlation to test mechanistic predictions. The experimental design and analysis pipeline provide a clear conceptual scaffold, with SDT-based schematic models that make the empirical results accessible even for readers who are not specialists in classification-image methods.

Strengths:

The study presents a coherent and well-executed investigation with several notable strengths. First, the main behavioral and EEG results in Figure 2 demonstrate robust pre-stimulus coupling between alpha phase and d′ across a substantial portion of the pre-stimulus interval, with little evidence that the criterion is modulated to a comparable extent. The inverse phasic relationship between hit and false-alarm rates maps clearly onto the variance-reduction account, and the response-consistency analysis offers an intuitive behavioral complement: when two identical stimuli are both presented at the participant's optimal phase, responses are more consistent than when one or both occur at suboptimal phases. The frontal-occipital phase-difference result suggests a coordinated rather than purely local phase mechanism, supporting the central claim that alpha phase is linked to changes in sensitivity that behave like changes in internal variability rather than simple gain or criterion shifts. Supplementary analyses showing that alpha power has only a limited relationship with d′ and confidence reassure readers that the main effects are genuinely phase-linked rather than a recasting of amplitude differences.

Second, the reverse-correlation results in Figure 3 extend this story in a satisfying way. The classification images and their Gaussian fits show that at the optimal phase, the weighting of stimulus energy is more sharply concentrated around target-relevant spatial frequencies and orientations, and the bootstrapped parameter distributions indicate that the suboptimal phase is best described by broader tuning and a modest change in gain rather than a pure criterion account. The authors' interpretation that optimal-phase perception reflects both reduced effective internal noise and sharpened sensory tuning is reasonable and well-supported. Overall, the data and figures largely achieve the stated aims, and the work is likely to have an impact both by clarifying the interpretation of alpha-phase effects and by illustrating a useful analytic framework that other groups can adopt.

Reviewer #2 (Public review):

Summary:

The study of Pilipenko et al evaluated the role of alpha phase in a visual perception paradigm using the framework of signal detection theory and reverse correlation. Their findings suggest that phase-related modulations in perception are mediated by a reduction in internal noise and a moderate increase in tuning to relevant features of the stimuli in specific phases of the alpha cycle. Interestingly, the alpha phase did not affect the criterion. Criterion was related to modulations in alpha power, in agreement with previous research.

Strengths:

The experiment was carefully designed, and the analytical pipeline is original and suited to answer the research question. The authors frame the research question very well and propose several models that account for the possible mechanisms by which the alpha phase can modulate perception. This study can be very valuable for the ongoing discussion about the role of alpha activity in perception.

Conclusion:

This study addresses an important and timely question and proposes an original and well-thought-out analytical framework to investigate the role of alpha phase in visual perception. While the experimental design and theoretical motivation are strong, the very limited sample size substantially constrains the strength of the conclusions that can be drawn at the group level.

Bibliography:

Button, K., Ioannidis, J., Mokrysz, C. et al. Power failure: why small sample size undermines the reliability of neuroscience. Nat Rev Neurosci 14, 365-376 (2013). https://doi.org/10.1038/nrn3475

Tamar R Makin, Jean-Jacques Orban de Xivry (2019) Science Forum: Ten common statistical mistakes to watch out for when writing or reviewing a manuscript eLife 8:e48175 https://doi.org/10.7554/eLife.48175

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their paper entitled "Alpha-Band Phase Modulates Perceptual Sensitivity by Changing Internal Noise and Sensory Tuning," Pilipenko et al. investigate how pre-stimulus alpha phase influences near-threshold visual perception. The authors aim to clarify whether alpha phase primarily shifts the criterion, multiplicatively amplifies signals, or changes the effective variance and tuning of sensory evidence. Six observers completed many thousands of trials in a double-pass Gabor-in-noise detection task while an EEG was recorded. The authors combine signal detection theory, phase-resolved analyses, and reverse correlation to test mechanistic predictions. The experimental design and analysis pipeline provide a clear conceptual scaffold, with SDT-based schematic models that make the empirical results accessible even for readers who are not specialists in classification-image methods.

Strengths:

The study presents a coherent and well-executed investigation with several notable strengths. First, the main behavioral and EEG results in Figure 2 demonstrate robust pre-stimulus coupling between alpha phase and d′ across a substantial portion of the pre-stimulus interval, with little evidence that the criterion is modulated to a comparable extent. The inverse phasic relationship between hit and false-alarm rates maps clearly onto the variance-reduction account, and the response-consistency analysis offers an intuitive behavioral complement: when two identical stimuli are both presented at the participant's optimal phase, responses are more consistent than when one or both occur at suboptimal phases. The frontal-occipital phase-difference result suggests a coordinated rather than purely local phase mechanism, supporting the central claim that alpha phase is linked to changes in sensitivity that behave like changes in internal variability rather than simple gain or criterion shifts. Supplementary analyses showing that alpha power has only a limited relationship with d′ and confidence reassure readers that the main effects are genuinely phase-linked rather than a recasting of amplitude differences.

Second, the reverse-correlation results in Figure 3 extend this story in a satisfying way. The classification images and their Gaussian fits show that at the optimal phase, the weighting of stimulus energy is more sharply concentrated around target-relevant spatial frequencies and orientations, and the bootstrapped parameter distributions indicate that the suboptimal phase is best described by broader tuning and a modest change in gain rather than a pure criterion account. The authors' interpretation that optimal-phase perception reflects both reduced effective internal noise and sharpened sensory tuning is reasonable and well-supported. Overall, the data and figures largely achieve the stated aims, and the work is likely to have an impact both by clarifying the interpretation of alpha-phase effects and by illustrating a useful analytic framework that other groups can adopt.

Weaknesses:

The weaknesses are limited and relate primarily to framing and presentation rather than to the substance of the work. First, because contrast was titrated to maintain moderate performance (d′ between 1.2 and 1.8), the phase-linked changes in sensitivity appear modest in absolute terms, which could benefit from explicit contextualization. Second, a coding error resulted in unequal numbers of double-pass stimulus pairs across participants, which affects the interpretability of the response-consistency results. Third, several methodological details could be stated more explicitly to enhance transparency, including stimulus timing specifications, electrode selection criteria, and the purpose of phase alignment in group averaging. Finally, some mechanistic interpretations in the Discussion could be phrased more conservatively to clearly distinguish between measurement and inference, particularly regarding the relationship between reduced internal noise and sharpened tuning, and the physiological implementation of the frontal-occipital phase relationship.

We appreciate the reviewer’s thoughtful and constructive feedback, particularly regarding clarity and framing. In response, we have made several revisions to improve transparency and contextualization throughout the manuscript.

First, we now explicitly contextualize the relatively modest change in sensitivity by adding discussion of the contrast-titration procedure and its implications for effect size interpretation. Second, we address the coding error that led to unequal numbers of double-pass stimulus pairs across participants sooner in the manuscript by reporting the average number of pairs per participant in the Results (as well as the Methods), allowing for readers to interpret the results more appropriately. Third, we have provided additional detail, including precise stimulus timing parameters, electrode selection criteria, and a clearer explanation of the rationale for phase alignment in the Results (in addition to the Methods) section. Finally, we have revised portions of the Discussion to adopt more conservative language when interpreting our results, which more clearly distinguishes between empirical observations and mechanistic inferences, along with offering additional interpretations for the frontal-occipital phase relationship.

We believe these revisions substantially improve the clarity, transparency, and interpretability of the manuscript.

Reviewer #2 (Public review):

Summary:

The study of Pilipenko et al evaluated the role of alpha phase in a visual perception paradigm using the framework of signal detection theory and reverse correlation. Their findings suggest that phase-related modulations in perception are mediated by a reduction in internal noise and a moderate increase in tuning to relevant features of the stimuli in specific phases of the alpha cycle. Interestingly, the alpha phase did not affect the criterion. Criterion was related to modulations in alpha power, in agreement with previous research.

Strengths:

The experiment was carefully designed, and the analytical pipeline is original and suited to answer the research question. The authors frame the research question very well and propose several models that account for the possible mechanisms by which the alpha phase can modulate perception. This study can be very valuable for the ongoing discussion about the role of alpha activity in perception.

Weaknesses:

The sample size collected (N = 6) is, in my opinion, too small for the statistical approach adopted (group level). It is well known that small sample sizes result in an increased likelihood of false positives; even in the case of true positives, effect sizes are inflated (Button et al., 2013; Tamar and Orban de Xivry, 2019), negatively affecting the replicability of the effect.

Although the experimental design allows for an accurate characterization of the effects at the single-subject level, conclusions are drawn from group-level aggregated measures. With only six subjects, the estimation of between-subject variability is not reliable. The authors need to acknowledge that the sample size is too small; therefore, results should be interpreted with caution.

Conclusion:

This study addresses an important and timely question and proposes an original and well-thought-out analytical framework to investigate the role of alpha phase in visual perception. While the experimental design and theoretical motivation are strong, the very limited sample size substantially constrains the strength of the conclusions that can be drawn at the group level.

Bibliography:

Button, K., Ioannidis, J., Mokrysz, C. et al. Power failure: why small sample size undermines the reliability of neuroscience. Nat Rev Neurosci 14, 365-376 (2013). https://doi.org/10.1038/nrn3475

Tamar R Makin, Jean-Jacques Orban de Xivry (2019) Science Forum: Ten common statistical mistakes to watch out for when writing or reviewing a manuscript eLife 8:e48175 https://doi.org/10.7554/eLife.48175

We thank the reviewer for their supportive remarks on our design and analysis, and for raising this important statistical concern about our sample size (n=6). Our choice of a small sample size was driven by methodological considerations. Specifically, our reverse correlation analysis requires a large number of trials per participant, as it estimates perceptual tuning by regressing behavioral responses against fluctuations in the energy of stimulus features (orientation and spatial frequency). This approach, as well as the computation of signal detection theory (SDT) metrics such as d′ and criterion, depends on high trial counts to obtain reliable estimates, particularly given that our analysis further subdivides trials across eight phase bins. For this reason, we prioritized collecting a large number of trials per participant (∼5,000), which is consistent with established practices in psychophysical research.

Importantly, our approach means that our design is reliable on the individual level, which motivated us to include a new binomial probability testing in our revised paper. This binomial test helps address concerns about the generalizability of our results. Binomial testing considers each participant as an independent replication of the effect and then computes the p-value associated with the probability of having observed the given number of statistically significant participants by chance, with a false positive rate of 0.05. In our data, 3 out of 6 participants showed significant effects, which corresponds to a probability of 0.002 of having observed these effects by chance alone. We believe this converging evidence supports the replicability and generalizability of our results. To improve the transparency of the single-subject data, we have included single-participant results in the Supplemental Materials to allow readers to directly assess the consistency of effects across individuals and to better contextualize between-subject variability.

Thank you again for your suggestions, we believe that these additions have greatly improved our manuscript by demonstrating the robustness of our findings and increasing the transparency of our single-subject results.

Recommendations for the authors:

Reviewing Editor Comments:

The issue of generalizability arose during the review process, as your results are based on a small sample of participants who undertook a very large number of trials. In the revised version, it would be useful to discuss why this approach is valid, especially in the context of linking EEG with modeling (i.e., why it is more powerful than having many participants with fewer trials), and the extent to which your results can generalize to the population.

We sincerely appreciate all of the helpful comments provided by the reviewers and hope we can address the concerns of our experimental approach. In the introduction, we have emphasized the importance of our current small sample size design, which allows us to reliably compute our signal detection theory metrics across 8 phase bins in addition to including the reverse correlation analysis. In the methods section, we have added a description of the binomial probability statistical framework, which addresses the generalizability of our results. In this framework, each participant is viewed as an independent replication and the p-value reflects the probability of having observed the number of individually significant subjects from the total sample size by chance. In this regard, observing a significant effect in 3 out of 6 participants (as in our study) from chance alone has a 0.002 probability, which we believe is unlikely and instead reflects a true effect present in the general population.

Below I have copied our changes in the introduction and methods sections.

“... in a large number of trials (6,020 per observer, n = 6) across multiple EEG sessions. This approach ensures a sufficient number of trials in order to reliably compute signal detection theory (SDT) metrics across multiple alpha phase bins while also affording enough statistical power for reverse correlation analysis (Xue et al., 2024), making it preferred over having a larger sample size with fewer trials.”

“Additionally, we used a binomial probability testing framework that is designed for small sample sizes and treats each participant as an independent replication. As such, it computes the probability of having observed the number of statistically significant outcomes by chance given our sample size (Schwarzkopf & Huang, 2024).”

Reviewer #1 (Recommendations for the authors):

My suggestions are intended to be light-touch and focused on strengthening the clarity and durability of the Reviewed Preprint rather than on additional experimentation or major new analyses.

(1) Limitation statement for the double-pass coding error:

Add a short statement in the Methods or Results acknowledging that the coding error led to markedly fewer repeated stimulus pairs for the first three participants than for the last three. For the response-consistency result in Figure 2E, a simple acknowledgement that the available evidence is stronger for some participants than others will help readers calibrate their confidence without detracting from the main story.

Thank you for this suggestion, we have now added a statement to this effect in the Results section, in addition to the description already mentioned in the Methods section.

“To examine this, we implemented a double-pass stimulus presentation (~600 stimulus pairs for participants 1-3 and ~2,500 pairs for participants 4-6) and analyzed participant’s response consistency (Xue et al., 2024) to two identical stimuli.”

(2) Contextualizing the titrated performance level:

In the Discussion, explicitly note that contrast was titrated to keep d′ between approximately 1.2 and 1.8, which intentionally maintains moderate performance. This contextualization will help readers understand that while the phase-linked changes appear modest in absolute terms, they are mechanistically informative within this design.

Thank you, we have included a sentence to the Discussions speaking to this point.

“We also note that the observed modulation of d’ between optimal and suboptimal phases was relatively modest in absolute terms (0.21) in our study and could therefore require many trials per subject to detect. Two reasons for this modest effect size could be related to specific features of our task design. First, we titrated stimulus contrast to maintain consistent task performance. This titration could have reduced the magnitude of the phase effect on d’ that would otherwise be apparent if the stimulus intensity were kept constant. Additionally, the use of (relatively) high-contrast random noise likely means that trial-to-trial variability in perception is largely driven by random fluctuations in the noise properties and, to a lesser extent, internal brain state. Although both of these choices were necessary to perform SDT and reverse correlation analysis, they differ from many previous studies investigating alpha phase using only near-threshold detection in the absence of external noise and may contribute to an underestimation of the true effect size.”

(3) Methods clarifications:

(a) Replace placeholder text such as "{plus minus}" and "{degree sign}" with the appropriate symbols, and ensure that any equations implied in the reverse-correlation section are fully present.

Thank you for bringing this to our attention, these placeholder texts are an artifact of the conversion process and we will correct this.

(b) State explicitly that the 8 ms stimulus duration corresponds to a single frame on your 120 Hz display, which will clarify the timing in Figure 1A and the pre-stimulus windows in the phase analyses.

Thank you, we have added language to both the Method and Results sections explicitly indicating that the 8 ms stimulus choice corresponds to a single screen refresh. Additionally, we changed the text in Figure 1A to include inter-trial interval timing (as opposed to merely saying “Start Trial”):

“(A) Task design. Each trial contained a brief, filtered-noise stimulus (8 ms; one screen refresh) presented to the right or left of fixation with equal probability.”

“Each participant (n = 6) completed 5-6 EEG sessions of a Yes/No detection paradigm whereby participants reported the presence or absence of a brief (8 ms; one screen refresh) vertical Gabor target (2 cycles per degree) with concurrent confidence judgments (see Figure 1A), along with an additional imagination judgement (reported in the supplemental materials).”

(c) In the description of the post-stimulus taper, consider phrasing the rationale in terms of minimizing contamination from evoked responses rather than asserting that the taper ends before the earliest evoked response, which keeps the argument correct without committing to a precise latency boundary.

Thank you for this suggestion. We have changed our rationale for the taper to “minimizing”, rather than avoiding, the evoked response.

“This resulted in the post-stimulus data being flat after 70 ms, which is intended to minimize the evoked response in our data.”

(4) Analysis transparency:

(a) In the description of posterior electrode selection, explicitly note that channels were chosen solely on the basis of alpha power, independent of behavioural performance, and that the same electrodes were used for each participant across sessions.

We have gladly made this clarification to the methods.

“This was individually determined by rank-ordering 17 of the posterior channels (Pz, P3, P7, O1, Oz, O2, P4, P8, P1, P5, PO7, PO3, POz, PO4, PO8, P6, and P2) and algorithmically choosing the three with the highest power. This ensured that electrode selection was made independent of performance and instead was based upon maximizing alpha signal strength.”

(b) Describe the phase-alignment step used to center each participant's optimal bin before group averaging as a device for visualization and summary, and clarify that inferential statistics are based on the underlying, non-aligned data as appropriate. This will reassure readers who are cautious about circularity.

We agree that this should be made more explicit throughout the manuscript and have added statements clarifying this aspect in the Figure 2B caption, the Results, and Method sections.

“The data have been aligned across participants so that each individual's highest d’ was assigned to bin 8 (omitted from the plot), with the remaining data circularly shifted, and is averaged across -450 ms to stimulus onset. This graph is for visualization purposes only. Error bars represent ± 1 SEM. The pattern shows a clear phasic modulation of d’ across bins.”

