Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Teplenin and coworkers assesses the combined effects of localized depolarization and excitatory electrical stimulation in myocardial monolayers. They study the electrophysiological behaviour of cultured neonatal rat ventricular cardiomyocytes expressing the light-gated cation channel Cheriff, allowing them to induce local depolarization of varying area and amplitude, the latter titrated by the applied light intensity. In addition, they used computational modeling to screen for critical parameters determining state transitions and to dissect the underlying mechanisms. Two stable states, thus bistability, could be induced upon local depolarization and electrical stimulation, one state characterized by a constant membrane voltage and a second, spontaneously firing, thus oscillatory state. The resulting 'state' of the monolayer was dependent on the duration and frequency of electrical stimuli, as well as the size of the illuminated area and the applied light intensity, determining the degree of depolarization as well as the steepness of the local voltage gradient. In addition to the induction of oscillatory behaviour, they also tested frequency-dependent termination of induced oscillations.

Strengths:

The data from optogenetic experiments and computational modelling provide quantitative insights into the parameter space determining the induction of spontaneous excitation in the monolayer. The most important findings can also be reproduced using a strongly reduced computational model, suggesting that the observed phenomena might be more generally applicable.

Weaknesses:

While the study is thoroughly performed and provides interesting mechanistic insights into scenarios of ventricular arrhythmogenesis in the presence of localized depolarized tissue areas, the translational perspective of the study remains relatively vague. In addition, the chosen theoretical approach and the way the data are presented might make it difficult for the wider community of cardiac researchers to understand the significance of the study.

Reviewer #2 (Public review):

In the presented manuscript, Teplenin and colleagues use both electrical pacing and optogenetic stimulation to create a reproducible, controllable source of ectopy in cardiomyocyte monolayers. To accomplish this, they use a careful calibration of electrical pacing characteristics (i.e., frequency, number of pulses) and illumination characteristics (i.e., light intensity, surface area) to show that there exists a "sweet spot" where oscillatory excitations can emerge proximal to the optogenetically depolarized region following electrical pacing cessation, akin to pacemaker cells. Furthermore, the authors demonstrate that a high-frequency electrical wave-train can be used to terminate these oscillatory excitations. The authors observed this oscillatory phenomenon both in vitro (using neonatal rat ventricular cardiomyocyte monolayers) and in silico (using a computational action potential model of the same cell type). These are surprising findings and provide a novel approach for studying triggered activity in cardiac tissue.

The study is extremely thorough and one of the more memorable and grounded applications of cardiac optogenetics in the past decade. One of the benefits of the authors' "two-prong" approach of experimental preps and computational models is that they could probe the number of potential variable combinations much deeper than through in vitro experiments alone. The strong similarities between the real-life and computational findings suggest that these oscillatory excitations are consistent, reproducible, and controllable.

Triggered activity, which can lead to ventricular arrhythmias and cardiac sudden death, has been largely attributed to sub-cellular phenomena, such as early or delayed afterdepolarizations, and thus to date has largely been studied in isolated single cardiomyocytes. However, these findings have been difficult to translate to tissue and organ-scale experiments, as well-coupled cardiac tissue has notably different electrical properties. This underscores the significance of the study's methodological advances: the use of a constant depolarizing current in a subset of (illuminated) cells to reliably result in triggered activity could facilitate the more consistent evaluation of triggered activity at various scales. An experimental prep that is both repeatable and controllable (i.e., both initiated and terminated through the same means).

The authors also substantially explored phase space and single-cell analyses to document how this "hidden" bi-stable phenomenon can be uncovered during emergent collective tissue behavior. Calibration and testing of different aspects (e.g., light intensity, illuminated surface area, electrical pulse frequency, electrical pulse count) and other deeper analyses, as illustrated in Appendix 2, Figures 3-8, are significant and commendable.

Given that the study is computational, it is surprising that the authors did not replicate their findings using well-validated adult ventricular cardiomyocyte action potential models, such as ten Tusscher 2006 or O'Hara 2011. This may have felt out of scope, given the nice alignment of rat cardiomyocyte data between in vitro and in silico experiments. However, it would have been helpful peace-of-mind validation, given the significant ionic current differences between neonatal rat and adult ventricular tissue. It is not fully clear whether the pulse trains could have resulted in the same bi-stable oscillatory behavior, given the longer APD of humans relative to rats. The observed phenomenon certainly would be frequency-dependent and would have required tedious calibration for a new cell type, albeit partially mitigated by the relative ease of in silico experiments.

For all its strengths, there are likely significant mechanistic differences between this optogenetically tied oscillatory behavior and triggered activity observed in other studies. This is because the constant light-elicited depolarizing current is disrupting the typical resting cardiomyocyte state, thereby altering the balance between depolarizing ionic currents (such as Na+ and Ca2+) and repolarizing ionic currents (such as K+ and Ca2+). The oscillatory excitations appear to later emerge at the border of the illuminated region and non-stimulated surrounding tissue, which is likely an area of high source-sink mismatch. The authors appear to acknowledge differences in this oscillatory behavior and previous sub-cellular triggered activity research in their discussion of ectopic pacemaker activity, which is canonically expected more so from genetic or pathological conditions. Regardless, it is exciting to see new ground being broken in this difficult-to-characterize experimental space, even if the method illustrated here may not necessarily be broadly applicable.

We thank the reviewers for their thoughtful and constructive feedback, as well as for recognizing the conceptual and technical strengths of our work. We are especially pleased that our integrated use of optogenetics, electrical pacing, and computational modelling was seen as a rigorous and innovative approach to investigating spontaneous excitability in cardiac tissue.

At the core of our study was the decision to focus exclusively on neonatal rat ventricular cardiomyocytes. This ensured a tightly controlled and consistent environment across experimental and computational settings, allowing for direct comparison and deeper mechanistic insight. While extending our findings to adult or human cardiomyocytes would enhance translational relevance, such efforts are complicated by the distinct ionic properties and action potential dynamics of these cells, as also noted by Reviewer #2. For this foundational study, we chose to prioritize depth and clarity over breadth.