“... requiring us to phase-align the performance data across participants in order to visualize the underlying phasic effects. To this end, we aligned all metrics (d’, c, HR, and FAR) by circularly shifting the data so that the bin with the highest d’ was assigned to bin 8, which was then omitted from further visualizations.”

“Bin 8 was then omitted from further visualizations. The shifted data were then averaged across all time points from -450 ms to 0 ms, based on significant effects at the group level, and averaged across participants. No statistics were conducted on these shifted variables and instead are for visualization purposes only.”

(c) Add a short note on the number of permutations and the cluster-forming threshold in the phase-coupling analyses, if not already stated in the Results or captions, to complete the description of your non-parametric testing procedure.

Thank you, we agree that reiterating this information in the Results section is helpful for the reader to clarify the analysis procedure.

“After smoothing the resultant vector length over time with a 50 ms moving average, we compared the observed vector lengths to a permuted threshold (95th percentile of 1,000 permutations) at each time point from –700 to 0 ms and performed cluster correction (95th percentile of the permuted cluster size) to account for multiple comparisons.”

(5) Discussion framing:

Make one or two small adjustments to your mechanistic phrasing so that the distinctions between measurement and interpretation are fully explicit:

(a) State that the combination of phase-d′ coupling, counterphased hit and false-alarm rates, response consistency, and phase-dependent classification images is "consistent with" a reduction in effective internal noise and sharper estimated tuning at optimal alpha phase, within the assumptions of your SDT and reverse-correlation framework.

Thank you for this suggestion. We have changed the language in the discussions to reflect this framing and interpretation of the results.

“Moreover, our data are consistent with a model in which the variability of internal responses changes systematically across the alpha cycle, as reflected in the inverse relationship between hit rate and false alarm rate.”

(b) Emphasize that reduced effective internal noise and sharpened sensory tuning are two complementary descriptions of a better match between sensory evidence and decision template rather than fully separable mechanisms.

Thank you, we have added this language for clarity of our interpretation.

“Together with decreases in the variance of sensory tuning during the optimal phase, our results suggest that alpha phase impacts sensitivity by shaping trial-to-trial variation in internal noise during perceptual decision making, leading to better matches between sensory evidence and decision templates as opposed to a change in the gain of internal sensory responses.”

(c) Note that the frontal-occipital phase relationship is consistent with a coordinated, possibly top-down component to the alpha-phase effect, while remaining agnostic about the precise physiological implementation.

Thank you for raising this additional interpretation. We have added this as a plausible alternative to the single-source account in the Discussion section.

“Moreover, our results suggest that prior literature reporting phasic effects in the alpha-band range from both frontal and occipital regions may plausibly be reporting the same effect from a single projected dipole source; however, these results are also consistent with two synchronized alpha sources which are anti-phase.”

Reviewer #2 (Recommendations for the authors):

Major issues:

Given that collecting more data may not be doable, the authors should take some actions to test the reliability of their results. For instance, simulations could be run to test the robustness of the results with such a small sample size (Zoefel, 2019). It would also be of interest to include in the report statistics and plots at the individual level, not only the aggregates. It is also important to report which electrodes were used in the analysis for each of the subjects, in the Methods section, it is clearly stated that these electrodes differed between subjects.

Thank you for these suggestions. To assess the reliability of our results at the single-subject level, we have included a new binomial probability test which is a framework suitable for small sample size experiments with large trail numbers (Schwarzkopf & Huang, 2024). Binomial testing views each individual as an independent replication and considers the probability of having observed the number of significant participants given the total number tested participants, and outputs the probability of having observed the results by chance. We believe this framework adequately addresses the reviewer’s concern of generalizability in addition to being well-suited to the design of our study.

To assess individual significance, we averaged the resultant vector length and permutations over the analysis window from -450 to 0 ms. If the resultant vector length exceeded the permutation for that participant, then they were considered to be a significant participant. In total, 3 out of 6 participants (participants 1, 4, and 5) showed significant d’ coupling. The binomial probability (equivalent to a p-value) of having observed this outcome as a result of three false positives at the individual-subject level is very small (p = 0.002), which is sufficiently low for psychological studies.

Below is the text which we have added to the Results and Methods sections.

“To interrogate the robustness of our findings at the single-subject level, we adopted a test of binomial probability, which is a statistical framework that treats each individual as an independent replication and is ideal for small sample size studies that utilize a large number of trials per observer (Schwarzkopf & Huang, 2024). For our data, we assessed individual significance by averaging the actual and permuted resultant vector lengths across time (-450 to 0ms) and comparing the real vector length to the 95% percentile of the permuted datasets. With this approach, 3 out of 6 participants showed significant d’-phase coupling which corresponds to a binomial probability of p = 0.002, indicating a very low probability that we observed these results by chance alone.”

“Additionally, we used a binomial probability testing framework that is designed for small sample sizes and treats each participant as an independent replication. As such, it computes the probability of having observed the number of statistically significant outcomes by chance given our sample size (Schwarzkopf & Huang, 2024). To assess significance at the participant level, we averaged the participant’s resultant vector length and permutations from -450 to 0 ms and obtained the 95th percentile of the time-averaged permutations. We then compared the averaged resultant vector lengths to the permutation thresholds for each subject, which revealed 3 out of 6 significant subjects. We then used the MATLAB function myBinomTest.m (Nelson, 2026) to compute the p-value associated with the probability of having observed 3 out of 6 significant subjects by chance (with a false-positive rate of 0.05).”

To address the reviewer's second request, we now include a supplemental figure which has each individual’s results for the main analysis (see Supplementary figure 3). These graphs, in addition to the methods, now provides the reader with each participant’s given set of analysis electrodes.

“Each participant had a different combination of electrodes which were used in the analyses; however, the same three channels were used across sessions within a participant (participant 1: POz, PO3, O1; participant 2: P7, PO7, PO4; participant 3: P2, P1, Pz; participant 4: O1, Oz, O2; participant 5: O2, PO8, PO4; participant 6: Oz, O2, O1).”

As an alternative approach, linear mixed models (LMM) could be used for statistics, as they are more suitable for small sample sizes (Wiley et al., 2019). LMM improve generalization by modelling subject-specific random effects. Although raw circular data is not suitable for LMM, the sine and cosine of the phases could have been used as predictors, for instance. Given that data were collected for 6 different sessions, sessions could be included as a factor in the model to improve statistical power.

We appreciate the suggestion but feel that LMMs would be a challenge in this case not only because the main predictor variables are circular, but because the main outcome variables are not defined on the single-trial level and require many trials to be computed (e.g., classification images, SDT measures, response consistency). As such, computing these measures within a session may also lead to noisier estimates than we had designed our experiment for. We therefore prefer the more straightforward approach we have taken in the paper, which has now been supplemented by a binomial test of individual-subject level significance.

Given that the number of subjects is quite small, I believe that individual data should be presented (either in the main text or supplementary materials) also for figures: 2A, B, C and D.

Thank you, we have included all of these results to the individual graphs in the Supplemental Materials (see Supplementary figure 3).

In plot 2B (HR and FAR) a p-value = 0.015 appears. However, in the text you write:

"Indeed, this showed that the difference between the HR and FAR vector angle was significantly clustered around a mean of 180{degree sign} (v = 3.78, p = 0.01), indicating that the phase angle associated with the greatest hits was counterphase to the phase angle associated with the greatest false alarms."

Which one is correct? Or do they refer to different tests?

We appreciate you catching this confusing discrepancy. The two values refer to the same test which has a p-value of 0.0145. In the figure, this value was rounded to the thousandths decimal place (i.e., 0.015), whereas in the text it was rounded to the hundredths value (0.01). We now consistently report p-values out to three decimal places throughout the manuscript.

Did you perform any statistical test for phasic modulation of dprime and criterion? I say that because in Figure 2B, you state that the data shows a "clear phasic modulation of d' across bins", but no statistic is mentioned. On the other hand, in Figure 2D, you state, "We did not & observe any significant phase-dependent relationship between phase and criterion." Is this sentence referring to both 2C and 2D panels or only to 2C?

Figure 2B and 2D show the phase-behavior relationship across bins after aligning the phase bins to each participant's “best” d’ bin. This bin is omitted from the plots because it is used for alignment, making the analysis circular. Accordingly, these panels were intended purely for visualization and were not used for statistical inference. Additional language has been added to the figure caption highlighting this aspect.

“The data have been aligned across participants so that each individual's highest d’ was assigned to bin 8 (omitted from the plot), with the remaining data circularly shifted, and is averaged across -450 ms to stimulus onset. This graph is for visualization purposes only.”

The primary statistical test for phase-behavior coupling was performed using permutation testing of the resultant vector length, which quantifies the magnitude of phase-dependent modulation. These results are shown in Figures 2A (for d′) and 2C (for criterion). In the original manuscript, we reported only the time points that survived cluster-based correction, but did not explicitly report the cluster p-values. We have now added these cluster p-values to the manuscript for completeness.

“The data revealed significant cluster-corrected coupling between alpha phase and d’ in the prestimulus window from -220 ms until stimulus onset (cluster p = 0.046),...”

Additionally, we have changed the caption of Figure 2 to be separate for C) and D).

“(C) No evidence for the coupling of criterion to pre-stimulus alpha-band phase. Graph C reveals the time course of the resultant vector lengths for alpha phase-criterion coupling, which shows no significant phase-dependent relationship between phase and criterion.

(D) The underlying shifted c across phase bins (shifted to participants’ optimal phase, as in graph B) did not visually demonstrate a phasic modulation pattern.”

Minor issues:

In general, the paper is very clear. I found a statement confusing in the Response consistency section:

"To quantify response consistency, we computed the proportion of trials in which participants provided the same response across the two identical trials. This procedure was done for each channel at each time point (from -450 to 0 ms) and then averaged."

Which makes no sense, as response consistency is independent of channel and time point. I believe here you refer to the phase, maybe by just changing the order (start with response consistency and then proceed to phase), the paragraph would be clearer.

We appreciate you catching this mistake. We have clarified the Methods section in the following way:

“To quantify response consistency, we computed the proportion of trials in which participants provided the same response across the two identical trials. Since the optimal phase changes over time, the set of trials were classified as either both having occurred during the optimal phase (or otherwise) for each time point (from -450 to 0 ms) and channel. The proportion of consistent responses was then averaged across channels and time.”

Could you include a plot of the power spectrum used for IAF estimation of all the subjects?

Thank you for the suggestion. In Supplemental Figure 3 we have included the power spectrum that was used to estimate IAF in addition to a topoplot of alpha power (IAF +/- 2 Hz) that has the analysis electrodes labelled.

Bibliography:

Wiley RW, Rapp B. Statistical analysis in Small-N Designs: using linear mixed-effects modeling for evaluating intervention effectiveness. Aphasiology. 2019;33(1):1-30. doi: 10.1080/02687038.2018.1454884.

Zoefel B, Davis MH, Valente G, Riecke L, How to test for phasic modulation of neural and behavioural responses, NeuroImage, Volume 202, 2019,116175, https://doi.org/10.1016/j.neuroimage.2019.116175.

eLife Assessment

This is an important study that addresses the role of fever as a conserved response to viral infection. It demonstrates that the heat-shock factor, HSF1, is activated by increased temperature during fever to enhance the anti-viral immune response. The data provides compelling evidence for the conclusions and the work will be of interest to virologists, immunologists, and cell biologists.

Reviewer #1 (Public review):

Summary:

In the manuscript "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods," Xiao and colleagues examine the role of the shrimp Litopenaeus vannamei HSF1 ortholog (LvHSF1) in the response to viral infection. The authors provide compelling support for their conclusions that the activation of LvHSF1 limits viral load at high temperatures. Specifically, the authors convincingly show that (i) LvHSF1 mRNA and protein are induced in response to viral infection at high temperatures, (ii) increased LvHSF1 levels can directly induce the expression of the nSWD (and directly or indirectly other antibacterial peptides, AMPs), (ii) nSWD's antimicrobial activities can limit viral load, and, (iv) LvHSF1 protects survival at high temperatures following virus infection. These data thus provide a model by which an increase in HSF1 levels limits viral load through the transcription of antimicrobial peptides, and provide a rationale for the febrile response as a conserved response to viral infection.

Strengths:

The large body of careful time series experiments, tissue profiling, and validation of RNA-seq data is convincing. Several experimental methodologies are used to support the author's conclusions that nSWD is an LvHSf1 target and increased LvHSF1 alone can explain increased levels of nSWD. Similar carefully conducted experiments also conclusively implicate nSWD protein in limiting WSSV viral loads.

Weaknesses:

As with any complex biological phenomenon, several aspects remain incompletely explained. Nevertheless, in their revision, the authors provide additional analyses supporting the authors model that losing LvHSF1 is not detrimental to survival, by more directly altering viral loads. In addition, their revised manuscript clarifies the complex interactions between infection, the role of HSF1, and hormesis. These revisions increase the impact of their findings.

Comments on revisions:

The authors have addressed all comments, and the manuscript is very much improved.

Reviewer #3 (Public review):

In the manuscript titled "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods", the authors investigate the role of heat shock factor 1 (HSF1) in regulating antimicrobial peptides (AMPs) in response to viral infections, particularly focusing on febrile temperatures. Using shrimp (Litopenaeus vannamei) and Drosophila S2 cells as models, this study shows that HSF1 induces the expression of AMPs, which in turn inhibit viral replication, offering insights into how febrile temperatures enhance immune responses. The study demonstrates that HSF1 binds to heat shock elements (HSE) in AMPs, suggesting a conserved antiviral defense mechanism in arthropods. The findings are informative for understanding innate immunity against viral infections, particularly in aquaculture. However the logical flow of the paper can be improved.

Comments on revisions:

Some aspects of the initial study design, regarding the selection of representative candidate genes and the logical flow, raised concerns. However, these issues have been addressed in the revised manuscript through additional validations and clarifications. Most of my comments and concerns were sufficiently addressed in the revised manuscript. The results support the authors' conclusion that HSF1-dependent regulation of AMP expression contributes to antiviral defense under febrile conditions.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

Despite this compelling data regarding the protective role of HSF1 in the febrile response, what remains unexplained and complicates the authors' model is the observation that losing LvHSF1 at 'normal' temperatures of 25 ℃ is not detrimental to survival, even though viral loads increase and nSWD is likely still subject to LvHSF1 regulation. These observations suggest that WSSV infection may have other detrimental effects on the cell not reflected by viral load and that LvHSF1 may play additional roles in protecting the organism from these effects of WSSV infection, such as perhaps, perturbations to protein homeostasis. This is worth discussing, especially in light of the rather complicated roles of hormesis in protection from infection, the role of HSF1 in hormesis responses, and the findings from other groups that the authors discuss.

We are grateful for your unbiased advice by reviewer. And we have added the description about the role of HSF1 in hormesis responses in discussion in Lines 422-425 in the revised manuscript. Thank you.

Reviewer #2 (Public review):

Temperature is a critical factor affecting the progression of viral diseases in vertebrates and invertebrates. In the current study, the authors investigate mechanisms by which high temperatures promote anti-viral resistance in shrimp. They show that high temperatures induce HSF1 expression, which in turn upregulates AMPs. The AMPs target viral envelope proteins and inhibit viral infection/replication. The authors confirm this process in drosophila and suggest that there may be a conserved mechanism of high-temperature mediated anti-viral response in arthropods. These findings will enhance our understanding of how high temperature improves resistance to viral infection in animals.

The conclusions of this paper are mostly well supported by data, but some aspects of data analysis need to be clarified and extended. Further investigation on how WSSV infection is affected by AMP would have strengthened the study.

We are grateful for your unbiased advice by reviewer. We have provided additional experimental evidence and supplementary instructions in the revised manuscript. Thank you.

Reviewer #3 (Public review):

In the manuscript titled "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods", the authors investigate the role of heat shock factor 1 (HSF1) in regulating antimicrobial peptides (AMPs) in response to viral infections, particularly focusing on febrile temperatures. Using shrimp (Litopenaeus vannamei) and Drosophila S2 cells as models, this study shows that HSF1 induces the expression of AMPs, which in turn inhibit viral replication, offering insights into how febrile temperatures enhance immune responses. The study demonstrates that HSF1 binds to heat shock elements (HSE) in AMPs, suggesting a conserved antiviral defense mechanism in arthropods. The findings are informative for understanding innate immunity against viral infections, particularly in aquaculture. However, the logical flow of the paper can be improved.

We are grateful for the positive comments and the unbiased advice by reviewer. We have improved the logical flow of the paper and added corresponding instructions in the revised manuscript. Thank you.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1: The analysis compares Group TW to Group W (not the other way around).

Thank you very much. To uncover the molecular mechanisms by which high temperature restricts WSSV infection, two shrimp groups, Group TW and Group W, were cultured at 25 °C. Group W comprised shrimp injected with WSSV and maintained at 25 °C continuously. In contrast, Group TW was subjected to a temperature increase to 32 °C at 24 hours post-injection (hpi). Gill samples were collected for analysis 12 hours post-temperature rise (hptr) and subjected to Illumina sequencing (Figure 1A). RNA-seq was used to identify genes responsive to high temperature, particularly those encoding potential transcriptional regulators. Thank you.