Our computational domain was designed to faithfully reflect the experimental system. The strong agreement between both domains is encouraging and supports the robustness of our framework. Although some degree of theoretical abstraction was necessary (thereby sometimes making it a bit harder to read), it reflects the intrinsic complexity of the collective behaviours we aimed to capture such as emergent bi-stability. To make these ideas more accessible, we included simplified illustrations, a reduced model, and extensive supplementary material.

A key insight from our work is the emergence of oscillatory behaviour through interaction of illuminated and non-illuminated regions. Rather than replicating classical sub-cellular triggered activity, this behaviour arises from systems-level dynamics shaped by the imposed depolarizing current and surrounding electrotonic environment. By tuning illumination and local pacing parameters, we could reproducibly induce and suppress these oscillations, thereby providing a controllable platform to study ectopy as a manifestation of spatial heterogeneity and collective dynamics.

Altogether, our aim was to build a clear and versatile model system for investigating how spatial structure and pacing influence the conditions under which bistability becomes apparent in cardiac tissue. We believe this platform lays strong groundwork for future extensions into more physiologically and clinically relevant contexts.

In revising the manuscript, we carefully addressed all points raised by the reviewers. We have also responded to each of their specific comments in detail, which are provided below.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

Please find my specific comments and suggestions below:

(1) Line 64: When first introduced, the concept of 'emergent bi-stability' may not be clear to the reader.

We concur that the full breadth of the concept of emergent bi-stability may not be immediately clear upon first mention. Nonetheless, its components have been introduced separately: “emergent” was linked to multicellular behaviour in line 63, while “bi-stability” was described in detail in lines 39–56. We therefore believe that readers could form an intuitive understanding of the combined term, which will be further clarified as the manuscript develops. To further ease comprehension of the reader, we have added the following clarification to line 64:

“Within this dynamic system of cardiomyocytes, we investigated emergent bi-stability (a concept that will be explained more thoroughly later on) in cell monolayers under the influence of spatial depolarization patterns.”

(2) Lines 67-80: While the introduction until line 66 is extremely well written, the introduction of both cardiac arrhythmia and cardiac optogenetics could be improved. It is especially surprising that miniSOG is first mentioned as a tool for optogenetic depolarisation of cardiomyocytes, as the authors would probably agree that Channelrhodopsins are by far the most commonly applied tools for optogenetic depolarisation (please also refer to the literature by others in this respect). In addition, miniSOG has side effects other than depolarisation, and thus cannot be the tool of choice when not directly studying the effects of oxidative stress or damage.

The reviewer is absolutely correct in noting that channelrhodopsins are the most commonly applied tools for optogenetic depolarisation. We introduced miniSOG primarily for historical context: the effects of specific depolarization patterns on collective pacemaker activity were first observed with this tool (Teplenin et al., 2018). In that paper, we also reported ultralong action potentials, occurring as a side effect of cumulative miniSOG-induced ROS damage. In the following paragraph (starting at line 81), we emphasize that membrane potential can be controlled much better using channelrhodopsins, which is why we employed them in the present study.

(3) Line 78: I appreciate the concept of 'high curvature', but please always state which parameter(s) you are referring to (membrane voltage in space/time, etc?).

We corrected our statement to include the specification of space curvature of the depolarised region:

“In such a system, it was previously observed that spatiotemporal illumination can give rise to collective behaviour and ectopic waves (Teplenin et al. (2018)) originating from illuminated/depolarised regions (with high spatial curvature).”

(4) Line 79: 'bi-stable state' - not yet properly introduced in this context.

The bi-stability mentioned here refers back to single cell bistability introduced in Teplenin et al. (2018), which we cited again for clarity.

“These waves resulted from the interplay between the diffusion current and the single cell bi-stable state (Teplenin et al. (2018)) that was induced in the illuminated region.”

(5) Line 84-85: 'these ion channels allow the cells to respond' - please describe the channel used; and please correct: the channels respond to light, not the cells. Re-ordering this paragraph may help, because first you introduce channels for depolarization, then you go back to both de- and hyperpolarization. On the same note, which channels can be used for hyperpolarization of cardiomyocytes? I am not aware of any, even WiChR shows depolarizing effects in cardiomyocytes during prolonged activation (Vierock et al. 2022). Please delete: 'through a direct pathway' (Channelrhodopsins a directly light-gated channels, there are no pathways involved).

We realised that the confusion arose from our use of incorrect terminology: we mistakenly wrote hyperpolarisation instead of repolarisation. In addition to channelrhodopsins such as WiChR, other tools can also induce a repolarising effect, including light-activatable chloride pumps (e.g., JAWS). However, to improve clarity, we recognize that repolarisation is not relevant to our manuscript and therefore decided to remove its mention (see below). Regarding the reported depolarising effects of WiChR in Vierock et al. (2022), we speculate that these may arise either from the specific phenotype of the cardiomyocytes used in the study, i.e. human induced pluripotent stem cell-derived atrial myocytes (aCMs), or from the particular ionic conditions applied during patch-clamp recordings (e.g., a bath solution containing 1 mM KCl). Notably, even after prolonged WiChR activation, the aCMs maintained a strongly negative maximum diastolic potential of approximately –55 mV.

“Although effects of illuminating miniSOG with light might lead to formation of depolarised areas, it is difficult to control the process precisely since it depolarises cardiomyocytes indirectly. Therefore, in this manuscript, we used light-sensitive ion channels to obtain more refined control over cardiomyocyte depolarisation. These ion channels allow the cells to respond to specific wavelengths of light, facilitating direct depolarisation (Ördög et al. (2021, 2023)). By inducing cardiomyocyte depolarisation only in the illuminated areas, optogenetics enables precise spatiotemporal control of cardiac excitability, an attribute we exploit in this manuscript (Appendix 2 Figure 1).”

(6) Figure 1: What would be the y-axis of the 'energy-like curves' in B? What exactly did you plot here?

The graphs in Figure 1B are schematic representations intended to clarify the phenomenon for the reader. They do not depict actual data from any simulation or experiment. We clarified this misunderstanding by specifying that Figure 1B is a schematic representation of the effects at play in this paper.

“(B) Schematic representation showing how light intensity influences collective behaviour of excitable systems, transitioning between a stationary state (STA) at low illumination intensities and an oscillatory state (OSC) at high illumination intensities. Bi-stability occurs at intermediate light intensities, where transitions between states are dependent on periodic wave train properties. TR. OSC, transient oscillations.”

To expand slightly beyond the paper: our schematic representation was inspired by a common visualization in dynamical systems used to illustrate bi-stability (for an example, see Fig. 3 in Schleimer, J. H., Hesse, J., Contreras, S. A., & Schreiber, S. (2021). Firing statistics in the bistable regime of neurons with homoclinic spike generation. Physical Review E, 103(1), 012407.). In this framework, the y-axis can indeed be interpreted as an energy landscape, which is related to a probability measure through the Boltzmann distribution: . Here, p denotes the probability of occupying a particular state (STA or OSC). This probability can be estimated from the area (BCL × number of pulses) falling within each state, as shown in Fig. 4C. Since an attractor corresponds to a high-probability state, it naturally appears as a potential well in the landscape.

(7) Lines 92-93: 'this transition resulted for the interaction of an illuminated region with depolarized CM and an external wave train' - please consider rephrasing (it is not the region interacting with depolarized CM; and the external wave train could be explained more clearly).

We rephrased our unclear sentence as follows:

“This transition resulted from the interaction of depolarized cardiomyocytes in an illuminated region with an external wave train not originating from within the illuminated region.”

(8) Figure 2 and elsewhere: When mentioning 'frequency', please state frequency values and not cycle lengths. Please also reconsider your distinction between high and low frequencies; 200 ms (5 Hz) is actually the normal heart rate for neonatal rats (300 bpm).

In the revised version, we have clarified frequency values explicitly and included them alongside period values wherever frequency is mentioned, to avoid any ambiguity. We also emphasize that our use of "high" and "low" frequency is strictly a relative distinction within the context of our data, and not meant to imply a biological interpretation.

(9) Lines 129-131: Why not record optical maps? Voltage dynamics in the transition zone between depolarised and non-depolarised regions might be especially interesting to look at?

We would like to clarify that optical maps were recorded for every experiment, and all experimental traces of cardiac monolayer activity were derived from these maps. We agree with the reviewer that the voltage dynamics in the transition zone are particularly interesting. However, we selected the data representations that, in our view, best highlight the main mechanisms. When we analysed full voltage profiles, they didn’t add extra insights to this main mechanism. As the other reviewer noted, the manuscript already presents a wide range of regimes, so we decided not to introduce further complexity.

(10) Lines 156-157: Why was the model not adapted to match the biophysical properties (e.g., kinetics, ion selectivity, light sensitivity) of Cheriff?

The model was not adapted to the biophysical properties of Cheriff, because this would entail a whole new study involving extensive patch-clamping experiments, fitting, and calibration to model the correct properties of the ion channel. Beyond considerations of time efficiency, incorporating more specific modelling parameters would not change the essence of our findings. While numeric parameter ranges might shift, the core results would remain unchanged. This is a result of our experimental design where we applied constant illumination of long duration (6s or longer), thus making a difference in kinetical properties of an optogenetic tool irrelevant. In addition, we were able to observe qualitatively similar phenomena using many other depolarising optogenetic tools (e.g. ChR2, ReaChR, CatCh and more) in our in-vitro experiments. We ended up with Cheriff as our optotool-of-choice for the practical reasons of good light-sensitivity and a non-overlapping spectrum with our fluorescent dyes.

Therefore, computationally using a more general depolarising ion channel hints at the more general applicability of the observed phenomena, supporting our claim of a universal mechanism  (demonstrated experimentally with CheRiff and computationally with ChR2).

(11) Line 158: 1.7124 mW/mm^2 - While I understand that this is the specific intensity used as input in the model, I am convinced that the model is not as accurate to predict behaviour at this specific intensity (4 digits after the comma), especially given that the model has not been adapted to Cheriff (probably more light sensitive than ChR2). Can this be rephrased?

We did not aim for quantitative correspondence between the computational model and the biological experiments, but rather for qualitative agreement and mechanistic insight (see line 157). Qualitative comparisons are computationally obtained in a whole range of different intensities, as demonstrated in the 3D diagram of Fig. 4C. We wanted to demonstrate that at one fixed light intensity (chosen to be 1.7124 mW/mm^2 for the most clear effect), it was possible for all three states (STA, OSC. TR. OSC.) to coexist depending on the number of pulses and their period. Therefore the specific intensity used in the computational model is correct, and for reproducibility, we have left it unchanged while clarifying that it refers specifically to the in silico model:

“Simulating at a fixed constant illumination of 1.7124 𝑚𝑊∕𝑚𝑚² and a fixed number of 4 pulses, frequency dependency of collective bi-stability was reproduced in Figure 4A.”

(12) Lines 160, 165, and elsewhere: 'Once again, Once more' - please delete or rephrase.

We agree that we could have written these binding words better and reformulated them to:

“Similar to the experimental observations, only intermediate electrical pacing frequencies (500-𝑚𝑠 period) caused transitions from collective stationary behaviour to collective oscillatory behaviour and ectopic pacemaker activity had periods (710 𝑚𝑠) that were different from the stimulation train period (500 𝑚𝑠). Figure 4B shows the accumulation of pulses necessary to invoke a transition from the collective stationary state to the collective oscillatory state at a fixed stimulation period (600 𝑚𝑠). Also in the in silico simulations, ectopic pacemaker activity had periods (750 𝑚𝑠) that were different from the stimulation train period (600 𝑚𝑠). Also for the transient oscillatory state, the simulations show frequency selectivity (Appendix 2 Figure 4B).”

(13) Line 171: 'illumination strength': please refer to 'light intensity'.

We have revised our formulation to now refer specifically to “light intensity”:

“We previously identified three important parameters influencing such transitions: light intensity, number of pulses, and frequency of pulses.”

(14) Lines 187-188: 'the illuminated region settles into this period of sending out pulses' - please rephrase, the meaning is not clear.

We reformulated our sentence to make its content more clear to the reader:

“For the conditions that resulted in stable oscillations, the green vertical lines in the middle and right slices represent the natural pacemaker frequency in the oscillatory state. After the transition from the stationary towards the oscillatory state, oscillatory pulses emerging from the illuminated region gradually dampen and stabilize at this period, corresponding to the natural pacemaker frequency.”