(2) The RNA-seq data in Figure 1 focus only on the TFs. The manuscript would benefit from showing all the RNA-seq data and the differentially expressed genes. In particular, are the AMPs upregulated at the same time point? This should not be the case if LvHSF1 were responsible for the transcription of the AMPs, given the time lag between transcription and translation.

Thank you for your suggestion. In Author response image 1, our previous study has revealed that classical heat shock proteins (such as HSP21, HSP70, HSP60, HSP83, HSP90, HSP27, HSP10, and Bip) were induced by RNA-seq between Group TW and Group W, suggesting heat shock proteins exert a crucial role in enhancing the resistance of shrimp to WSSV at elevated temperatures (32 ℃) and underscoring the reliability of our transcriptomic findings (Xiao et al., 2024).

Additionally, we also analyzed the AMPs expression between Group TW and Group W, and the results show that some antimicrobial peptides such as Lysozyme and C-type lectin are upregulated between Group TW and Group W. Notably, we did not detect upregulated expression of SWD between Group TW and Group W. We agree with the reviewer's point of view that there is a time lag between transcription and translation. Supplementary experimental evidences show that the expression level of LvHSF1 is strongly induced by WSSV stimulation, and then the expression level of SWD begins to increase. We have added a description in Lines 136-138 in the revised manuscript.

Author response image 1.

The Figure of the heat shock proteins in Group TW and Group W

Author response image 2.

Transcriptional expression levels of HSF1 and SWD after WSSV stimulation

Reference:

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(3) The data showing the tissue distribution of LvHSF1 and nSWD is a rigorous approach and adds to the manuscript. A similar approach to understanding the time course of expression of AMPs in relationship to LvHSF1 expression levels would strengthen the authors' conclusions that LvHSF1 induction in response to high temperatures and viral infection, in turn, upregulates SWD and other antibacterial genes.

Thank you for your suggestion. As you good suggestion, we detected the transcriptional expression levels of HSF1 and SWD after WSSV stimulation for 0, 2, 4, 6, 8, 12, 16, 20, and 24 hours. The transcriptional expression level of SWD was set to 1.00 at 0 h, in the early stage of WSSV infection (0-12 h, except 6 h), the expression level of LvHSF1 is strongly induced, and then the expression level of SWD begins to increase. Theses results show that LvHSF1 induction in response to viral infection, in turn, upregulates SWD and other antibacterial genes. Thank you.

(4) The data (Figures 3 and 4) show that LvHSF1 is necessary to survive WSSV infection at high temperatures but does not affect survival at lower temperatures, even though LvHSF1 limits VP28 levels, and viral load at both temperatures is confusing. Does this suggest that LvHSF1 is not primarily important for protection against the virus but instead, for protection from the heat-induced damage caused by high temperatures, which would not be surprising? The manuscript would benefit if the authors could address this point. How do the authors envision the protection conferred by LvHSF1 only at high temperatures?

Thank you for your comment. Although no significant difference in shrimp survival rates was observed between LvHSF1-silenced shrimp and GFP-silenced shrimp at low temperature (25 °C), shrimp with silenced LvHSF1 exhibited increased viral loads in hemocytes and gills, suggesting that upregulation of HSF1 expression can protect shrimp from WSSV infection.

Notably, the tolerance temperature for L. vannamei growth ranges from 7.5 to 42 °C. When infected with WSSV, shrimp use behavioral fever to elevate their body temperature (~32 °C), thereby inhibiting WSSV infection (Rakhshaninejad et al., 2023; Xiao et al., 2024). And this temperature (~32 °C) will not cause heat-induced damage to the shrimp. Our results demonstrate that febrile temperatures induce HSF1, which in turn upregulates antimicrobial peptides (AMPs) that target viral envelope proteins and inhibit viral replication.

Only at high temperatures, we observed that knockdown of HSF1 did not affect shrimp survival rate (Figure 4A). Thank you again for your valuable feedback.

Reference:

Rakhshaninejad, M., Zheng, L., Nauwynck, H., 2023. Shrimp (Penaeus vannamei) survive white spot syndrome virus infection by behavioral fever. Sci Rep 13, 18034.

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(5) Related to the previous comment, the authors do not clearly distinguish between basal effects of LvHSF1 or nSWD induction and heat-induced effects and the differences related to the requirement of LvHSF1 for protection. Simply increasing LvHSF1 levels can result in increased nSWD. SWD levels increase upon WSSV infection even at 25 ℃, and the knockdown experiments suggest that this could also occur through LvHSF1. It would be useful to explicitly differentiate between basal functions of HSF1 and induced functions.

Thank you for your suggestion. In previous responses, we have distinguished between basal effects of LvHSF1 or nSWD induction and heat-induced effects.

As your good suggestion, we injected GST or rHSF1 protein into shrimp, the results showed that recombinant protein HSF1 could significantly induced the expression level of SWD (Supplementary Fig. 5C). Further, after knockdown of SWD, shrimp were injection with rLvHSF1 mixed with WSSV. The results showed that the viral load was significantly lower than the control group 48 hours post WSSV infection (Supplementary Fig. 5D). We have added these results to the Supplementary Figure 5C&5D and added a description in Lines 253-255 and Lines 290-293 in the revised manuscript. Thank you for your constructive comments.

Reviewer #2 (Recommendations for the authors):

(1) Two temperatures are used in the experiments of shrimp. It seems that HSF1 is also upregulated by WSSV infection at 25 ℃. However, this upregulation seems not to be able to protect the animals. The authors compare the infection at 25 and 32 ℃ but did not discuss the findings.

Thank you for your comment. Although no significant difference in shrimp survival rates was observed between LvHSF1-silenced shrimp and GFP-silenced shrimp at low temperature (25 °C), shrimp with silenced LvHSF1 exhibited increased viral loads in hemocytes and gills, suggesting that upregulation of HSF1 expression can protect shrimp from WSSV infection. We have added a discussion of this finding in Lines 461-464 in the revised manuscript. Thank you.

(2) In the abstract the authors say that "These insights provide new avenues for managing viral infections in aquaculture and other settings by leveraging environmental temperature control." However, this point has not been discussed in the main text.

We appreciated your comments. We have added a discussion about the environmental temperature control in Lines 512-514 in the revised manuscript. Thank you.

(3) Line 142: "These results suggest that LvHSF1 may play a key role in enhancing shrimp resistance to WSSV at elevated temperatures." Although this type of conclusion has been made in many studies, I think it is impossible to see a "KEY role" based mainly on change in expression.

Thank you for your suggestion. We have revised this conclusion in the revised manuscript. Thank you.

(4) Section 2.1 Induction of Heat Shock Factor 1 in Response to WSSV at High Temperature

Figure 1. Identification of HSF1 as a key factor induced by high temperature.

The two titles are confusing. Whether the upregulation of HSF1 is a response to high temperature or WSSV infection? I think it is more likely a response to high temperature. Did the authors see the difference in HSF1 expression in shrimp with and without WSSV infection at high temperatures?

Thank you for your comment. We have modified the title of Section 2.1 in the revised manuscript. As your good suggestion, we have measured the expression of LvHSF1 after WSSV challenge at high temperatures (32 ℃) in revised Figure 2F-2H in Line 122 in the revised manuscript. The results demonstrate that the expression of LvHSF1 is strongly induced by WSSV stimulation at high temperatures (32 ℃) in the revised manuscript. Thank you.

(5) Figure 2. Upregulation of LvHSF1 in shrimp challenged by WSSV at both low and high temperatures. Results for WSSV challenge at high temperatures are not included in this figure.

Thank you for your suggestion. As your good suggestion, we have measured the expression of LvHSF1 after Poly (I: C) and WSSV challenge at high temperatures (32 ℃) in revised Figure 2C-2H. The results demonstrate that the expression of LvHSF1 is strongly induced by Poly (I: C) and WSSV stimulation at high temperatures (32 ℃). And we have added a description in Lines 168-179 in revised manuscript. Thank you.

(6) Section 2.2 Expression Profiles of LvHSF1 in Shrimp Under Varied Temperature Conditions and WSSV Challenge. Did the authors try poly IC and WSSV challenge at 32℃, and compare with the un-challenge group? Why were only low temperature was analyzed?

Thank you for your suggestion. As your good suggestion, we have measured the expression of LvHSF1 after Poly (I: C) and WSSV challenge at high temperatures (32 ℃) in revised Figure 2C-2H. And we have added a description about the expression of LvHSF1 after Poly (I: C) and WSSV challenge at high temperatures (32 ℃) in Lines 168-179 in revised manuscript. Thank you.

(7) Figure 2: Please indicate the temperature used in C-E and F-H in the figure legend. Statistical significance: compared with which group? Please provide information in the legend or show it in the bar chart.

Thank you for your suggestion. We have added the description of temperature used in revised Figures 2C-2E. The expression changes of HSF1 were compared with those of PBS control group at the corresponding time and we modified the comparison method of significance in revised Figures 2C-2E. Thank you.

(8) Figure 3H: There are two groups (dsGFP+PBS; dsHSF1+PBS) showing with the same symbol (dot line).

Thank you for your comment. The revised Figure 3H has used different symbols to distinguish the two groups. Thank you.

(9) Line 205: qPCR

Thank you for your careful checks. We have corrected this error in the revised manuscript. Thank you.

(10) Figure 5d and f: Please indicate the sample in each row.

Thank you for your suggestion. We have marked the samples in each row in the revised Figures 5d&5f.

(11) Figure 3 and Figure 4: Why different tissues were analyzed in the two experiments? Low temperature: gill and hemocytes. High temperature: gill and muscle? It is better to use the same tissues so that they can be compared. Please indicate the tissue analyzed in D and d.

Thank you for your suggestion. We have repeated the experiment to detect the copy number of WSSV in hemocyte at high temperature (32 °C) after LvHSF1 knockdown. The results showed that knockdown LvHSF1 showed increased viral loads in shrimp hemocyte (Figure 4C). We have supplemented the tissue information in Figure 4D&4d. Thank you.

(12) Figure 2A The time for temperature treatment? hours or days?

Thank you for your comment. Transcriptional expression of LvHSF1 in different tissues of healthy shrimp subjected to low (25 °C) and high (32 °C) temperatures for 12 hours. We have supplemented this information in the legend of Figure 2A in Lines 840-841 in revised manuscript. Thank you.

(13) Line 249: purified by SDS-PAGE gel?

Thank you for your comment. We have modified this description in Lines 272-274 in current manuscript. Thank you.

(14) Line 258 "Next, to verify whether the anti-WSSV function of nSWD was mediated by LvHSF1 at high temperature". I think it is confusing to use "mediated" here. It seems that HSF1 is downstream of nSWD. Actually, HSF1 controls the expression of nSWD and thus regulates the anti-WSSV effect of shrimp at high temperatures.

We appreciated your comments. We have modified this description in Lines 282-283 in current manuscript. Thank you.

(15) Line 458 "The most probable anti-WSSV mechanism of nSWD is its direct interaction with WSSV envelope proteins VP24 and VP26, potentially inhibiting viral entry into target cells. I suggest the author analyze the entry of WSSV to see whether nSWD blocks this process.

Thank you for your comment. In general, the antimicrobial mechanism of action of AMPs is thought to involve direct membrane disruption, especially for enveloped virus (such as WSSV) (Wilson et al., 2013).

Thanks to the reviewers for their valuable comments. Our manuscript mainly focuses on the febrile temperature-inducible HSF in host antiviral immunity, and the role of HSF1 in regulating antimicrobial effectors (such as SWD). Due to the limitation of the manuscript's length, we will further investigate the functional mechanisms of SWD-specific anti-WSSV in future studies. Thank you.

Reference:

Wilson, S.S., Wiens, M.E., Smith, J.G., 2013. Antiviral Mechanisms of Human Defensins. Journal of Molecular Biology 425, 4965-4980.

(16) Line 435-456 The author discusses the difference between two shrimp species. Did the two studies measure the same immune parameters? I wonder whether the different observation is due to true differences or different methods they used to evaluate the response. If no immune response was promoted in the previous study, what's the possible anti-viral mechanism?

We appreciated your comments. Firstly, the shrimps in the two experimental groups have different adaptability to temperature. The optimal water temperature for M. japonicus growth ranges from 25 to 32 °C, and the tolerance temperature for L. vannamei growth ranges from 7.5 to 42 °C. Secondly, the experimental environmental factors are different in the two experimental groups. Ammonia is a key stress factor in aquatic environments that usually increases the risk of pathogenic diseases in aquatic animals, however, High temperatures (32°C) have been shown to inhibit the replication of WSSV and reduce mortality in WSSV-infected shrimp. Thirdly, the two studies tested different immune indicators. Ammonia-induced Hsf1 suppressed the production and function of MjVago-L, an arthropod interferon analog. In this study, our findings revealed the molecular mechanism through which the HSF-AMPs axis mediates host resistance to viruses induced by febrile temperature. Taken together, the benefits of HSF1 can be attributed to either the host or the pathogen, depending on the nature and context of the host-virus-environment interaction.

(17) Line 472 "directly bind to WSSV envelope proteins and inhibit WSSV proliferation"

I think it is confusing to use "proliferation" here. It seems that the binding of HSF affects the replication process. However, based on the authors' discussion, HSF may likely block viral entry.

Thank you for your suggestion. We have modified this description in Lines 505-507 in the current manuscript. Thank you.

Reviewer #3 (Recommendations for the authors):

In the manuscript titled "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods", the authors investigate the role of heat shock factor 1 (HSF1) in regulating antimicrobial peptides (AMPs) in response to viral infections, particularly focusing on febrile temperatures. Using shrimp (Litopenaeus vannamei) and Drosophila S2 cells as models, this study shows that HSF1 induces the expression of AMPs, which in turn inhibit viral replication, offering insights into how febrile temperatures enhance immune responses. The study demonstrates that HSF1 binds to heat shock elements (HSE) in AMPs, suggesting a conserved antiviral defense mechanism in arthropods. The findings are informative for understanding innate immunity against viral infections, particularly in aquaculture. However, the logical flow of the paper can be improved. Following are my specific concerns.

Major comments

(1) The study design is pretty good, but the logical flow is not. The following should be improved.

(a) In Figure 1, the reason for selecting HSF1 as the focus of the study is not clearly explained.

Thank you for your comment. In a previous study, we have revealed that heat shock proteins exerted a significant role in enhancing the resistance of shrimp to WSSV at elevated temperature (32 ℃) (Xiao et al., 2024). GO functional enrichment analysis of DEGs between group TW and group W, indicating that most DEGs were involved in biological processes such as protein refolding, chaperone-mediated protein folding, and heat response. Therefore, special attention has been paid to heat shock factor 1 (HSF1), the master regulator of the heat shock response. We have added the description in Lines 136-138 in the revised manuscript. Thank you.

Reference:

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(b) As the authors draw models in Figure 9, the established activation mechanism of HSF1 is via trimerization by the release of HSP90, which binds to misfolded proteins under stress conditions, such as heat shock. Therefore, the increase in the HSF1 mRNA level in Figure 1 is strange. The authors need to clarify this issue by explaining this established activation mechanism of HSF1 and also must provide the basis of upregulation of HSF1 by mRNA increase via citing papers in the Introduction.

We appreciated your comments. Under non-stress conditions, HSF monomers are retained in the cytoplasm in a complex with HSP90. During the stress response, such as high temperature, HSF dissociates from the complex, trimerizes, and converts into a DNA-binding conformation through regulatory upstream promoter elements known as heat shock elements (HSEs) (Andrasi et al., 2021). Previous studies have demonstrated that the expression of HSF1 was remarkably induced by stress response, such as high temperature (Ren et al., 2025), virus infection (Merkling et al., 2015), and ammonia stress (Wang et al., 2024). Our results also showed that the expression of LvHSF1 was significant induced by WSSV infection and high temperature (Figure 2). Therefore, this is not surprising that the increase in the HSF1 mRNA level in Figure 1.

In response, we have revised the proposed model to better reflect our experimental findings and the accompanying description. This revision ensures that the schematic is consistent with our data and accurately represents the proposed mechanism. We appreciate your careful review and constructive feedback.

Reference:

Andrasi, N., Pettko-Szandtner, A., Szabados, L., 2021. Diversity of plant heat shock factors: regulation, interactions, and functions. J Exp Bot 72, 1558-1575.

Ren, Q., Li, L., Liu, L., Li, J., Shi, C., Sun, Y., Yao, X., Hou, Z., Xiang, S., 2025. The molecular mechanism of temperature-dependent phase separation of heat shock factor 1. Nature Chemical Biology.

Merkling, S.H., Overheul, G.J., van Mierlo, J.T., Arends, D., Gilissen, C., van Rij, R.P., 2015. The heat shock response restricts virus infection in Drosophila. Sci Rep 5, 12758.

Wang, X.X., Zhang, H., Gao, J., Wang, X.W., 2024. Ammonia stress-induced heat shock factor 1 enhances white spot syndrome virus infection by targeting the interferon-like system in shrimp. mBio 15, e0313623.

(c) For RNA seq analysis in both in Figures 1 and 5, they need to provide changes in conventional HSF1 target chaperones (many HSPs) to validate their RNA seq data.

Thank you for your suggestion. In Authopr response image 1, our previous study has revealed that classical heat shock proteins (such as HSP21, HSP70, HSP60, HSP83, HSP90, HSP27, HSP10, and Bip) were induced by RNA-seq between Group TW and Group W, suggesting heat shock proteins exert a crucial role in enhancing the resistance of shrimp to WSSV at elevated temperatures (32 ℃) and underscoring the reliability of our transcriptomic findings (Xiao et al., 2024). We have added the description in Lines 136-138 in the revised manuscript.