(15) Figure 7: A)- please state in the legend which parameter is plotted on the y-axis (it is included in the main text, but should be provided here as well); C) The numbers provided in brackets are confusing. Why is (4) a high pulse number and (3) a low pulse number? Why not just state the number of pulses and add alpha, beta, gamma, and delta for the panels in brackets? I suggest providing the parameters (e.g., 800 ms cycle length, 2 pulses, etc) for all combinations, but not rate them with low, high, etc. (see also comment above).

We appreciate the reviewer’s comments and have revised the caption for figure 7, which now reads as follows:

“Figure 7. Phase plane projections of pulse-dependent collective state transitions. (A) Phase space trajectories (displayed in the Voltage – x_r plane) of the NRVM computational model show a limit cycle (OSC) that is not lying around a stable fixed point (STA). (B) Parameter space slice showing the relationship between stimulation period and number of pulses for a fixed illumination intensity (1.72 𝑚𝑊 ∕𝑚𝑚2) and size of the illuminated area (67 pixels edge length). Letters correspond to the graphs shown in C. (C) Phase space trajectories for different combinations of stimulus train period and number of pulses (α: 800 ms cycle length + 2 pulses, β: 800 ms cycle length + 4 pulses, γ: 250 ms cycle length + 3 pulses, δ: 250 ms cycle length + 8 pulses). α and δ do not result in a transition from the resting state to ectopic pacemaker activity, as under these circumstances the system moves towards the stationary stable fixed point from outside and inside the stable limit cycle, respectively. However, for β and γ, the stable limit cycle is approached from outside and inside, respectively, and ectopic pacemaker activity is induced.”

(16) Line 258: 'other dimensions by the electrotonic current' - not clear, please rephrase and explain.

We realized that our explanation was somewhat convoluted and have therefore changed the text as follows:

“Rather than producing oscillations, the system returns to the stationary state along dimensions other than those shown in Figure 7C (Voltage and x_r), as evidenced by the phase space trajectory crossing itself. This return is mediated by the electrotonic current.”

(17) Line 263: ‘increased too much’ – please rephrase using scientific terminology.

We rephrased our sentence to:

“However, this is not a Hopf bifurcation, because in that case the system would not return to the stationary state when the number of pulses exceeds a critical threshold.”

(18) Line 275: 'stronger diffusion/electrotonic influence from the non-illuminated region' - not sure diffusion is the correct term here. Please explain by taking into account the membrane potential. Please make sure to use proper terminology. The same applies to lines 281-282.

We appreciate this comment, which prompted us to revisit on our text. We realised that some sections could be worded more clearly, and we also identified an error in the legend of Supplementary Figure 7. The corresponding corrections are provided below:

“However, repolarisation reserve does have an influence, prolonging the transition when it is reduced (Appendix 2 Figure 7). This effect can be observed either by moving further from the boundary of the illuminated region, where the electrotonic influence from the non-illuminated region is weaker, or by introducing ionic changes, such as a reduction in I_Ks and/or I_to. For example, because the electrotonic influence is weaker in the center of the illuminated region, the voltage there is not pulled down toward the resting membrane potential as quickly as in cells at the border of the illuminated zone.”

“To add a multicellular component to our single cell model we introduced a current that replicates the effect of cell coupling and its associated electrotonic influence.”

“Figure 7. The effect of ionic changes on the termination of pacemaker activity. The mechanism that moves the oscillating illuminated tissue back to the stationary state after high frequency pacing is dependent on the ionic properties of the tissue, i.e. lower repolarisation reserves (20% 𝐼_𝐾𝑠 + 50% 𝐼_𝑡𝑜) are associated with longer transition times.”

(19) Line 289: -58 mV (to be corrected), -20 mV, and +50 mV - please justify the selection of parameters chosen. This also applies elsewhere- the selection of parameters seems quite arbitrary, please make sure the selection process is more transparent to the reader.

Our choice of parameters was guided by the dynamical properties of the illuminated cells as well as by illustrative purposes. The value of –58 mV corresponds to the stimulation threshold of the model. The values of 50 mV and –20 mV match those used for single-cell stimulation (Figure 8C2, right panel), producing excitable and bistable dynamics, respectively. We refer to this point in line 288 with the phrase “building on this result.” To maintain conciseness, we did not elaborate on the underlying reasoning within the manuscript and instead reported only the results.

We also corrected the previously missed minus sign: -58 mV.

(20) Figure 8 and corresponding text: I don't understand what stimulation with a voltage means. Is this an externally applied electric field? Or did you inject a current necessary to change the membrane voltage by this value? Please explain.

Stimulation with a specific voltage is a standard computational technique and can be likened to performing a voltage-clamp experiment on each individual cell. In this approach, the voltage of every cell in the tissue is briefly forced to a defined value.

(21) Figure 8C- panel 2: Traces at -20 mV and + 50 mV are identical. Is this correct? Please explain.

Yes, that is correct. The cell responds similarly to a voltage stimulus of -20 mV or one of 50 mV, because both values are well above the excitation threshold of a cardiomyocyte.

(22) Line 344 and elsewhere: 'diffusion current' - This is probably not the correct terminology for gap-junction mediated currents. Please rephrase.

A diffusion current is a mathematical formulation for a gap junction mediated current here, so , depending on the background of the reader, one of the terms might be used focusing on different aspects of the results. In a mathematical modelling context one often refers to a diffusion current because cardiomyocytes monolayers and tissues can be modelled using a reaction-diffusion equation. From the context of fine-grain biological and biophysical details, one uses the term gap-junction mediated current. Our choice is motivated by the main target audience we have in mind, namely interdisciplinary researchers with a core background in the mathematics/physics/computer science fields.

However, to not exclude our secondary target audience of biological and medical readers we now clarified the terminology, drawing the parallel between the different fields of study at line 79:

“These waves resulted from the interplay between the diffusion current (also known in biology/biophysics as the gap junction mediated current) and the bi-stable state that was induced in the illuminated region.”

(23) Lines 357-58: 'Such ectopic sources are typically initiated by high frequency pacing' - While this might be true during clinical testing, how would you explain this when not externally imposed? What could be biological high-frequency triggers?