In Figure 5, we have supplemented the heat shock proteins downregulated DEGs by transcriptome sequencing of dsGFP +WSSV (32 ℃) vs. dsLvHSF1 +WSSV (32 ℃) in Supplementary table 2. The results showed that the classical heat shock proteins were downregulated by the RNA-seq, underscoring the reliability of our transcriptomic findings. We have added the description in Lines 213-216 in the revised manuscript. Thank you.

Reference:

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(d) In Figure 5, they did experiments by focusing on the changes by HSF1 knockdown at 32 ℃. However, the logical flow should be focusing on genes whose expression was increased by 32 ℃ compared with 25 ℃ (in figure 1), among them they need to characterize HSF1 target genes. Here as mentioned above, classical HSP genes must be included in addition to those AMP genes.

Thank you for your suggestion. As your good suggestion, we have supplemented the heat shock proteins downregulated DEGs by transcriptome sequencing of dsGFP +WSSV (32 ℃) vs. dsLvHSF1 +WSSV (32 ℃) in Supplementary table 2. The results showed that the classical heat shock proteins were downregulated by the RNA-seq, underscoring the reliability of our transcriptomic findings. We have added the description in Lines 213-216 in the revised manuscript. Thank you.

(e) What is the logical basis of just picking nSWD? It is another example of cherry-picking similar to picking HSF1 in Figure 1.

We appreciated your comments. To determine how temperature-induced LvHSF1 restricts WSSV infection, RNA-seq was performed to identify target genes regulated by HSF1. By analyzing the differentially expressed genes (DEGs), we screened eight candidate proteins for immunity-effector molecules, including SWD, CrustinⅠ, C-type lectin, Anti-lipopolysaccharide factor (ALF), and Vago. CrustinⅠ has been shown to play an important role in antiviral immunity (Li et al., 2020); C-type lectin (CTL1) can bind to the VP28, VP26, VP24, VP19, and VP14, thereby inhibiting the infection of WSSV (Zhao et al., 2009); Anti-lipopolysaccharide factor (ALF3) performs its anti-WSSV activity by binding to the envelope protein WSSV189 (Methatham et al., 2017); Vago can inhibit WSSV infection by activating the Jak/Stat pathway in shrimp (Gao et al., 2021). However, the detailed regulatory mechanism of SWD against WSSV was unclear, and particular attention was paid to the SWD. We have added the description in Lines 215-220 in the revised manuscript. Thank you for your valuable comments and the logic of the manuscript has been improved.

Reference:

Li, S., Lv, X., Yu, Y., Zhang, X., Li, F., 2020. Molecular and Functional Diversity of Crustin-Like Genes in the Shrimp Litopenaeus vannamei, Marine Drugs 18, 361.

Zhao, Z.Y., Yin, Z.X., Xu, X.P., Weng, S.P., Rao, X.Y., Dai, Z.X., Luo, Y.W., Yang, G., Li, Z.S., Guan, H.J., Li, S.D., Chan, S.M., Yu, X.Q., He, J.G., 2009. A novel C-type lectin from the shrimp Litopenaeus vannamei possesses anti-white spot syndrome virus activity. Journal of Virology 83, 347-356.

Methatham, T., Boonchuen, P., Jaree, P., Tassanakajon, A., Somboonwiwat, K., 2017. Antiviral action of the antimicrobial peptide ALFPm3 from Penaeus monodon against white spot syndrome virus. Dev Comp Immunol 69, 23-32.

Gao, J., Zhao, B.R., Zhang, H., You, Y.L., Li, F., Wang, X.W., 2021. Interferon functional analog activates antiviral Jak/Stat signaling through integrin in an arthropod. Cell Rep 36, 109761.

(f) Likewise, choosing Atta in S2 cells needs logic.

We appreciated your comments. Our manuscript revealed that febrile temperature inducible HSF1 confers virus resistance by regulating the expression of antimicrobial peptides (AMPs) in L. vannamei. Further, we want to know that whether HSF1 regulation of antimicrobial peptides is a conserved defense mechanism induced by elevated temperature in arthropods, and experiments were performed in an invertebrate model system (Drosophila S2 cells). Previous study showed that DmAMPs (such as Attacin A, Cecropins A, Defensin, Metchnikowin, and Drosomycin) exerted a significant role in the antiviral immunity in Drosophila (Zhu et al., 2013). Our results showed that the expression of Attacin A, Cecropins A and Defensin were remarkably induced by DmHSF, and the expression of Attacin A was the highest induced. Therefore, DmAtta was chosen as a representative to further demonstrate that DmHSF1 exerts its anti-DCV function by regulating DmAMPs. We have added the description in Lines 328-330 and Lines 361-364 in the revised manuscript. Thank you for your valuable comments and the logic of the manuscript has been improved.

Reference:

Zhu, F., Ding, H., Zhu, B., 2013. Transcriptional profiling of Drosophila S2 cells in early response to Drosophila C virus. Virol J 10, 210.

(2) From Figure 6I to 6K, the authors aimed to verify whether the anti-WSSV function of nSWD was mediated by LvHSF1 at high temperatures. However, what they showed was just showing that nSWD plays anti-WSSV function downstream of HSF1. The authors should show additional data for dsControl+rnSWD.

Thank you for your suggestion. As your suggestion, after knockdown of SWD, shrimp were injection with rLvHSF1 mixed with WSSV. The results showed that the viral load was significantly lower than the control group 48 hours post WSSV infection (Supplementary Fig. 5D). We have added these results to the Supplementary Figure 5C&5D and added a description in Lines 290-293 in the revised manuscript. Thank you for your constructive comments.

(3) For the physical interaction between nSWD and WSSV, it will be great if the authors perform Alphafold3 prediction analysis (Abramson et al PMID: 38718835).

Thank you for your suggestion. As you suggestion, we performed Alphafold3 prediction analysis on SWD and WSSV (VP24 and VP26). The predicted template modeling (pTM) score measures the accuracy of the entire structure. A pTM score above 0.5 means the overall predicted fold for the complex might be similar to the true structure. The Alphafold3 prediction results show that there is a possible interaction between SWD and WSSV. Notably, our manuscript demonstrated that rSWD could interact with VP24 and VP26 by pulldown assays and confocal analysis.

Author response image 3.

Alphafold3 prediction analysis of SWD&VP24 as follow (pTM = 0.64)

Author response image 4.

Alphafold3 prediction analysis of SWD&VP26 as follow (pTM = 0.53)

Minor comments

(1) In the Abstract and many other places, the authors need to specifically write "Drosophila S2 cells" instead of "Drosophila" because conventionally Drosophila implies fruit fly as an organism. We don't say cultured human cells as "human" or "Homo sapiens" in papers.

Thank you for your suggestion. We have modified the description of Drosophila in the revised manuscript. Thank you.

(2) Figure numbers can be reduced for better readability. I would combine Figures 1 and 2, and Figures 3 and 4. If the combined figures are too crowded, some can go to into supplementary figures.

Thank you for your suggestion. We have moved the Poly (I: C) data to Supplementary Figure 2 in the revised manuscript. However, we have added some experimental data to Figures 1, 2, 3, and 4. Therefore, we did not combine Figure 1 and Figure 2, and Figures 3 and 4. Thank you.

(3) One of the best-understood roles of HSF1 in physiology other than heat shock response is longevity, in particular with C. elegans. The authors need to mention this in the Discussion by citing the following recent review paper (Lee PMID: 36380728).

Thank you for your suggestion. We have supplemented the description of HSF1 regulating longevity and aging of organisms and cited the above reference in the revised manuscript (Lee and Lee, 2022). Thank you.

Reference:

Lee, H., Lee, S.V., 2022. Recent Progress in Regulation of Aging by Insulin/IGF-1 Signaling in Caenorhabditis elegans. Mol Cells 45, 763-770.

(4) Please make your own label for small letter panels or transfer small letter panels to supplementary figures.

Thank you for your suggestion. We have adjusted the relevant letter labels. The uppercase letters represent the main image of the Figure, and the small letter panels are the corresponding supplementary instructions in the revised manuscript. Thank you.

(5) In the introduction part, I recommend changing the references for HSFs and HSR with recent ones.

Thank you for your suggestion. We have added the latest references for HSFs and HSR in the Introduction part of the revised manuscript. Thank you.

(6) In Figure 1, it is not intuitive to understand the name groups W and TW.

We appreciated your comments. We have added the description of Group W and Group TW in revised Figure 1. Group W comprised shrimp injected with WSSV and maintained at 25 °C continuously. In contrast, Group TW was subjected to a temperature increase to 32 °C at 24 hours post-injection (hpi). Gill samples were collected for analysis 12 hours post-temperature rise (hptr) and subjected to Illumina sequencing. Thank you.

(7) Please add some kinds of sequence comparisons of SWD and nSWD for readers to understand the homology.

We appreciated your comments. We have added the multiple sequence alignment of SWD proteins in shrimp species in revised Supplementary Figure 3. Highly conserved amino acid residues and cysteine and residues are highlighted in red, indicating that LvSWD is a conserved antimicrobial peptide of the Crustin family. Thank you.

(8) Naming nSWD with "newly identified" is strange as it will not be new anymore as time goes by. Please change the name.

Thank you for your suggestion. We have modified the name of nSWD to SWD in the revised manuscript. Thank you.

(9) Please write the full name for Lv (Litopenaeus vannamei), Dm (Drosophila melanogaster), ds (double-stranded) before using LvHSF1, DmHSF1, and dsLvHSF1.

Thank you for your comments. We have added the full name of LvHSF1, DmHSF1, and dsLvHSF1 in the revised manuscript. Thank you.

(10) In Figure 2, it will be better to transfer poly I:C data to supplementary figures.

Thank you for your comments. We have moved the Poly (I: C) data to Supplementary Figure 2 in the revised manuscript. Thank you.

(11) The label for pGL3-nSWD-M12 is confusing. M1 and M2 are OK. Please change M12 with M1/2 or another one.

Thank you for your suggestion. We have changed pGL3-nSWD-M12 with pGL3-nSWD-M1/2 in the revised manuscript. Thank you.

eLife Assessment

This article presents valuable findings on how the timing of cooling affects autumn bud set in European beech saplings. The study leverages extensive experimental data and provides an interesting conceptual framework for the various ways in which warming can affect bud set timing. The statistical analysis is very well considered, while indicating some factors that may temper the authors' claims. The factorial experiments offer solid support.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

This study provided key experimental evidence for the "Solstice-as-Phenology-Switch Hypothesis" through two temperature manipulation experiments.

Strengths:

The research is data-rich, particularly in exploring the effects of pre- and post-solstice cooling, as well as daytime versus nighttime cooling, on bud set timing, showcasing significant innovation. The article is well-written, logically clear, and is likely to attract a wide readership.

Reviewer #2 (Public review):

In 'Developmental constraints mediate the reversal of temperature effects on the autumn phenology of European beech after the summer solstice', Rebindaine and co-authors report on two experiments on Fagus sylvatica where they manipulated temperatures of saplings between day and night and at different times of year. I think the experiments are interesting, but note that the treatments are extreme compared to natural conditions. Further, given that much of the experiment happened outside, I am not sure how much we can generalize from one year for each experiment, especially when conducted on one population of one species.

Author Response:

The following is the authors’ response to the previous reviews

eLife Assessment

This article presents useful findings on how the timing of cooling affects the timing of autumn bud set in European beech saplings. The study leverages extensive experimental data and provides an interesting conceptual framework for the various ways in which warming can affect but set timing. The statistical analysis is compelling, but indicates some factors that may temper the authors' claims, while the designs of experiments offer incomplete support for the current claims as they rely on one population under extreme conditions for only one year each while a confounding effect (time in a chamber) sometimes lacks a control.

We thank the editor and reviewers for their consideration of our revised manuscript and for their constructive suggestions. In response to the editor’s guidance, we have ensured that: 1) the experimental design is clearly presented as physiological forcing, 2) the Solstice-as-Phenology-Switch concept is explicitly defined, limited, and framed as inferred, 3) conclusions are strictly aligned with the scope of the evidence, and limitations are acknowledged transparently.

We hope these revisions fully address the remaining concerns and clarify both the conceptual framework and the appropriate scope of inference.

Public Review:

Reviewer #1 (Public review):

The authors identified the summer solstice (June 21) as a phenological "switch point", but the flexibility of this switch point remains poorly understood. A more precise explanation of what "flexibility" means in this context is needed, along with a description of the specific experimental results that would demonstrate this flexibility.

We agree that the concept of “flexibility” required clearer definition and a more explicit link to the experimental results. In the Introduction, we now explicitly define flexibility as the capacity for the effective timing of the phenological switch to shift earlier or later depending on developmental progression, rather than occurring at a fixed calendar date. This switch occurs at the compensatory point between the antagonistic influences of early-season development [ESD effect] and late-season temperature [LST effect](L92-98). We have extended and clarified our explanation of the summer solstice’s role in this framework (L69-90). We propose that the solstice acts as an environmental switch that initiates the LST effect, as declining daylengths signal trees to become responsive to late-season cooling (L92-94). The compensatory point then occurs where the advancing ESD effect is balanced by the delaying LST effect. This point should therefore not be fixed to a calendar date but instead vary with developmental progression each year (L75-95).

In the Discussion, we clarify that flexibility is demonstrated experimentally by the observation that the magnitude of July cooling effects (LST effect) on autumn phenology depend on prior developmental rate (ESD effect) [3.4 times greater delay in late-leafing trees], indicating that the position of the compensatory point is development-dependent rather than fixed to June 21 (L398-410). We have made consistent edits throughout the Discussion, in particular in the ‘Support for the Solstice-as-Phenology-Switch Hypothesis’ subsection (L514-530).

The experiment did not directly measure the specific date of the phenological switch point. Instead, it was inferred by comparing temperature effects before and after the solstice. The manuscript should clearly state that this switch point remains an inferred conceptual node rather than a directly measured variable.

We fully agree and have clarified this in the revised manuscript. In the Discussion, we now clearly state that the compensatory point is a conceptual node inferred from responses to cooling before the solstice (June), directly after it (July), or later in the growing season (August) rather than a directly observed phenological event (L352-358 & L405-406).

In Experiment 1, the effect of bud type (terminal vs. lateral) was inconsistent across the overall model and the different leafing groups. The authors should provide a more thorough discussion of potential reasons for this inconsistency.

This inconsistency reflects biological complexity. In the Discussion, we now expand our interpretation to note that terminal and lateral buds may differ in developmental status, resource allocation and hormonal context. We emphasize that bud-type effects are therefore expected to be context-dependent and to interact with wholeplant developmental state, which plausibly explains why effects differ across leafing groups and models (L390-396).

In addition, the statistical model for Experiment 1 indicates that the measured variables (summer cooling and leaf emergence date) explain only 23.4% of the variation in bud formation timing. This leaves over 76% of the variation unexplained, suggesting that other important factors are involved. The discussion should address this limitation in greater depth, moving beyond a focus on the measured variables.

We now discuss the explained and unexplained variance in more detail. We also make it clear that our experiment was designed to test specific mechanistic pathways rather than to fully explain all phenological variability or maximise predictive power L417-419).

In the Discussion, we acknowledge that a substantial fraction of variation remains unexplained (L419-421). We discuss the possibility of other physiological mechanisms, such as photosynthetic assimilation, contributing to the unexplained variation (L421-427). However, large inter-individual variability is commonplace in autumn phenology. A low intra-class correlation coefficient (ICC = 0.26; see L276-280 for methods) suggests much of the remaining variation is attributable to individual-level differences rather than missing explanatory variables (L429-431). In line with the literature, we suggest that genetic and epigenetic differences likely contributed significantly to inter-individual variation, even within a single provenance population (L431-434). In this context of high individual variability, leaf-out timing (ESD effect) and summer cooling treatment (LST effect) together explaining 23.4% of variation in bud set timing is biologically meaningful and demonstrates the mechanistic importance of these processes (L438-441). For completeness, we also briefly discuss alternate sources of within-treatment variability (L434-437).

Reviewer #2 (Public review):

I think the experiments are interesting, but I found the exact methods of them somewhat extreme compared to how the authors present them.

We appreciate this concern and have substantially revised the manuscript to clarify the experimental logic. In the Introduction, we now state explicitly that the study uses temperature regimes that were designed as strong physiological forcing treatments, intended to deeply constrain development and isolate mechanisms rather than to simulate natural or future climatic conditions (L113-115).

In the Methods, we have enhanced our description of the non-linear effects of temperatures below 10°C on physiological processes (L154-158).

At the start of the Discussion, we have added a dedicated paragraph clarifying the scope of inference: the experiment tests causality and constraint (i.e. whether specific physiological processes can drive phenological shifts), not quantitative responses under realistic climate scenarios (L346-363). Throughout the Discussion, we have revised language that could be read as scenario-based interpretation, replacing it with mechanistic phrasing.

Further, given that much of the experiment happened outside, I am not sure how much we can generalize from one year for each experiment, especially when conducted on one population of one species.