Biological high-frequency triggers could include sudden increases in heart rates, such as those induced by physical activity or emotional stress. Another possibility is the occurrence of paroxysmal atrial or ventricular fibrillation, which could then give rise to an ectopic source.

(24) Lines 419-420: 'large ionic cell currents and small repolarising coupling currents'. Are coupling currents actually small in comparison to cellular currents? Can you provide relative numbers (~ratio)?

Coupling currents are indeed small compared to cellular currents. This can be inferred from the I-V curve shown in Figure 8C1, which dips below 0 and creates bi-stability only because of the small coupling current. If the coupling current were larger, the system would revert to a monostable regime. To make this more concrete, we have now provided the exact value of the coupling current used in Figure 8C1.

“Otherwise, if the hills and dips of the N-shaped steady-state IV curve were large (Figure 8C-1), they would have similar magnitudes as the large currents of fast ion channels, preventing the subtle interaction between these strong ionic cell currents and the small repolarising coupling currents (-0.103649 ≈ 0.1 pA).”

(25) Line 426: Please explain how ‘voltage shocks’ were modelled.

We would like to refer the reviewer to our response to comment (20) regarding how we model voltage shocks. In the context of line 426, a typical voltage shock corresponds to a tissue-wide stimulus of 50 mV. Independent of our computational model, line 426 also cites other publications showing that, in clinical settings, high-voltage shocks are unable to terminate ectopic sustained activity, consistent with our findings.

(26) Lines 429 ff: 0.2pA/pF would correspond to 20 pA for a small cardiomyocyte of 100 pF, this current should be measurable using patch-clamp recordings.

In trying to be succinct, we may have caused some confusion. The difference between the dips (≈-0.07 pA/pF) and hills (_≈_0.11 pA/pF) is approximately 0.18 pA/pF. For a small cardiomyocyte, this corresponds to deviations from zero of roughly ±10 pA. Considering that typical RMS noise levels in whole-cell patch-clamp recordings range from 2-10 pA , it is understandable that detecting these peaks and dips in an I-V curve (average current after holding a voltage for an extended period)  is difficult. Achieving statistical significance would therefore require patching a large number of cells.

Given the already extensive scope of our manuscript in terms of techniques and concepts, we decided not to pursue these additional patch-clamp experiments.

Reviewer #2 (Recommendations for the authors):

Given the deluge of conditions to consider, there are several areas of improvement possible in communicating the authors' findings. I have the following suggestions to improve the manuscript.

(1) Please change "pulse train" straight pink bar OR add stimulation marks (such as "*", or individual pulse icons) to provide better visual clarity that the applied stimuli are "short ON, long OFF" electrical pulses. I had significant initial difficulty understanding what the pulse bars represented in Figures 2, 3, 4A-B, etc. This may be partially because stimuli here could be either light (either continuous or pulsed) or electrical (likely pulsed only). To me, a solid & unbroken line intuitively denotes a continuous stimulation. I understand now that the pink bar represents the entire pulse-train duration, but I think readers would be better served with an improvement to this indicator in some fashion. For instance, the "phases" were much clearer in Figures 7C and 8D because of how colour was used on the Vm(t) traces. (How you implement this is up to you, though!)

We have addressed the reviewer’s concern and updated the figures by marking each external pulse with a small vertical line (see below).

(2) Please label the electrical stimulation location (akin to the labelled stimulation marker in circle 2 state in Figure 1A) in at least Figures 2 and 4A, and at most throughout the manuscript. It is unclear which "edge" or "pixel" the pulse-train is originating from, although I've assumed it's the left edge of the 2D tissue (both in vitro and silico). This would help readers compare the relative timing of dark blue vs. orange optical signal tracings and to understand how the activation wavefront transverses the tissue.

We indicated the pacing electrode in the optical voltage recordings with a grey asterisk. For the in silico simulations, the electrode was assumed to be far away, and the excitation was modelled as a parallel wave originating from the top boundary, indicated with a grey zone.

(3) Given the prevalence of computational experiments in this study, I suggest considering making a straightforward video demonstrating basic examples of STA, OSC, and TR.OSC states. I believe that a video visualizing these states would be visually clarifying to and greatly appreciated by readers. Appendix 2 Figure 3 would be the no-motion visualization of the examples I'm thinking of (i.e., a corresponding stitched video could be generated for this). However, this video-generation comment is a suggestion and not a request.

We have included a video showing all relevant states, which is now part of the Supplementary Material.

(4) Please fix several typos that I found in the manuscript:

(4A) Line 279: a comma is needed after i.e. when used in: "peculiar, i.e. a standard". However, this is possibly stylistic (discard suggestion if you are consistent in the manuscript).

(4B) Line 382: extra period before "(Figure 3C)".

(4C) Line 501: two periods at end of sentence "scientific purposes.." .

We would like to thank the reviewer for pointing out these typos. We have corrected them and conducted an additional check throughout the manuscript for minor errors.

eLife Assessment

The authors investigate arrestin2-mediated CCR5 endocytosis in the context of clathrin and AP2 contributions. Using an extensive set of NMR experiments, and supported by microscopy and other biophysical assays, the authors provide compelling data on the roles of AP2 and clathrin in CCR5 endocytosis. This important work will appeal to an audience beyond those studying chemokine receptors, including those studying GPCR regulation and trafficking. The distinct role of AP2 and not clathrin will be of particular interest to those studying GPCR internalization mechanisms.

Reviewer #1 (Public review):

Petrovic et al. investigate CCR5 endocytosis via arrestin2, with a particular focus on clathrin and AP2 contributions. The study is thorough and methodologically diverse. The NMR titration data clearly demonstrate chemical shift changes at the canonical clathrin-binding site (LIELD), present in both the 2S and 2L arrestin splice variants. To assess the effect of arrestin activation on clathrin binding, the authors compare: truncated arrestin (1-393), full-length arrestin, and 1-393 incubated with CCR5 phosphopeptides. All three bind clathrin comparably, whereas controls show no binding. These findings are consistent with prior crystal structures showing peptide-like binding of the LIELD motif, with disordered flanking regions. The manuscript also evaluates a non-canonical clathrin binding site specific to the 2L splice variant. Though this region has been shown to enhance beta2-adrenergic receptor binding, it appears not to affect CCR5 internalization.