Given the large individual variation expected in phenological experiments, we used single experimental populations of single provenance beech saplings to minimise uncontrolled for variation arising from genetic differences (L358-360). This allowed us to elucidate mechanisms despite noisy biological heterogeneity associated with phenology.

In the last round of revision, we toned down statements of generalisation. In the Discussion, we now go further to clarify what mechanistic understanding can be gleamed directly from our findings and then cautiously make suggestions how these mechanisms may play out in natural systems. We repeatedly state the intention of the study as mechanistic inference rather than predictive power, e.g. “However, extrapolations to more complex natural ecosystems should be made with caution as our experimental design prioritised mechanistic inference over generalisability and predictive power.” (L417-419). Alongside our previous calls for tests on other species, we now additionally call for tests on other provenances of beech (L511-512).

I was also very concerned by the revisions.

If this concern stems from the confusion regarding line-numbers and the two submitted versions of the manuscript (with tracked changes and without tracked changes; as required by eLife), then we hope that situation is now clarified. Otherwise, the authors do not understand why our previous revisions would be perceived as being concerning. Regardless, we have made every attempt to address the remaining comments comprehensively.

Further, I am at a loss about their hypothesis, when they write in their letter: "Importantly, the Solstice-asPhenology-Switch hypothesis does not assume that the reversal is fixed to June 21." Why on earth reference the solstice if the authors do not mean to exactly reference the solstice?

We appreciate this important conceptual point. The Solstice-as-Phenology-Switch hypothesis is central to our conceptual model and therefore requires clear explanation. In concert with our changes in response to Reviewer 1’s comment regarding flexibility, we have substantially revised and improved our description of this hypothesis (L69-108).

Whilst the summer solstice is fixed to a calendar date (June 21), the timing of when trees change their autumn phenological responses to temperature is not (L88-90 & L515-517). This occurs when the compensatory point of two antagonistic effects is crossed. Higher early-season development rates (which are driven by temperature) have an advancing (negative) effect on autumn phenology, which we now refer to as the ESD effect (L71-78). Warmer late-season temperatures have a delaying (positive) effect because trees become phenologically susceptible to cooling, i.e. overwintering responses are induced in response to cooling, which we now refer to as the LST effect (L78-82). The point in time when these two effects balance each other out, i.e. the net effect = 0, is the compensatory point (L95-97 & L523-525). The reason this point occurs after the solstice, is because the LST effect only becomes active when days begin to shorten (L92-94 & L522-523). The solstice acts as an environmental switch, initiating trees’ susceptibility to cooling. Therefore, the solstice is referenced in the hypothesis because it forms a daylength barrier. In this framework, the compensatory point cannot occur earlier than the solstice because day lengths are still increasing (L517-519).

In the Introduction and Discussion, we clarify that the solstice is referenced as a biologically meaningful photoperiodic cue, not as a fixed threshold date. We now emphasise that the hypothesis concerns a seasonal reversal in responses to temperature structured around photoperiod, whose effective timing depends on developmental state, rather than a reversal occurring precisely on June 21. To avoid confusion, we have reworded phrases such as “summer solstice effect reversal” to “reversal of phenological responses to temperature after the summer solstice” (L371). In accordance, we have also changed the title to “Developmental constraints mediate the reversal of temperature effects on the autumn phenology of European beech after the summer solstice”.

The following comments stem from the first round of review. We have previously revised the manuscript in accordance with these comments. For most of these points we do not see further cause for changes except for any overlap with comments above. We therefore predominantly copy our previous responses in quotes for clarity, the exception being the comment regarding the framing of our results in relation to natural systems.

The comments below relate to my original review with many of them still applying.

Methods: As I read the Results I was surprised the authors did not give more info on the methods here. For example, they refer to the 'effect of July cooling' but never say what the cooling was. Once I read the methods I feared they were burying this as the methods feel quite extreme given the framing of the paper.

“We understand the concern regarding the structure of the manuscript and note that the methods section was moved to the end of the paper in accordance with eLife’s recommended formatting. We have now moved the methods section before the results to ensure that readers are familiar with the treatments before encountering the outcomes.

Regarding presentation, treatment details are now described in both the Methods and the relevant figure legends. Given this structure, we have chosen not to restate the full treatment conditions in the main Results text to avoid repetition.”

The paper is framed as explaining observational results of natural systems, but the treatments are not natural for any system in Europe of which I have worked in. For example a low of 2 deg C at night and 7 deg C during the day through end of May and then 7/13 deg C in July is extreme. I think these methods need to be clearly laid out for the reader so they can judge what to make of the experiment before they see the results.

We appreciate the reviewer’s concern regarding the use of relatively extreme temperature treatments and the need to ensure that our conclusions are consistent with the motivation for using them. The manuscript was also revised in this regard in the previous round, and we copy the relevant responses at the bottom of this response. Despite this, we agree that further explanation of how our experimental treatments suited the aims of our study was still required.

The aim of these treatments was not to reproduce typical ambient conditions, but to act as a mechanistic probe. Such mechanisms are not readily identifiable from observations or mild manipulations, because the expected effects are small relative to natural variability; stronger perturbations are therefore required to generate a diagnostic contrast. By strongly constraining development in the early-season, and by providing a robust cooling signal in the late-season, we sought to reveal the causal structure underlying the observed solstice-related reversal in temperature effects on autumn phenology.

Temperatures below 10°C intensively slow down cell division and mitotic rates, these rates then rapidly and non-linearly approach 0 as temperatures drop towards 0°C (Körner, 2021). As reflected in L152-158 of the revised manuscript, we selected a spring cooling regime of 2–7 °C to strongly slow developmental processes while maintaining a clear thermal safety margin that eliminates the risk of frost damage. Although a milder cooling regime (e.g. 5–10 °C) would be less extreme, it would also be expected to produce only a comparatively small reduction in developmental rates, thereby substantially reducing our ability to generate distinct early- and late-developing individuals and to detect carry-over effects on autumn phenology. Applying strong cooling therefore increases signal-to-noise and allows us to detect the underlying mechanism, which would not be possible with temperature treatments that represent average contemporary climatic variation.

The use of conditions out with the norm is a standard practice to elucidate mechanisms in ecology, where organisms are often pushed to their physiological limits or transplanted into environments fundamentally different to those which they are adapted (Somero, 2010; Berend et al., 2019). Experiments targeting autumn phenology have utilised a broad range of environmental conditions from moderate to extreme manipulations (Tanino et al., 2010). For example, to test the controls of growth cessation and dormancy induction in Prunus species, one study applied a range of treatments including constant 9°C temperature and 24 hour photoperiod between April and July (Heide, 2008).

Our experimental design aimed to reduce rates of development, cell division and maturation. In the Methods, we describe this aim and clearly state that the experimental design was not intended to mimic natural climatic variation (L154-156 & L181-186). Importantly, our conclusions are framed at the level of direction, timing, and interaction of effects, rather than the magnitude expected under contemporary or future field conditions (L360-363).

This framing intends to reflect the primary inference of this study, which concerns when and why temperature effects reverse around the solstice, and how this timing depends on developmental state and diel temperature exposure, rather than making quantitative predictions for present-day or future climates. This aligns our conclusions with the experimental design. We have further revised the Discussion to explain these aims and conclusions more clearly, including the addition of a subsection at the beginning titled “Experimental forcing and scope of inference” (L346-363). We have also set up this expectation in the Introduction (L113-115).

Additionally, we have improved the Discussion in a number of related aspects.

We explicitly separate mechanistic conclusions and any relation to natural systems, remaining cautious to not overgeneralise or overstate our findings (L417-419).

We now include a dedicated paragraph explaining that, although these specific conditions are not likely to be found in beech’s range, analogous developmental constraints can arise during cold springs, late cold spells following budburst, or at high-elevation and continental sites where temperatures remain low despite increasing photoperiod (L540-545, L583-588). We further explain that because developmental progression integrates temperature cumulatively over time, even short episodes of strong cooling can exert lasting carry-over effects on seasonal timing, thereby linking the forced experimental responses to processes relevant under natural, fluctuating conditions (L545-550).

We explicitly state that the decoupling of day and night temperatures was not intended to represent realistic meteorological states (L458-460). We explain that this design was used diagnostically to isolate inherently diel physiological processes (e.g. nocturnal growth, cell division and expansion versus daytime carbon assimilation), and that the observed responses demonstrate the importance of diel timing of temperature exposure rather than the realism of the imposed cycles (L460-468).

Previous response:

We recognise that our temperature treatments were severe and do not mimic real world scenarios. They were deliberately designed to create large contrasts in developmental rates, thereby maximising our ability to detect the mechanisms underpinning the solstice switch. For example, the severe cooling between 4 April and 24 May was specifically designed to slow spring development as much as possible without damaging the plants. We have added text in the Methods to clarify this aim.

I also think the control is confounded with growth chamber experience in Experiment 1. That is, the control plants never experience any time in a chamber, but all the treatments include significant time in a chamber. The authors mention how detrimental chamber time can be to saplings (indeed, they mention an aphid problem in experiment 2) so I think they need to be more upfront about this. The study is still very valuable, but -- again -- we may need to be more cautious in how much we infer from the results.

We appreciate the reviewer’s concern about the potential confounding effect of chamber exposure in experiment 1. We have now discussed this limitation more explicitly, adding further explanation to the Methods and Discussion.

Note that chamber-related problems (e.g. aphid infestations) primarily occurred under warm chamber conditions, whereas our experiment 1 cooling treatments maintained low temperatures that suppressed such issues. This means that an equivalent “warm chamber control” could have been associated with its own artefacts, as trees kept under warm chamber conditions would have been exposed to additional stressors that were not present under natural growing conditions. To address this point, we included a chamber control in experiment 2. While aphid abundance was indeed higher in the warm chamber controls, chamber exposure itself had no detectable effect on autumn phenology. This suggests that the main findings of experiment 1 are unlikely to be artefacts of chamber conditions.

Nevertheless, we agree that chamber exposure remains a potential limitation of experiment 1, which requires clear acknowledgement. We now state this more explicitly in the manuscript while also emphasising that our results are supported by experiment 2 and by converging lines of external evidence.

Also, I suggest the authors add a figure to explain their experiments as they are very hard to follow. Perhaps this could be added to Figure 1?

We have now added figures to the methods section to depict the experimental timelines and settings more clearly (Figs. 2 and 3).

Finally, given how much the authors extrapolate to carbon and forests, I would have liked to see some metrics related to carbon assimilation, versus just information on timing.

We agree that carbon assimilation is an important component of forest carbon dynamics. However, the primary aim of this study was to identify how developmental state and diel cycles mediate temperature effects on autumn phenology, rather than to quantify carbon assimilation per se. Assessing photosynthetic controls on autumn phenology would require a substantially different experimental design and is therefore beyond the scope of the present study.

That said, we were able to include measurements of photosynthetic assimilation during pre-solstice cooling (now presented as Fig. S12 for all treatments). These data show that cooling strongly reduced assimilation across all treatments, despite their markedly different phenological outcomes. This supports our interpretation that variation in assimilation alone cannot explain the observed phenological responses, consistent with previous manipulative and observational studies reporting a weak role of late-season assimilation in controlling autumn phenology.

Fagus sylvatica: Fagus sylvatica is an extremely important tree to European forests, but it also has outlier responses to photoperiod and other cues (and leafs out very late) so using just this species to then state 'our results likely are generalisable across temperate tree species' seems questionable at best.

We agree that Fagus sylvatica has a stronger photoperiod dependence than many other European tree species. As we note in our response to Reviewer 1, our findings align with previous research across temperate northern forests. Within our framework, interspecific variation in leaf-out timing would not alter the overall response pattern, though it could shift the specific timing of effect reversals. For example, earlier-leafing species may approach completion of development sooner and thus show sensitivity to late-season cooling earlier than F. sylvatica. Nevertheless, we acknowledge the importance of not overstating generality. We have therefore revised the manuscript to phrase conclusions more cautiously and highlight the need for further research across species.

And the referenced response to Reviewer one:

We agree that extrapolation from our experiments on Fagus sylvatica to other species and natural forests requires caution. However, it is precisely the controlled nature of our design that allowed us to isolate the precise mechanisms that appear to underpin the solstice switch, highlighting the role of diel and seasonal temperature variation. In natural systems, additional variables such as competition, precipitation, and soil heterogeneity can strongly influence phenology, but they also make it difficult to disentangle causal mechanisms. By minimising these confounding factors, our experiment provided a clear test of how temperature before and after the solstice regulates growth cessation.

To acknowledge the limitation, we have toned down statements about generalisation (e.g. “likely generalisable” to “other temperate tree species may display similarities”) and explicitly call for follow-up studies across species and forest contexts. At the same time, we highlight that our findings align with independent evidence from manipulative experiments, satellite observations, flux measurements, and groundbased phenology, which suggests the mechanisms we report may extend beyond the specific populations studied here.”

As described in responses above, we have further clarified what can be directly concluded from our study, avoiding overgeneralisation.

Measuring end of season (EOS): It's well known that different parts of plants shut down at different times and each metric of end of season -- budset, end of radial expansion, leaf coloring etc. -- relate to different things. Thus I was surprised that the authors ignore all this complexity and seem to equate leaf coloring with budset (which can happen MONTHS before leaf coloring often) and with other metrics. The paper needs a much better connection to the physiology of end of season and a better explanation for the focus on budset. Relatedly, I was surprised the authors cite almost none of the literature on budset, which generally suggests is it is heavily controlled by photoperiod and population-level differences in photoperiod cues, meaning results may different with a different population of plants. 

We thank the reviewer for pointing out that our discussion of the responses of different EOS metrics needs more clarity. We agree with much of this perspective, and we have added an additional analysis of leaf chlorophyll content data to use leaf discolouration as an alternative EOS marker. On this we would like to make two important points:

Firstly, we agree that bud set often occurs before leaf discolouration, although this can depend on which definition of leaf discolouration is used. In experiment 1, budset occurred on average on day-of-year (DOY) 262 and leaf senescence (50% loss of leaf chlorophyll) occurred on DOY 320. However, we do not necessarily agree that this excludes the combined discussion of bud set and leaf senescence timing. Whilst environmental drivers can affect parts of plants differently, often responses from different end-of-season indicators (e.g. bud set and loss of leaf chlorophyll) are similar, even if only directionally. Figure S11 shows how, across both experiments, treatment effects were tightly conserved (R² = 0.49) amongst the two phenometrics. In accordance with these revisions, we have updated the manuscript title to “Developmental constraints mediate the summer solstice reversal of climate effects on the autumn phenology of European beech”.

Secondly, shifts in bud set timing remain the primary focus of the manuscript as these shifts are of direct physiological relevance to plant development and dormancy induction, whereas leaf discolouration may simply follow bud set as a symptom of developmental completion. This is supported by our results, which show stronger responses of bud set than leaf senescence (Figs. 4 & 5 vs. Figs. S9 & S10).

Following the reviewer’s suggestion, we have included more references on the topic of bud set and its environmental controls. The reviewer rightly stresses that photoperiod is considered the most important factor. Photoperiod is therefore key in our conceptual model. However, the responses we observed in F. sylvatica cannot be explained by photoperiod alone. For example, in experiment 1, July cooling delayed the autumn phenology of late-leafing trees but had negligible impact on early-leafing trees, even though both experienced the exact same photoperiod. Moreover, in experiment 2, day, night and full-day cooling showed substantial variations in their effects despite equal photoperiod across the climate regimes. This is why we suggest that the annual progression of photoperiod modulates the responses to temperature variations instead of eliciting complete control.

Following the addition of an analysis of leaf senescence data, we also revised the terminology in places (including the title) from “primary growth cessation/bud set” to the broader term “autumn phenology.” This term is intended to encompass two distinct but related physiological processes—bud set and leaf senescence—both of which are commonly used as markers of autumn phenology and the end of the growing season.

Somewhat minor comments:

(1) How can a bud type -- which is apical or lateral -- be a random effect? The model needs to try to estimate a variance for each random effect so doing this for n=2 is quite odd to me. I think the authors should also report the results with bud type as fixed, or report the bud types separately.

We have revised the analysis to include bud type as a fixed effect. There are only very minor numerical adjustments (e.g. rounding to 4.8 days instead of 4.9) and inferences are not altered. We also report the bud type effects for experiment 1 and experiment 2.

(2) I didn't fully see how the authors results support the Solstice as Switch hypothesis, since what timing mattered seemed to depend on the timing of treatment and was not clearly related to solstice. Could it be that these results suggest the Solstice as Switch hypothesis is actually not well supported (e.g., line 135) and instead suggest that the pattern of climate in the summer months affects end of season timing?

Our responses to the main comments in this new round of revision have comprehensively covered this topic.

References

Berend K, Haynes K, MacKenzie CM. 2019. Common garden experiments as a dynamic tool for ecological studies of alpine plants and communities in northeastern North America. Rhodora 121: 174.

Heide OM. 2008. Interaction of photoperiod and temperature in the control of growth and dormancy of Prunus species. Scientia Horticulturae 115: 309–314.

Körner C. 2021. Alpine Plant Life: Functional Plant Ecology of High Mountain Ecosystems. Cham: Springer International Publishing.

Somero GN. 2010. The physiology of climate change: how potentials for acclimatization and genetic adaptation will determine ‘winners’ and ‘losers’. Journal of Experimental Biology 213: 912–920.

Tanino KK, Kalcsits L, Silim S, Kendall E, Gray GR. 2010. Temperature-driven plasticity in growth cessation and dormancy development in deciduous woody plants: a working hypothesis suggesting how molecular and cellular function is affected by temperature during dormancy induction. Plant Molecular Biology 73: 49–65.

eLife Assessment

This important study combined careful computational modeling, a large patient sample, and replication in an independent general population sample to provide convincing evidence in support of a computational account of a difference in risk-taking between people who have attempted suicide and those who have not. It is proposed that this difference reflects a general change in the approach to risky (high-reward) options and a lower emotional response to certain rewards. While the findings advance our understanding of cognitive mechanisms at the group level, the observation that computational phenotype is predictive of suicidal behavior only in the clinical sample and not in the online sample limits its applicability for individual prediction, early detection and prevention of suicidality.

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in a general online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents diagnosed with depression or anxiety with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide) regardless of the potential losses. However, such a result was only found in the clinical sample and cannot be generalized more broadly based on the current findings.

Strengths:

(1) The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

(2) Sampling of adolescents at high risk can help target early preventative diagnoses and treatments for suicide.

(3) Replication of the results in an online cohort increases confidence in the findings.

(4) The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

(5) Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

(1) Sample size of 25 for S- group is low-powered, which is explicitly mentioned as a study limitation.

(2) Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. Thus, the implications of this work are more relevant to a basic-science understanding of the etiology of suicidal behavior than they are useful as a predictor of suicidal behavior, and it is not clear that a psychiatrist or psychologist could use this task to potentially determine who is at higher risk of attempting suicide and must be more closely monitored. Indeed, relationships between task parameters and behavior and suicidal behavior was limited to the clinical sample with a diagnosis of depression or anxiety disorder, and did not extend to the online sample. Therefore, the claim that these findings provide "computational markers for general suicidal tendency among adolescents" is unwarranted.

Reviewer #2 (Public review):

Summary:

This article addresses a very pertinent question - what are the computational mechanisms underlying risky behaviour in patients having attempted suicide. In particular, it is impressive how the authors find a broad behavioral effect whose mechanisms they can then explain and refine through computational modeling. This work is important because currently, beyond previous suicide attempts, there has been a lack of predictive measures. This study is the first step towards that: understanding the cognition on a group level. Before then being able to include it in future predictive studies (based on the cross-sectional data, this study by itself cannot assess the predictive validity of the measure).

Strengths:

- Large sample size<br /> - Replication of their own findings<br /> - Well-controlled task with measures of behaviour and mood + precise and well-validated computational modeling

Questions, based on revised manuscript and replies to other reviewers:

(1) Replies to reviewers in general: Bayes Factors have been added, it would be good to also use common verbal terms to describe them (e.g. 'anecdotal', 'moderate' etc). For example, my reading of table S8 would be that for gambling rate there is only anecdotal evidence that it does not relate to PSWQ, BDI, and moderate evidence it does not relate to TAI.

(2) Reply to reviewer 1 Q2 (Predicting STB):<br /> For the regression predicting suicidal ideation, it seems to me that what you did was a regression STB ~ gambling behaviour + approach + mood? Could you clarify? I had expected as a test of whether the task can predict STB risk something slightly different - a cross-validation (LOO or maybe 5-fold in the large sample): STB ~ gambling behaviour + approach [parameter from model] + mood [parameter from model]; and then computing in the left out participants: predicted STB. Then checking correlation between STB and predicted STB. This would allow testing whether the diverse task measures together predict STB (with the caveat, that it's cross-validated, rather than hold-out sample, unless you could train on one sample (in lab) and test on the other (online).

(3) Reply to reviewer 2 Q1 (parameter recovery): I'm looking at S3, it seems to still show only the scatter plots and not the correlation matrices, which are now added as text notes. Can you actually show these matrices? An off-diagonal correlation of 0.63 appears quite high. I think it needs to be discussed exactly which parameters those are, and whether that impacts the interpretation of the results.

(4) Reply to reviewer 3 Q3 (mood model): I would have imagined that the response would involve changing the mood equations (equation 8 main text) to include a term for whether the participant gambled or not, independent of the gamble value.

Reviewer #3 (Public review):

This manuscript investigates computational mechanisms underlying increased risk-taking behavior in adolescent patients with suicidal thoughts and behaviors. Using a well-established gambling task that incorporates momentary mood ratings and previously established computational modeling approaches, the authors identify particular aspects of choice behavior (which they term approach bias) and mood responsivity (to certain rewards) that differ as a function of suicidality. The authors replicate their findings on both clinical and large-scale non-clinical samples.

The main problem, however, is that the results do not seem to support a specific conclusion with regard to suicidality. The S+ and S- groups differ substantially in the severity of symptoms, as can be seen by all symptom questionnaires and the baseline and mean mood, where S- is closer to HC than it is to S+. The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence. Therefore, the results do not adequately deconfound suicidality from general symptom severity.

The second main issue is that the relationship between an increased approach bias and decreased mood response to CR is conceptually unclear. In this respect, it would be natural to test whether mood responses influence subsequent gambling choices. This could be done either within the model by having mood moderate the approach bias or outside the model using model-agnostic analyses.

Additionally, there is a conceptual inconsistency between the choice and mood findings that partly results from the analytic strategy. The approach bias is implemented in choice as a categorical value-independent effect, whereas the mood responses always scale linearly with the magnitude of outcomes. One way to make the models more conceptually related would be to include a categorical value-independent mood response to choosing to gamble/not to gamble.

The manuscript requires editing to improve clarity and precision. The use of terms such as "mood" and "approach motivation" is often inaccurate or not sufficiently specific. There are also many grammatical errors throughout the text.

Claims of clinical relevance should be toned down, given that the findings are based on noisy parameter estimates whose clinical utility for the treatment of an individual patient is doubtful at best.

Comments on revisions:'

The authors adequately addressed my comments and I find the manuscript substantially strengthened.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This valuable study combined careful computational modeling, a large patient sample, and replication in an independent general population sample to provide a computational account of a difference in risk-taking between people who have attempted suicide and those who have not. It is proposed that this difference reflects a general change in the approach to risky (high-reward) options and a lower emotional response to certain rewards. Evidence for the specificity of the effect to suicide, however, is incomplete, which would require additional analyses.

We thank the editors and reviewers for this important assessment. Based on clinical interviews, we included patients with and without suicidality (S⁺ and S^- groups). However, in line with suicidal-related literature (e.g., Tsypes et al., 2024), two groups also differed substantially in the severity of symptoms (see Table 1). To address the request for evidence on specificity to suicidality beyond general symptom severity, we performed separate linear regressions to explain in gambling behaviour, value-insensitive approach parameter (β_gain), and mood sensitivity to certain rewards (β_CR) with group as a predictor (1 for S⁺ group and 0 for S^- group) and scores for anxiety and depression as covariates. Results remained significant after controlling anxiety and depression (ps < 0.027; Table S8). Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) on the clinical questionnaire to extract the orthogonal components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. We then performed linear regressions using these components as covariates to control for anxiety and depression. Our main results remained significant (ps < 0.027; Table S9). We believe that these analyses provide evidence that the main effects on gambling and on mood were specific to suicide.

Moreover, as Reviewer 3 pointed out, these “absence of evidence” cannot provide insights of “evidence of absence”. Although we median-split patients by the scores of general symptoms (e.g., depression and anxiety-related questionnaires) and verified no significant differences in these severities (Figure S11), we additionally conducted Bayesian statistics in gambling behavior, value-insensitive approach parameter, and mood sensitivity to certain rewards. BF₀₁ is a Bayes factor comparing the null model (M₀) to the alternative model (M₁), where M₀ assumes no group difference. BF₀₁ > 1 indicates that evidence favors M₀. As can be seen in Table S7, most results supported null hypothesis, suggesting that general symptoms of anxiety and depression overall did not influence our main results. Overall, we believe that these analyses provide compelling evidence for the specificity of the effect to suicide, above and beyond depression and anxiety.

Beyond these specific findings, this work highlights the broader utility of computational modelling and mood to better understand behavioral effect, showing how to use both mood and choice data to better comprehend a psychiatric issue. 

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in an undifferentiated online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide), regardless of the potential losses.

Strengths:

(1) The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

(2) Sampling choice is optimal, with adolescents at high risk; an ideal cohort to target early preventative diagnoses and treatments for suicide.

(3) Replication of the results in an online cohort increases confidence in the findings.

(4) The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

(5) Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

(1) The sample size of 25 for the S- group was justified based on previous studies (lines 181-183); however, all three papers cited mention that their sample was low powered as a study limitation.

We thank the Reviewer for rising this concern. We agree that the sample size for S^- group (n=25) is modest, and the prior studies we cited also acknowledged limited power. We wanted to point out that we obtained a comparable sample size to a prior study. In the revision, we therefore updated the section to justify this sample size in which we acknowledge the limited power of our study in the limitation section. Please see our clarification below:

Page 32:

“Third, despite replicating our main results in an independent dataset (n=747), the modest S^- subgroup size (n=25) has a limited statistical power.”

(2) Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. However, the prediction of clinical interest is of suicidal behaviors from task parameters/behavior - as a psychiatrist or psychologist, I would want to use this task to potentially determine who is at higher risk of attempting suicide and therefore needs to be more closely watched rather than the other way around (predicting behavior in the task from their symptom profile). Unfortunately, the analyses presented do not show that this prediction can be made using the current task. I was left wondering: is there a correlation between beta_gain and STB? It is also important to test for the same relationships between task parameters and behavior in the healthy control group, or to clarify that the recommendations for potential clinical relevance of these findings apply exclusively to people with a diagnosis of depression or anxiety disorder. Indeed, in line 672, the authors claim their results provide "computational markers for general suicidal tendency among adolescents", but this was not shown here, as there were no models predicting STB within patient groups or across patients and healthy controls.

Thank you for these thoughtful comments. Our study focuses on why adolescent patients with suicidality have increased risk behavior, aiming to provide a mechanism-based target for suicide prevention. Therefore, our dependent variable in the mediation model was gambling behavior. We also agree that the clinically relevant question is whether suicidality can be predicted from task-derived behavior/parameters. We thus used risky behavior and the potential mental parameters to predict STB. Linear regressions showed that gambling behavior, as well as the value-insensitive approach parameter, can predict suicidal symptom scores among patients (former: β = 9.189, t = 2.004, p = 0.048; latter: β = 5.587, t = 2.890, p = 0.005). In healthy controls, these predictions failed (gambling behavior: β = 1.471, t = 0.825, p = 0.411; approach: β = 0.874, t = 1.178, p = 0.241). These results suggest that clinical relevance of these findings apply exclusively to people with a diagnosis of depression or anxiety disorder. We found same patterns for the mood parameter (mood sensitivity to certain rewards: patients: β = -28.706, t = -2.801, p = 0.006; healthy controls: β = -2.204, t = -0.528, p = 0.599). In sum, we believe that our statement of “computational markers for general suicidal tendency among adolescents” is reasonable now. Please see our revisions below:

Page 17:

“Furthermore, linear regression showed that gambling rate can predict the current suicidal ideation score (BSI-C, β = 9.189, t = 2.004, p = 0.048) among patients, but not among HC (β = 1.471, t = 0.825, p = 0.411), suggesting that gambling behavior has patient-specific predictive utility for suicidal symptoms.”

Page 19:

“Furthermore, linear regression showed that approach parameter can predict the current suicidal ideation score (β = 5.587, t = 2.890, p = 0.005) among patients, but not among HC (β = 0.874, t = 1.178, p = 0.241), suggesting that value-insensitive approach parameter has patient-specific predictive utility for suicidal symptoms.”

Page 21:

“Furthermore, linear regression showed that mood sensitivity to CR can predict the current suicidal ideation score (β = -28.706, t = -2.801, p = 0.006) among patients, but not among HC (β = -2.204, t = 0.528, p = 0.599), suggesting that mood sensitivity to CR has patient-specific predictive utility for suicidal symptoms.”

(3) The FDR correction for multiple comparisons mentioned briefly in lines 536-538 was not clear. Which analyses were included in the FDR correction? In particular, did the correlations between gambling rate and BSI-C/BSI-W survive such correction? Were there other correlations tested here (e.g., with the TAI score or ERQ-R and ERQ-S) that should be corrected for? Did the mediation model survive FDR correction? Was there a correction for other mediation models (e.g., with BSI-W as a predictor), or was this specific model hypothesized and pre-registered, and therefore no other models were considered? Did the differences in beta_gain across groups survive FDR when including comparisons of all other parameters across groups? Because the results were replicated in the online dataset, it is ok if they did not survive FDR in the patient dataset, but it is important to be clear about this in presenting the findings in the patient dataset.

Thank you for raising the important issue of multiple testing and for asking us to clarify exactly which tests were covered by the FDR procedure. In the clinical dataset we conducted a large number of inferential tests (χ², t-tests, ANOVAs, regressions) spanning: (i) group differences in demographic/clinical characteristics; (ii) sanity checks (e.g., anxiety/depression questionnaires); (iii) primary hypotheses (e.g., group differences in risky behavior); (iv) model-based analyses (parameter checks and between-group contrasts); and (v) control/sensitivity analyses. Post-hoc t-tests were performed only when the three-group ANOVA was significant. This yielded >150 p-values. FDR was applied using all these p-values. Please see our clarification below:

Supplementary Page 4:

“Supplementary Note 8: Clarification for FDR correction.

In the clinical dataset we conducted a large number of inferential tests (χ<sup2\</sup>, t-tests, ANOVAs, regressions) spanning: (i) group differences in demographic/clinical characteristics; (ii) sanity checks (e.g., anxiety/depression questionnaires); (iii) primary hypotheses (e.g., group differences in risky behavior); (iv) model-based analyses (parameter checks and between-group contrasts); and (v) control/sensitivity analyses. Post-hoc t-tests were performed only when the three-group ANOVA was significant. This yielded >150 p-values. FDR was applied using all these p-values.”

(4) There is a lack of explicit mention when replication analyses differ from the analyses in the patient sample. For instance, the mediation model is different in the two samples: in the patient sample, it is only tested in S+ and S- groups, but not in healthy controls, and the model relates a dimensional measure of suicidal symptoms to gambling in the task, whereas in the online sample, the model includes all participants (including those who are presumably equivalent to healthy controls) and the predictor is a binary measure of S+ versus S- rather than the response to item 9 in the BDI. Indeed, some results did not replicate at all and this needs to be emphasized more as the lack of replication can be interpreted not only as "the link between mood sensitivity to CR and gambling behavior may be specifically observable in suicidal patients" (lines 582-585) - it may also be that this link is not truly there, and without a replication it needs to be interpreted with caution.

Thank you for these important comments. This study focused on cognitive and affective computational mechanisms underlying increased risky behavior in STB. Accordingly, we compared patients with STB (S⁺) with patients without STB (S^-) and healthy controls (HC) to examine the effects of STB on risky behavior. Therefore, group comparison, instead of dimensional measure of suicidal symptoms by Beck Scale for Suicidal Ideation, can answer our research questions directly.

To enhance consistency between the clinical and replication datasets, we included all participants in each dataset when performing the mediation analysis. Given that S^- and HC did not differ in gambling behavior or the approach parameter in the clinical dataset, we merged these two groups. In the replication dataset, to mirror the S⁺ vs. S^- contrast used clinically, we categorized the general sample into S+ and S^- based on BDI item 9. The mediation results remained significant in both datasets (the clinical dataset: a×b = 0.321, 95% CI = [0.070, 0.549], p = 0.016; the replication dataset: a×b = 0.143, 95% CI = [0.016, 0.288], p = 0.031), suggesting that STB is associated with increased risk behavior via stronger approach motivation.

We also acknowledge the non-replication of the correlation between gambling behavior and mood sensitivity to certain rewards in the online sample. While this pattern might indicate that the link is specific to suicidal patients, it may also reflect sample-specific or unstable effects; thus, we now state this explicitly and interpret the finding with caution. Please see our revisions below:

Page 15:

“We next verified our results in an independent dataset, including the same task and BDI questionnaire in 747 general participants (500 females; age: 20.90±2.41) (46). One item in BDI involves the measurement of STB. In item 9 of BDI, participants chose one option that describes them best: Option 1, “I don't have any thoughts of killing myself.”; Option 2, “I have thoughts of killing myself, but I would not carry them out.”; Option 3, “I would like to kill myself.”; Option 4, “I would kill myself if I had the chance.”. In line with the current definition of S⁺/S^- in the clinical dataset, we identified S⁺ group as choosing Option 2, 3, or 4, while participants selecting Option 1 were categorized as S^- group.”

Page 19:

“Given significant correlations between group, approach parameter, and gambling rate for gain trials (ps < 0.017), we further conducted a mediation analysis with the assumption of the mediating effect of approach motivation of suicidality on the risk behavior. Given that we aimed to test the effect of STB, with S^- and HC as controls, and given that S^- and HC did not differ in gambling behavior or in the approach parameter, we merged these two groups for the mediation analysis. Results supported our hypothesis (a×b = 0.321, 95% CI = [0.070, 0.549], p = 0.016; Figure 2C), confirming that suicidal thoughts and behavior increase risk behavior through stronger approach motivation.”

Page 26:

“However, we did not observe any significant correlation between mood sensitivity to CR and gambling behavior (ps > 0.389), which suggests that the link between mood sensitivity to CR and gambling behavior may be specifically observable in suicidal patients. Alternatively, this non-replicated result may also reflect sample-specific or unstable effects, which needs to be interpreted with caution.”