Similar analyses applied to AP2 show a different result. AP2 binding is activation-dependent and influenced by the presence and level of phosphorylation of CCR5-derived phosphopeptides. These findings are reinforced by cellular internalization assays.

In sum, the results highlight splice-variant-dependent effects and phosphorylation-sensitive arrestin-partner interactions. The data argue against a (rapidly disappearing) one-size-fits-all model for GPCR-arrestin signaling and instead support a nuanced, receptor-specific view, with one example summarized effectively in the mechanistic figure.

Weaknesses:

Figure 1 shows regions alphaFold model that are intrinsically disordered without making it clear that this is not an expected stable position. The authors NMR titration data are n=1. Many figure panels require that readers pinch and zoom to see the data.

Reviewer #2 (Public review):

Summary:

Based on extensive live cell assays, SEC, and NMR studies of reconstituted complexes, these authors explore the roles of clathrin and the AP2 protein in facilitating clathrin mediated endocytosis via activated arrestin-2. NMR, SEC, proteolysis, and live cell tracking confirm a strong interaction between AP2 and activated arrestin using a phosphorylated C-terminus of CCR5. At the same time a weak interaction between clathrin and arrestin-2 is observed, irrespective of activation.

These results contrast with previous observations of class A GPCRs and the more direct participation by clathrin. The results are discussed in terms of the importance of short and long phosphorylated bar codes in class A and class B endocytosis.

Strengths:

The 15N,1H and 13C,methyl TROSY NMR and assignments represent a monumental amount of work on arrestin-2, clathrin, and AP2. Weak NMR interactions between arrestin-2 and clathrin are observed irrespective of activation of arrestin. A second interface, proposed by crystallography, was suggested to be a possible crystal artifact. NMR establishes realistic information on the clathrin and AP2 affinities to activated arrestin with both kD and description of the interfaces.

Weaknesses:

This reviewer has identified only minor weaknesses with the study.

(1) I don't observe two overlapping spectra of Arrestin2 (1-393) +/- CLTC NTD in Supp Figure 1

(2) Arrestin-2 1-418 resonances all but disappear with CCR5pp6 addition. Are they recovered with Ap2Beta2 addition and is this what is shown in Supp Fig 2D

(3) I don't understand how methyl TROSY spectra of arrestin2 with phosphopeptide could look so broadened unless there are sample stability problems?

(4) At one point the authors added excess fully phosphorylated CCR5 phosphopeptide (CCR5pp6). Does the phosphopeptide rescue resolution of arrestin2 (NH or methyl) to the point where interaction dynamics with clathrin (CLTC NTD) are now more evident on the arrestin2 surface?

(5) Once phosphopeptide activates arrestin-2 and AP2 binds can phosphopeptide be exchanged off? In this case, would it be possible for the activated arrestin-2 AP2 complex to re-engage a new (phosphorylated) receptor?

(6) I'd be tempted to move the discussion of class A and class B GPCRs and their presumed differences to the intro and then motivate the paper with specific questions.

(7) Did the authors ever try SEC measurements of arrestin-2 + AP2beta2+CCR5pp6 with and without PIP2, and with and without clathrin (CLTC NTD? The question becomes what the active complex is and how PIP2 modulates this cascade of complexation events in class B receptors.

Reviewer #3 (Public review):

Summary:

Overall, this is a well-done study, and the conclusions are largely supported by the data, which will be of interest to the field.

Strengths:

Strengths of this study include experiments with solution NMR that can resolve high-resolution interactions of the highly flexible C-terminal tail of arr2 with clathrin and AP2. Although mainly confirmatory in defining the arr2 CBL 376LIELD380 as the clathrin binding site, the use of the NMR is of high interest (Fig. 1). The 15N-labeled CLTC-NTD experiment with arr2 titrations reveals a span from 39-108 that mediates an arr2 interaction, which corroborates previous crystal data, but does not reveal a second area in CLTC-NTD that in previous crystal structures was observed to interact with arr2.

SEC and NMR data suggest that full-length arr2 (1-418) binding with 2-adaptin subunit of AP2 is enhanced in the presence of CCR5 phospho-peptides (Fig. 3). The pp6 peptide shows the highest degree of arr2 activation, and 2-adaptin binding, compared to less phosphorylated peptide or not phosphorylated at all. It is interesting that the arr2 interaction with CLTC NTD and pp6 cannot be detected using the SEC approach, further suggesting that clathrin binding is not dependent on arrestin activation. Overall, the data suggest that receptor activation promotes arrestin binding to AP2, not clathrin, suggesting the AP2 interaction is necessary for CCR5 endocytosis.

To validate the solid biophysical data, the authors pursue validation experiments in a HeLa cell model by confocal microscopy. This requires transient transfection of tagged receptor (CCR5-Flag) and arr2 (arr2-YFP). CCR5 displays a "class B"-like behavior in that arr2 is rapidly recruited to the receptor at the plasma membrane upon agonist activation, which forms a stable complex that internalizes onto endosomes (Fig. 4). The data suggest that complex internalization is dependent on AP2 binding not clathrin (Fig. 5).

The addition of the antagonist experiment/data adds rigor to the study.

Overall, this is a solid study that will be of interest to the field.

Author response:

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

Reviewer #1 (Public review): 

Petrovic et al. investigate CCR5 endocytosis via arrestin2, with a particular focus on clathrin and AP2 contributions. The study is thorough and methodologically diverse. The NMR titration data are particularly compelling, clearly demonstrating chemical shift changes at the canonical clathrin-binding site (LIELD), present in both the 2S and 2L arrestin splice variants. 

To assess the effect of arrestin activation on clathrin binding, the authors compare: truncated arrestin (1-393), full-length arrestin, and 1-393 incubated with CCR5 phosphopeptides. All three bind clathrin comparably, whereas controls show no binding. These findings are consistent with prior crystal structures showing peptide-like binding of the LIELD motif, with disordered flanking regions. The manuscript also evaluates a non-canonical clathrin binding site specific to the 2L splice variant. Though this region has been shown to enhance beta2-adrenergic receptor binding, it appears not to affect CCR5 internalization. 