(5) In interpreting their results, the authors use terms such as "motivation" (line 594) or "risk attitude" (line 606) that are not clear. In particular, how was risk attitude operationalized in this task? Is a bias for risky rewards not indicative of risk attitude? I ask because the claim is that "we did not observe a difference in risk attitude per se between STB and controls". However, it seems that participants with STB chose the risky option more often, so why is there no difference in risk attitude between the groups?

Thank you for pointing out the ambiguity. In our manuscript, “motivation” and “risk attitude” are defined at the computational level. Following prior work with this task Rutledge et al., (2015, 2016), we decompose observed gambling into (i) value-dependent valuation parameters that capture risk attitude (e.g., risk aversion and loss aversion, which scale the subjective value of outcomes), and (ii) value-insensitive, valence-dependent biases that capture approach/avoidance motivation. Accordingly, a higher gambling rate does not imply a change in risk attitude per se: it can arise from an increased value-insensitive approach bias even when risk-attitude parameters are comparable between groups—which is what we observe for S⁺ vs. controls. We have clarified this point in the computational modeling section.

Pages 12-13:

“Please note that a higher gambling rate does not imply a change in risk attitude per se: it can arise from an increased value-insensitive approach bias even when risk-attitude parameters are comparable between groups. Risk attitude is indeed conceptualized in economics as the curvature of the utility function (i.e., the subjective value) of the objective outcomes, with concave curves associated with risk aversion, and convex curves associated with risk seeking (54,56). By contrast, the approach or avoidance bias apply to all the value. A possible interpretation of the approach bias is that participant approach the option with the highest possible gain (the lottery) in the gain frame; the avoidance bias would then reflect a tendency to systematically avoid the highest potential losses (the lottery) in the loss frame.”

Reviewer #2 (Public review):

Summary:

This article addresses a very pertinent question: what are the computational mechanisms underlying risky behaviour in patients who have attempted suicide? In particular, it is impressive how the authors find a broad behavioural effect whose mechanisms they can then explain and refine through computational modeling. This work is important because, currently, beyond previous suicide attempts, there has been a lack of predictive measures. This study is the first step towards that: understanding the cognition on a group level. This is before being able to include it in future predictive studies (based on the cross-sectional data, this study by itself cannot assess the predictive validity of the measure).

Strengths:

(1) Large sample size.

(2) Replication of their own findings.

(3) Well-controlled task with measures of behaviour and mood + precise and well-validated computational modeling.

Weaknesses:

I can't really see any major weakness, but I have a few questions:

(1) I can see from the parameter recovery that the parameters are very well identified. Is it surprising that this is the case, given how many parameters there are for 90 trials? Could the authors show cross-correlations? I.e., make a correlation matrix with all real parameters and all fitted parameters to show that not only the diagonal (i.e., same data is the scatter plots in S3) are high, but that the off-diagonals are low.

Thank you for raising these thoughtful concerns. The current task consisted of 90 choices and 36 mood ratings. There were 5 choice parameters and 4 mood parameters. The apparently strong identifiability is not unexpected, as 90 choice trials and 36 mood ratings are comparable to those in prior computational modeling literature (Blain & Rutledge, 2022).

As suggested, we computed cross-correlations between all generating (“true”) and recovered (“fitted”) parameters. The resulting matrix showed high diagonal (choice winning model: rs > 0.91; mood winning model: rs > 0.90) and low off-diagonal (choice winning model: abs(rs) < 0.63; mood winning model: abs(rs) > 0.40) correlations, further supporting parameter recovery. Please see our clarifications below:

Supplementary Pages 2-3:

“Parameter recovery: Figure S3 shows good parameter recovery for both choice and mood winning model (choice: rs > 0.91, ps < 0.001; intraclass coefficients > 0.78; mood: rs > 0.90, ps < 0.001; intraclass coefficients > 0.86). Moreover, we computed cross-correlations between all generating (“true”) and recovered (“fitted”) parameters. The resulting matrix showed high diagonal (choice winning model: rs > 0.91; mood winning model: rs > 0.90) and low off-diagonal (choice winning model: abs(rs) < 0.63; mood winning model: abs(rs) > 0.40) correlations, further supporting parameter recovery.”

Page 10：

“The numbers of choice trials and mood ratings were comparable to those in prior computational modeling studies (34,35).”

(2) Could the authors clarify the result in Figure 2B of a correlation between gambling rate and suicidal ideation score, is that a different result than they had before with the group main effect? I.e., is your analysis like this: gambling rate ~ suicide ideation + group assignment? (or a partial correlation)? I'm asking because BSI-C is also different between the groups. [same comment for later analyses, e.g. on approach parameter].

Thank you for pointing out the lack of clarity. We performed group difference analysis and correlation of suicidal ideation analysis, separately. We first performed group difference analysis to test our hypothesis of STB effects. We then conducted correlational analysis to further specify our findings.

(3) The authors correlate the impact of certain rewards on mood with the % gambling variable. Could there not be a more direct analysis by including mood directly in the choice model?

Thank you for this insightful suggestion. As suggested, we tried to integrate mood into choice models by adding mood bias component(s) in line with previous literature (Vinckier et al., 2018). The first model (mcM1) assumes that mood biases choice, building on cM3 (the winning choice model). cmM2 further separated the mood bias parameter into two components according to participants’ choices.

However, model comparison using BIC supported cM3 (Table S6), that is, without consideration of mood in choice modeling. This can be due to the lack of block design in our experimental design unlike e.g., Vinckier et al., (2018) and Eldar & Niv, (2015). Please see our clarifications below:

Supplementary Pages 3-4:

“Supplementary Note 6: integration of mood into choice models

Although we modeled choice and mood separately to examine cognitive and affective mechanisms underlying increased risk behavior in adolescent suicidal patients, one interesting question was whether mood responses influence subsequent gambling choices and how to model them. First, we median-split mood responses (except the final rating) to compare gambling rate. Results showed a trend for less gambling rate in higher mood (t = -1.971, p = 0.050). However, there was no significant group difference (F = 0.680, p = 0.507). Second, with the assumption that mood biases choice, we constructed mcM1 based on cM3 (the winning choice model).

Based on our finding of the negative correlation between mood sensitivity to certain rewards and gambling rate in S⁺, we separated β_Mood parameter into β_Mood-CR and β_Mood-GR (cmM2).

Model comparison using BIC supported cM3 (Table S6), that is, without consideration of mood in choice modeling. The mood bias parameters in neither cM2 nor cM3 reached significance (ps > 0.091), which may be due to the absence of a blocked design in our experiment, unlike in Vinckier et al. (2018) and Eldar and Niv (2015).”

(4) In the large online sample, you split all participants into S+ and S-. I would have imagined that instead, you would do analyses that control for other clinical traits. Or, for example, you have in the S- group only participants who also have high depression scores, but low suicide items.

Thank you for this insightful suggestion. Following prior suicide-related literature (Tsypes et al., 2024), we controlled for depression by including them as covariates. Note that depression scores were derived from our established bifactor model (Wang et al., 2025), which decomposed depression from the anxiety. These results remained largely significant (ps ≤ 0.050), except a marginally significant effect of group on gambling behavior (p = 0.059). Despite a trend, this effect with covariates of depression-related questionnaires is strong in our clinical cohort (p = 0.024; Table S8). This suggests that the link between suicidality and risky behavior persists above and beyond general depressive symptoms.

Please see our clarifications below:

Page 26:

“After controlling for depression severity using our established bifactor model (see ref 60 for details), these results remained significant (ps ≤ 0.050), except a marginally significant effect of group on gambling behavior (p = 0.059). Despite a trend, this effect with covariates of depression-related questionnaires is strong in our clinical cohort (p = 0.024; Table S8). This suggests that the link between suicidality and risky behavior persists above and beyond general depressive symptoms.”

Reviewer #3 (Public review):

This manuscript investigates computational mechanisms underlying increased risk-taking behavior in adolescent patients with suicidal thoughts and behaviors. Using a well-established gambling task that incorporates momentary mood ratings and previously established computational modeling approaches, the authors identify particular aspects of choice behavior (which they term approach bias) and mood responsivity (to certain rewards) that differ as a function of suicidality. The authors replicate their findings on both clinical and large-scale non-clinical samples.

(1) The main problem, however, is that the results do not seem to support a specific conclusion with regard to suicidality. The S+ and S- groups differ substantially in the severity of symptoms, as can be seen by all symptom questionnaires and the baseline and mean mood, where S- is closer to HC than it is to S+. The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence. Therefore, the results do not adequately deconfound suicidality from general symptom severity.

Thank you for this important comment. Based on clinical interviews, we included patients with and without suicidality (S⁺ and S^- groups). However, in line with suicidal-related literature (e.g., Tsypes et al., 2024), two groups also differed substantially in the severity of symptoms (see Table 1). To address the request for evidence on specificity to suicidality beyond general symptom severity, we performed separate linear regressions to explain in gambling behaviour, value-insensitive approach parameter (β_gain), and mood sensitivity to certain rewards (β_CR) with group as a predictor (1 for S⁺ group and 0 for S^- group) and scores for anxiety and depression as covariates. Results remained significant after controlling anxiety and depression (ps < 0.027; Table S8). Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) on the clinical questionnaire to extract the orthogonal components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. We then performed linear regressions using these components as covariates to control for anxiety and depression. Our main results remained significant (ps < 0.027; Table S9). We believe that these analyses provide evidence that the main effects on gambling and on mood were specific to suicide.

As pointed out, these “absence of evidence” cannot provide insights of “evidence of absence”. Although we median-split patients by the scores of general symptoms (e.g., depression and anxiety-related questionnaires) and verified no significant differences in these severities (Figure S11), we additionally conducted Bayesian statistics in gambling behavior, value-insensitive approach parameter, and mood sensitivity to certain rewards. BF₀₁ is a Bayes factor comparing the null model (M₀) to the alternative model (M₁), where M₀ assumes no group difference. BF₀₁ > 1 indicates that evidence favors M₀. As can be seen in Table S7, most results supported null hypothesis, suggesting that general symptoms of anxiety and depression overall did not influence our main results. Overall, we believe that these analyses provide compelling evidence for the specificity of the effect to suicide, above and beyond depression and anxiety.

Please see our revisions below:

Page 17:

“Within patients, this group effect on gambling rate remained significant after controlling for sex, illness duration, family history, diagnosis, and various medications use (ps < 0.05), as well as general symptoms (e.g., depression and anxiety; p = 0.024; also see Figure S11, Table S7 and Table S8). Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) to extract main components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. To further control for anxiety and depression, linear regression using these components as covariates revealed that the group effect on gambling rate remained significant (p = 0.024; Table S9).”

Pages 18-19:

“Within patients, this group effect on the approach parameter remained significant after controlling for sex, illness duration, family history, diagnosis, and various medications use (ps < 0.05), as well as general symptoms (e.g., depression and anxiety; p = 0.027; also see Figure S11, Table S7 and Table S8). Linear regression using PCA components as covariates revealed that the group effect on approach parameter remained significant (p = 0.027; Table S9).”

Page 21:

“Within patients, this group effect on βCR remained significant after controlling for gambling rate, earnings, mood-related outcome effect, mood drift effect, sex, illness duration, family history, diagnosis, and various medications use (ps < 0.032), as well as general symptoms (e.g., depression and anxiety; p = 0.001; also see Figure S11, Table S7 and Table S8). Linear regression using PCA components as covariates revealed that the group effect on this mood parameter remained significant (p = 0.001; Table S9).”

(2) The second main issue is that the relationship between an increased approach bias and decreased mood response to CR is conceptually unclear. In this respect, it would be natural to test whether mood responses influence subsequent gambling choices. This could be done either within the model by having mood moderate the approach bias or outside the model using model-agnostic analyses.

Thank you for this important suggestion. As suggested, one interesting question was whether mood responses influence subsequent gambling choices and how to model them. First, we median-split mood responses (except the final rating) to compare gambling rate. Results showed a trend for less gambling rate in higher mood (t = -1.971, p = 0.050). However, there was no significant group difference (F = 0.680, p = 0.507). Second, with the assumption that mood biases choice, we constructed mcM1 based on cM3 (the winning choice model). Based on our finding of the negative correlation between mood sensitivity to certain rewards and gambling rate in S⁺, we separated β_Mood parameter into β_Mood-CR and β_Mood-GR (cmM2). Model comparison using BIC supported cM3 (Table S6), that is, without consideration of mood in choice modeling. This can be due to the lack of block design in our experimental design unlike e.g., Vinckier et al., (2018) and Eldar & Niv, (2015). Please see Supplementary Pages 3-4:

(3) Additionally, there is a conceptual inconsistency between the choice and mood findings that partly results from the analytic strategy. The approach bias is implemented in choice as a categorical value-independent effect, whereas the mood responses always scale linearly with the magnitude of outcomes. One way to make the models more conceptually related would be to include a categorical value-independent mood response to choosing to gamble/not to gamble.

We apologise for the unclear statement. The approach bias is implemented in choice as a continuous value-independent effect, ranging from -1 to 1.

It was true that the mood responses always scale with the magnitude of outcomes, since mood ratings were request after the outcomes. Therefore, mood parameters and the approach bias were both continuous.

We also attempted to integrate mood into choice modelling. See Response 2 for Reviewer 3 for details.

(4) The manuscript requires editing to improve clarity and precision. The use of terms such as "mood" and "approach motivation" is often inaccurate or not sufficiently specific. There are also many grammatical errors throughout the text.

Thank you for this important suggestion. We have now explained motivation and mood in the Introduction section and the computational modeling section. Please see our clarifications below:

Pages 3-4:

“A growing literature indeed shows that risky behavior can be far better explained after adding value-insensitive approach and avoidance components to prospect theory(18,19), that is by including a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference. This class of models highlights the important role of value-insensitive motivational components in decision making in addition to risk attitude-driven valuation (e.g., loss/risk aversion)(20).”

Page 5:

“Although mood is thought to persist for hours, days, or even weeks(30-33), momentary mood, measured over the timescale in the laboratory setting, represents the accumulation of the impact of multiple events at the scale of minutes(30,32,34-38). Momentary mood external validity is demonstrated e.g., through its association with depression symptoms(37). Mood is different from emotions, which reflect immediate affective reactivity and is more transient (e.g., from surprise to fear)(31-33,39).”

We have corrected grammatical errors throughout the manuscript.

5) Claims of clinical relevance should be toned down, given that the findings are based on noisy parameter estimates whose clinical utility for the treatment of an individual patient is doubtful at best.

Thank you for this comment. We agree that we did not evaluate the noise in our estimate e.g., by assessing the test-retest reliability on the task parameters, which is outside the scope of the study, and it is indeed possible that parameter estimate is somehow noisy. Therefore, we tone down the clinical relevance of our results. Please see our revision below:

Page 32:

“Next, we did not evaluate the noise in our estimate e.g., by assessing the test-retest reliability on the task parameters and it is indeed possible that parameter estimate is somehow noisy.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Title: I believe "aberrant mood dynamics" is both too general and overstating the results of this study, which did not measure mood dynamics longitudinally. "Aberrant" is also overly pathologizing. I would suggest sticking more directly to the results, for instance, "Insensitivity of momentary mood to non-risky rewards in adolescent suicidal patients".

Thank you for this suggestion. We have now corrected it.

(2) Abstract: in line 61, "Our study uncovers the cognitive and affective mechanisms" suggests that these are the only ones, and you uncovered them. Of course, there could be more mechanisms contributing to risk behavior in STB, so I would suggest removing the word "the" or adding "one of the".

Thank you for this suggestion. We have now corrected it.

(3) One major weakness of this study is that suicidal thoughts and behaviors were not assessed via a clinical instrument such as the Columbia Suicide Severity Rating Scale - this should be mentioned upfront.

Thank you for this comment. According to medical records and information from family and friends by the researcher and psychiatrists, patients with suicidal thoughts and behaviors were categorized as suicidal group (S⁺), while patients without suicidal thoughts and behaviors were identified as control group (S^-). Note that medical records and information were recorded from clinical interviews where the psychiatrists were vigilant for signs of suicidal ideation and inquired about suicidal-related thoughts and behaviors from both the patients and their families. Therefore, the current group operation was possibly comparable to Columbia Suicide Severity Rating Scale.

(4) Table 1: female/male are sex, not gender (gender is man/woman/transgender/non-binary).

Thank you for this suggestion. We have now corrected it.

(5) Equation 1: It would be good to clarify what happens in gain-only or loss-only trials (the other value is then 0, but this can be clarified as it is not technically a loss or a gain).

Thank you for this suggestion. We have now corrected it. Please see below for our revision:

Page 12:

“Please note that V_gain is 0 in gain trials and V_loss is 0 in loss trials.”

(6) Figure 1E: The model prediction is not informative here. Given the linear regression model, there is no other option except that the mean prediction would overlap with the mean empirical measurement (unless the model was specified incorrectly). The same is true in Figure 2A.

Thank you for this suggestion. We have now removed plots for model prediction.

(7) Figure 1G: There was no analysis of the differences between groups in terms of earnings, given that the ANOVA was not significant. Still, if the claim is that risky behavior is sometimes suboptimal in this task, it would be good to show that there is a correlation between, say, symptoms of STB across groups and 1) risky behavior and 2) earnings.