Similar analyses applied to AP2 show a different result. AP2 binding is activation-dependent and influenced by the presence and level of phosphorylation of CCR5-derived phosphopeptides. These findings are reinforced by cellular internalization assays. 

In sum, the results highlight splice-variant-dependent effects and phosphorylation-sensitive arrestin-partner interactions. The data argue against a (rapidly disappearing) one-size-fitsall model for GPCR-arrestin signaling and instead support a nuanced, receptor-specific view, with one example summarized effectively in the mechanistic figure. 

We thank the referee for this positive assessment of our manuscript. Indeed, by stepping away from the common receptor models for understanding internalization (b2AR and V2R), we revealed the phosphorylation level of the receptor as a key factor in driving the sequestration of the receptor from the plasma membrane. We hope that the proposed mechanistic model will aid further studies to obtain an even more detailed understanding of forces driving receptor internalization.

Reviewer #2 (Public review): 

Summary: 

Based on extensive live cell assays, SEC, and NMR studies of reconstituted complexes, these authors explore the roles of clathrin and the AP2 protein in facilitating clathrin-mediated endocytosis via activated arrestin-2. NMR, SEC, proteolysis, and live cell tracking confirm a strong interaction between AP2 and activated arrestin using a phosphorylated C-terminus of CCR5. At the same time, a weak interaction between clathrin and arrestin-2 is observed, irrespective of activation. 

These results contrast with previous observations of class A GPCRs and the more direct participation by clathrin. The results are discussed in terms of the importance of short and long phosphorylated bar codes in class A and class B endocytosis. 

Strengths: 

The 15N,1H, and 13C, methyl TROSY NMR and assignments represent a monumental amount of work on arrestin-2, clathrin, and AP2. Weak NMR interactions between arrestin-2 and clathrin are observed irrespective of the activation of arrestin. A second interface, proposed by crystallography, was suggested to be a possible crystal artifact. NMR establishes realistic information on the clathrin and AP2 affinities to activated arrestin, with both kD and description of the interfaces. 

We sincerely thank the referee for this encouraging evaluation of our work and appreciate the recognition of the NMR efforts and insights into the arrestin–clathrin–AP2 interactions.

Weaknesses: 

This reviewer has identified only minor weaknesses with the study.

(1) Arrestin-2 1-418 resonances all but disappear with CCR5pp6 addition. Are they recovered with Ap2Beta2 addition, and is this what is shown in Supplementary Figure 2D? 

We believe the reviewer is referring to Figure 3 - figure supplement 1. In this figure, the panels E and F show resonances of arrestin2^1-418 (apo state shown with black outline) disappear upon the addition of CCR5pp6 (arrestin2^1-418•CCR5pp6 complex spectrum in red). The panels C and D show resonances of arrestin2^1-418 (apo state shown with black outline), which remain unchanged upon addition of AP2b2^701-937 (orange), indicating no complex formation. We also recorded a spectrum of the arrestin2^1-418 •CCR5pp6 complex under addition of AP2b2 ^701-937(not shown), but the arrestin2 resonances in the arrestin2¹⁴¹⁸ •CCR5pp6 complex were already too broad for further analysis. This had been already explained in the text.

“In agreement with the AP2b2 NMR observations, no interaction was observed in the arrestin2 methyl and backbone NMR spectra upon addition of AP2b2 in the absence of phosphopeptide (Figure 3-figure supplement 1C, D). However, the significant line broadening of the arrestin2 resonances upon phosphopeptide addition (Figure 3-figure supplement 1E, F) precluded a meaningful assessment of the effect of the AP2b2 addition on arrestin2 in the presence of phosphopeptide””.

(2) I don't understand how methyl TROSY spectra of arrestin2 with phosphopeptide could look so broadened unless there are sample stability problems. 

We thank the referee for this comment. We would like to clarify that in general a broadened spectrum beyond what is expected from the rotational correlation time does not necessarily correlate with sample stability problems. It is rather evidence of conformational intermediate exchange on the micro- to millisecond time scale.

The displayed ¹H-¹⁵ N spectra of apo arrestin2 already suffer from line broadening due to such intrinsic mobility of the protein. These spectra were recorded with acquisition times of 50 ms (¹⁵N) and 55 ms (¹H) and resolution-enhanced by a 60˚-shifted sine-bell filter for ¹⁵N and a 60˚-shifted squared sine-bell filter for ¹H, respectively, which leads to the observed resolution with still reasonable sensitivity. The ¹H-¹⁵ resonances in Fig. 1b (arrestin2^1-393) look particularly narrow. However, this region contains a large number of flexible residues. The full spectrum, e.g. Figure 1-figure supplement 2, shows the entire situation with a clear variation of linewidths and intensities. The linewidth variation becomes stronger when omitting the resolution enhancement filters.

The addition of the CCR5pp6 phosphopeptide does not change protein stability, which we assessed by measuring the melting temperature of arrestin2^1-418 and arrestin2^1-418 •CCR5pp6 complex (Tm = 57°C in both cases). We believe that the explanation for the increased broadening of the arrestin2 resonances is that addition of the CCR5pp6, possibly due to the release of the arrestin2 strand b20, amplifies the mentioned intermediate timescale protein dynamics. This results in the disappearance of arrestin2 resonances. 

We have now included the assessment of arrestin2^1-418 and arrestin2^1-418 •CCR5pp6 stability in the manuscript:

“The observed line broadening of arrestin2 in the presence of phosphopeptide must be a result of increased protein motions and is not caused by a decrease in protein stability, since the melting temperature of arrestin2 in the absence and presence of phosphopeptide are identical (56.9 ± 0.1 °C)”.

(3) At one point, the authors added an excess fully phosphorylated CCR5 phosphopeptide (CCR5pp6). Does the phosphopeptide rescue resolution of arrestin2 (NH or methyl) to the point where interaction dynamics with clathrin (CLTC NTD) are now more evident on the arrestin2 surface? 