Thank you for this insightful comment. In the patient cohort, risky behavior (gambling rate)—but not earnings—predicted the current suicidal ideation score (BSI-C, β = 9.189, t = 2.004, p = 0.048; earnings, β = 0.001, t = 0.582, p = 0.562). The lack of association for earnings is consistent with the task design, in which there is no stable optimal policy and payouts are only a coarse proxy for decision quality. Future work in learning paradigms, where optimality is well defined, may be better suited to test earnings-based links to STB. We have clarified this point below:

Page 32:

“Second, although we assumed that increased risky behavior in STB was suboptimal, the current task was not suited to test this, given the task design of random feedback for gambling option. Future work in learning paradigms, where optimality is well defined, may be better suited to test earnings-based links to STB.”

(8) Line 290: "beta_gain: -1-1" is unclear. I believe you meant beta_gain \in [-1,1].

Thank you for this suggestion. We have now corrected it to make it clear.

(9) The gain and loss biases are modeled as minimum and maximum probabilities for choosing the gamble. This is a legitimate choice for value-agnostic biases, but it is not the traditional choice (as far as I know). I wonder if the same results would hold with the more traditional formulation of the bias as an added constant to the utility of the gamble, i.e., p(gamble) = 1/(1+ exp(-mu(U_gamble + beta_gain - U_certain)). I believe in this case, you would also not have to specify different equations for positive or negative biases, or to limit the bias to the range of [-1,1] (indeed, the bias would be in reward-equivalent units).

Thank you for this suggestion. The winning choice model we used here was consistent with previous literature (Rutledge et al., 2015 & 2016), which decomposed the decision process into risk-attitude-driven valuation (e.g., loss and risk aversion) and value-insensitive motivational components. These approach/avoidance parameters are a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference.

As suggested, we also compared the traditional bias choice model. Model comparison did not support this. Please see our revision below:

Supplementary Page 4:

“We also considered the traditional bias parameter (cM4), rather than approach/avoidance parameters. We limited the bias to the range of [-100, 100], which was in reward-equivalent units.

However, model comparison did not support cM4 (Table S6).”

(10) Also, for equations 5-8, it seems that 5-6 are identical to 7-8 except for the use of beta_gain versus beta_loss. You might want to consider simplifying by putting beta in the equations and specifying in the text that, depending on the trial type (loss or gain), the relevant beta is used.

Thank you for this suggestion. We have now simplified it. Please see response to Reviewer 2, point 3.

(11) It is not clear what equations are applied to mixed trials in cM3.

Sorry for the confusion. We have now clarified this point.

Page 12:

“Approach/avoidance parameters are not applied to in mixed trials.”

(12) Model comparison: the mood models are nested within each other (e.g., mM3 can be derived from mM1 by setting beta_EV = beta_RPE). In this case, model comparison can use the likelihood ratio test instead of BIC, which can be too conservative (and therefore does not support the extra beta parameter for RPE, different from previous results in the literature). I wonder if a likelihood ratio test would lead to results more in line with previous findings with this task?

Thanks for this suggestion. We agree that mM1 (CR+EV+RPE) and mM3 (CR+GR) are nested. However, our model space also included unnested models, such as mM5 (CR+GR_better+GR_worse). Therefore, it was not reasonable in our model space to use likelihood ratio tests.

(13) Line 346: The replication sample is described as "healthy participants," however, their health (or mental health) status was not assessed, and they may as well have mental health concerns. I would suggest calling this a general sample or an undifferentiated sample - but not a healthy sample.

Sorry for the confusion. We have now corrected this phrase.

(14) Line 363: "in addition to the replication of previous findings in the validation dataset" is unclear. Are those tests not two-tailed?

Sorry for the unclear statement. In the replication analyses, we used one-tailed t-tests because the direction of the effect was revealed on the clinical dataset. Please see our clarification below:

Page 15:

“For the replication of previous findings in the validation dataset, we used one-tailed tests in line with our clinically motivated directional hypothesis.”

(15) Line 372: "validating our group manipulation" - the presented work does not have a manipulation. Maybe you meant "validating our grouping of participants"?

Thank you for this suggestion. We have now corrected it to make it clear.

(16) Figure 2B: It is not clear how the data were binned for illustration purposes only, and why this binning is necessary (I have not seen it in other papers) - presenting the data from each subject and the correlation line with error margins (as is done here) should be sufficient.

Thank you for flagging this. For illustration only, we binned the data proportional to group sizes: in the patient sample (S^- n = 25; S⁺ n = 58; ≈1:2), we displayed 3 bins for S^- and 6 bins for S⁺. We agree that binning is not necessary; all statistics were computed on raw, unbinned data. The binned panel was included solely for visualization, consistent with our prior work (Blain et al., 2023).

(17) Table 2: delta BIC should be presented per subject (that is, divided by the number of subjects in each group), as the groups are of different sizes, so as presented now, the columns are not comparable across groups.

Thank you for the helpful suggestion. Our goal in Table 2 is not to compare ΔBIC magnitudes across groups, but to identify the winning model within each group. The ΔBICs are aggregated at the group level solely to rank models for that group. Dividing by the number of participants would rescale each group’s column by a constant and would therefore not affect the within-group ranking or the conclusion that cM3 is the best model in all groups. For this reason, we retain the current presentation and interpret each column within group rather than across groups.

(18) Line 640 - the effect of expectations and prediction errors on mood was not only shown in healthy people, but also in people with depression (Rutledge et al., 2007, https://pubmed.ncbi.nlm.nih.gov/28678984/)

Thank you for this comment. Indeed, Rutledge et al., (2017) showed evidence for CR+EV+RPE mood model in adult people with depression. However, our study recruited adolescents with depression or anxiety, given that adolescent period might provide a developmental window for opportunities for early intervention of suicidality. Therefore, it is also possible that the current winning model was specific to adolescents. Please see our clarifications below:

Page 28:

“It is also possible that the current winning model was specific to adolescents. Given that Rutledge et al., (2017) supported the “CR-EV-RPE model” in adults with depression, our study with adolescent populations may suggest a developmental change for mood sensitivities.”

(19) Supplemental material: Is the R2 section about R-squared? Perhaps you can use superscript on the 2 to make that clearer? For Figure S2, how was model recovery determined? Should I interpret the confusion matrix as suggesting that the winning model for each and every simulated subject was the generating model, or was the winning model determined for the whole simulated population in each of the 100 simulations? Traditionally, confusion matrices use the former measure, but the results of 100% recoverability make me suspect the latter was used here. In Figure S3, should we not be looking at simulated parameters and recovered parameters? What are "real parameters" here?

Thank you for these important comments. We now consistently denote the coefficient of determination as R² (with a superscript 2) throughout the manuscript and Supplementary Materials.

For the model recovery analysis in Figure S2, we have clarified that the confusion matrix is computed at the population level. Specifically, for each of the 100 simulations we generated a full dataset under each candidate model, fit all models to that dataset, and selected the winning model based on group-level model evidence (BIC). Each cell in the confusion matrix therefore reflects the proportion of simulations in which model j was selected as the best-fitting model when the data were generated by model i. This operation was reasonable because the decision of the winning model is made on the population-level dataset rather than on individual subjects.

In Figure S3, the term “real parameters” referred to the parameters used to generate the simulated data. To avoid confusion, we now relabel these as “simulated (generating) parameters” and explicitly describe the figure as showing the relationship between simulated (generating) parameters and recovered parameters. Please see our revisions below:

Supplementary Pages 2-3:

“Model recovery: We generated 100 simulated datasets for each model (3 choice models and 8 mood models) using the fitted parameters of each model as the ground truth. Each dataset contained 201 trials and included 3 (or 8) sets of simulated data corresponding to the respective models. For each simulated dataset, we then fit all models and determined the winning model at the population level based on group-level BIC, yielding a confusion matrix in which each entry represents the proportion of simulations in which model j was selected as the best-fitting model when the data were generated by model i. As shown in Figure S2, all models are highly identifiable, indicating excellent recovery performance for both the choice and mood models.”

“Parameter recovery: Figure S3 shows good parameter recovery for both choice and mood winning model (choice: rs > 0.91, ps < 0.001; intraclass coefficients > 0.78; mood: rs > 0.90, ps < 0.001; intraclass coefficients > 0.86). Moreover, we computed cross-correlations between all generating (“generating”) and recovered (“fitted”) parameters. The resulting matrix showed high diagonal (choice winning model: rs > 0.91; mood winning model: rs > 0.90) and low off-diagonal (choice winning model: abs(rs) < 0.63; mood winning model: abs(rs) > 0.40) correlations, further supporting parameter recovery.”

Typos:

(1) Line 90: original → originate

(2) Line 596-598 - the same phrase is repeated twice.

(3) Line 616: on the other word → hand.

Sorry for the mistakes. We have now corrected them throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

For people unfamiliar with interpersonal theory or motivational-volitional model, or three-step theory (lines 105-106), could you briefly explain the key idea of mood and suicide before going to the decision-making tasks? And from this, maybe motivate the predictions in your task? In particular, in the abstract and introduction, the phrasing could be a bit more concise and simpler. In the abstract, sentences were sometimes quite long. In the introduction, some paragraphs are somewhat repetitive. In the discussion, there were some typos.

Thank you for these suggestions. We have now explained the key idea of mood and suicide before going to the decision-making tasks in the introduction, which can be seen below:

Pages 4-5:

“Contemporary theories of suicide converge on the idea that STB is initially caused by low mood experience. The interpersonal theory of suicide proposes that suicidal desire arises when people simultaneously feel socially disconnected (“thwarted belongingness”) and like a burden on others (“perceived burdensomeness”), experiences that are tightly linked to chronically low mood(25). The motivational–volitional model(26) and the three-step theory(27,28) similarly emphasize that when negative mood and feelings of defeat or entrapment are experienced as inescapable, they can give rise to suicidal ideation, and that the progression from ideation to suicide attempts depends on additional factors such as reduced fear of death, increased pain tolerance, and a tendency to act impulsively under intense affect. Some official organizations, e.g., National Institute of Mental Health, have also listed mood problems as warning signals(8). Interestingly, within the framework of decision making under uncertainty, gambling on lotteries with a revealed outcome has been found to induce high mood variance(29), providing an opportunity to assess the relationship between deficient mood and increased gambling decisions in STB.”

We have also refined the wording and corrected typos throughout the manuscript.

Reviewer #3 (Recommendations for the authors):

(1) Since many readers might only read the abstract, it is important that it is both informative and accurate. I have two suggestions in this respect. First, for the abstract to be more informative, it may be helpful to indicate already there that these are value-insensitive approach-avoidance parameters, in the sense that they favor/disfavor the gamble regardless of the potential outcomes' magnitude or probability. This issue is also present throughout the text, where the phrases "approach and avoidance motivation" are referred to as if they have established and precise computational definitions. In my view, these terms could just as easily be interpreted as parameters that multiply the value of potential gains or losses, which is not what the authors mean. It would be helpful to clarify this terminology.

Thank you for these suggestions. In line with previous literature (Rutledge et al., 2015 & 2016), approach and avoidance motivation are indeed defined at the computational level, referring to a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference. We have cited these papers in the manuscript. We also make it clear to further clarify approach and avoidance parameters in the abstract and introduction. Please see our revisions below:

Page 2 (Abstract):

“Using a prospect theory model enhanced with value-insensitive approach-avoidance parameters revealed that this rise in risky behavior resulted only from a heightened approach parameter in S⁺.Altogether, model-based choice data analysis indicated dysfunction in the approach system in S⁺, leading to greater propensity for gambling in the gain domain regardless of the lottery expected value.”

Page 3 (Introduction):

“A growing literature indeed shows that risky behavior can be far better explained after adding value-insensitive approach and avoidance components to prospect theory(18,19), that is by including a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference. This class of models highlights the important role of value-insensitive motivational components in decision making in addition to risk attitude-driven valuation (e.g., loss/risk aversion)(20).”

(2) The statement "our study uncovers the cognitive and affective mechanisms contributing to increased risk behavior in STB" is overstating the findings, as the study may have uncovered some contributing mechanisms, but likely not all of them. Removing the word "the" would fix this issue.

Thank you for this suggestion. We have now corrected it.

(3) Since mood is typically defined as lasting hours, it's inappropriate to refer to ratings that only reflect the last few trials as self-reports of mood. To be sure, I view the distinction between emotions and moods as quantitative, not qualitative, so I do not think there is a problem studying the former to understand the latter, but to avoid confusion, the terminology should follow common usage.

Thank you for this suggestion. We follow previous work and operational definitions regarding mood (Rutledge et al., 2014, Eldar & Niv, 2015, Vinckier et al., 2018). Emotion is usually a very brief response to a specific stimulus (Emanuel & Eldar, 2023), e.g., leading to rapid changes like surprise then fear. In contrast, mood is defined as a diffuse state that is not specific to one stimulus. Here, we operationally and computationally define mood as an affective state reflecting the recent history of safe and gamble outcomes. We now clarify that point in the main text. Please see our revision below:

Page 5:

“Although mood is thought to persist for hours, days, or even weeks(30-33), momentary mood, measured over the timescale in the laboratory setting, represents the accumulation of the impact of multiple events at the scale of minutes(30,32,34-38). Momentary mood external validity is demonstrated e.g., through its association with depression symptoms(37). Mood is different from emotions, which reflect immediate affective reactivity and is more transient (e.g. from surprise to fear)(31-33,39).”

(4) Line 78: The phrases "increase in risk attitude", "decrease in loss attitude", and "decrease in value-independent choice biases" are unclear to me in terms of their directionality. An attitude might be avoidant or embracing. If it is the former then increasing it would decrease risk-taking.

Thank you for pointing out the ambiguity. We have now corrected them throughout the manuscript. Please see our revision below:

Page 4:

“We therefore hypothesized that heightened approach motivation, or weakened avoidance motivation, would account for increased risk behavior in STB.”

(5) Line 125: I was not sure why one would expect the mood response to gamble-related quantities (EV and RPE) to be lower in STB and not higher.

Sorry for the typo. We hypothesized that mood would respond more strongly to gambling-related quantities—expected value (EV) and reward prediction error (RPE)—in adolescents with STB than in controls, given prior evidence that STB is associated with greater risk-taking.

(6) The text could use proofreading, as there are many typos. These are from the first 100 lines alone:

a) Abstract: regardless the lotteries -> regardless of the lotteries'.

b) Line 78: it remains whether.

c) Line 80: can each -> each can.

d) Line 90: may original from.

Sorry for the mistakes. We have now corrected them throughout the manuscript.

(7) The rationale for focusing on the S+ group for mood model comparison is incorrect. The purpose is to identify parameters that vary as a function of suicidality, and for that, the S- group is just as important.

Thank you for this comment. We agree that the S^- group is as important as the S⁺ group. A direct comparison was complicated because the winning mood models differed (S⁺: mM3; S^-: mM5; Table 3). To ensure comparability, we checked results from both model specifications (mM3 and mM5). The conclusions were convergent: mood sensitivity to certain rewards (CR) was lower in S⁺ than in S^- (see Fig. 3 for mM3 and Fig. S8 for mM5).

(8) There appears to be a contradiction between the inclusion criteria, which include having experienced suicidal thoughts and behaviors, and the definition of the S- group as not having suicidality.

Thank you for pointing out this mistake. The corrected version of inclusion criteria can be seen on Page 7:

“Patients were included if they met the following criteria: 1) both the researcher and psychiatrists agreed on their group classification; 2) they had a current diagnosis of major depressive disorder (MDD; unipolar depression), generalized anxiety disorder (GAD), or bipolar disorder with depressive episodes (BD), confirmed by two experienced psychiatrists using the Structured Clinical Interview for DSM-IV-TR-Patient Edition (SCID-P, 2/2001 revision; see Supplementary Note 1 for details); 3) they were between 10 and 19 years of age; 4) they had no organic brain disorders, intellectual disability, or head trauma; 5) they had no history of substance abuse; 6) they had no experience of electroconvulsive therapy.”

(9) It would be helpful to specify whether mood modeling was based on objective or subjective values, and why.

Thank you for this helpful suggestion. We have now clarified whether mood modeling was based on objective or subjective values, and why. Specifically, we constructed two model families: one in which mood was driven by objective monetary outcomes (objective values) and one in which mood was driven by subjective values derived from each participant’s fitted choice model (subjective values). We then used the VBA_groupBMC function in the VBA toolbox to perform family-wise model comparison, with 8 candidate mood models within each family. Consistent with previous literature, the objective-value family provided a clearly superior fit to the data (exceedance probability, EP = 1.000). Based on this result and for parsimony, we report and interpret the mood modeling results from the objective-value family in the main text. We have clarified this point below:

Supplement Pages 4-5:

“Supplementary Note 9: Mood model comparison using subjective values.

To identify whether mood modeling was based on objective or subjective values, we constructed two model families: one in which mood was driven by objective monetary outcomes (objective values) and one in which mood was driven by subjective values derived from each participant’s fitted choice model (subjective values). We then used the VBA_groupBMC function in the VBA toolbox (Daunizeau et al., 2014) to perform family-wise model comparison, with 8 candidate mood models within each family. Consistent with previous literature, the objective-value family provided a clearly superior fit to the data (exceedance probability, EP = 1.000).”