Unfortunately, when we titrate arrestin2 with CCR5pp6 (please see Isaikina & Petrovic et. al, Mol. Cell, 2023 for more details), the arrestin2 resonances undergo fast-to-intermediate exchange upon binding. In the presence of phosphopeptide excess, very few resonances remain, the majority of which are in the disordered region, including resonances from the clathrin-binding loop. Due to the peak overlap, we could not unambiguously assign arrestin2 resonances in the bound state, which precluded our assessment of the arrestin2-clathrin interaction in the presence of phosphopeptide. We have made this now clearer in the paragraph ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Due to significant line broadening and peak overlap of the arrestin2 resonances upon phosphopeptide addition, the influence of arrestin activation on the clathrin interaction could not be detected on either backbone or methyl resonances”.

(4) Once phosphopeptide activates arrestin-2 and AP2 binds, can phosphopeptide be exchanged off? In this case, would it be possible for the activated arrestin-2 AP2 complex to re-engage a new (phosphorylated) receptor?

This would be an interesting mechanism. In principle, this should be possible as long as the other (phosphorylated) receptor outcompetes the initial phosphopeptide with higher affinity towards the binding site. However, we do not have experiments to assess this process directly. Therefore, we rather wish not to further speculate.

(5) Did the authors ever try SEC measurements of arrestin-2 + AP2beta2+CCR5pp6 with and without PIP2, and with and without clathrin (CLTC NTD? The question becomes what the active complex is and how PIP2 modulates this cascade of complexation events in class B receptors. 

We thank the referee for this question. Indeed, we tested whether PIP2 can stabilize the arrestin2•CCR5pp6•AP2 complex by SEC experiments. Unfortunately, the addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. The resolution of SEC experiments was not sufficient to distinguish arrestin2 in oligomeric form or in arrestin2•CCR5pp6•AP2 complex. We now mention this in the text: 

“We also attempted to stabilize the arrestin2-AP2b2-phosphopetide complex through the addition of PIP2, which can stabilize arrestin complexes with the receptor (Janetzko et al., 2022). The addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. Unfortunately, the resolution of the SEC experiments was not sufficient to separate the arrestin2 oligomers from complexes with AP2b2”.

Reviewer #3 (Public review): 

Summary: 

Overall, this is a well-done study, and the conclusions are largely supported by the data, which will be of interest to the field. 

Strengths: 

(1) The strengths of this study include experiments with solution NMR that can resolve high-resolution interactions of the highly flexible C-terminal tail of arr2 with clathrin and AP2. Although mainly confirmatory in defining the arr2 CBL 376LIELD380 as the clathrin binding site, the use of the NMR is of high interest (Figure 1). The 15N-labeled CLTC-NTD experiment with arr2 titrations reveals a span from 39-108 that mediates an arr2 interaction, which corroborates previous crystal data, but does not reveal a second area in CLTC-NTD that in previous crystal structures was observed to interact with arr2.

(2) SEC and NMR data suggest that full-length arr2 (1-418) binding with the 2-adaptin subunit of AP2 is enhanced in the presence of CCR5 phospho-peptides (Figure 3). The pp6 peptide shows the highest degree of arr2 activation and 2-adaptin binding, compared to less phosphorylated peptides or not phosphorylated at all. It is interesting that the arr2 interaction with CLTC NTD and pp6 cannot be detected using the SEC approach, further suggesting that clathrin binding is not dependent on arrestin activation. Overall, the data suggest that receptor activation promotes arrestin binding to AP2, not clathrin, suggesting the AP2 interaction is necessary for CCR5 endocytosis. 

(3) To validate the solid biophysical data, the authors pursue validation experiments in a HeLa cell model by confocal microscopy. This requires transient transfection of tagged receptor (CCR5-Flag) and arr2 (arr2-YFP). CCR5 displays a "class B"-like behavior in that arr2 is rapidly recruited to the receptor at the plasma membrane upon agonist activation, which forms a stable complex that internalizes into endosomes (Figure 4). The data suggest that complex internalization is dependent on AP2 binding, not clathrin (Figure 5). 

We thank the referee for the careful and encouraging evaluation of our work. We appreciate the recognition of the solidity of our data and the support for our conclusions regarding the distinct roles of AP2 and clathrin in arrestin-mediated receptor internalization.

Weaknesses:

The interaction of truncated arr2 (1-393) was not impacted by CCR5 phospho-peptide pp6, suggesting the interaction with clathrin is not dependent on arrestin activation (Figure 2). This raises some questions.

We thank the referee for raising this concern, as we were also surprised by the discovery that the interaction does not depend on arrestin activation. However, the NMR data clearly show at atomic resolution that arrestin activation does not influence the interaction with clathrin in vitro. Evolutionary, the arrestin-clathrin interaction appears not to be conserved as the visual arrestin completely lacks a clathrin-binding motif. For that reason, we believe that the weak arrestin-clathrin interaction provides more of a supportive role during the internalization rather than the regulatory interaction with AP2, which requires and quantitatively depends on the arrestin2 activation. We have reflected on this in the Discussion:

“Although the generalization of this mechanism from CCR5 to other arr-class B receptors has to be explored further, it is indirectly corroborated in the visual rhodopsin-arrestin1 system. The arr-class B receptor rhodopsin (Isaikina et al., 2023) also undergoes CME (Moaven et al., 2013) with arrestin1 harboring the conserved AP2 binding motif, but missing the clathrinbinding motif (Figure 1-figure supplement 1A)”.

Overall, the data are solid, but for added rigor, can these experiments be repeated without tagged receptor and/or arr2? My concern stems from the fact that the stability of the interaction between arr2 and the receptor may be related to the position of the tags.

We thank the referee for this suggestion, which refers to the cellular experiments; the biophysical experiments were carried out without tags. To eliminate the possibility of tags contributing to receptor-arrestin2 binding in the cellular experiments, we also performed the experiments in the presence of CCR5 antagonist [5P12]CCL5 (Figure 4). These data show that in the case of inactive CCR5, arrestin2 is not recruited to CCR5, nor does it form internalization complexes, which would be the case if the tags were increasing the receptorarrestin interaction. In contrast, if the tags were decreasing the interaction, we would not expect such a strong internalization. As indicated below, we have also attempted to perform our cellular experiments using an N-terminally SNAP-tagged CCR5. Unfortunately, this construct did not express in HeLa cells indicating that SNAP-CCR5 was either toxic or degraded.

Reviewing Editor Comments: 

Overall, the reviewers did not suggest much by way of additional experiments. They do suggest several aspects of the manuscript that would benefit from further clarification. 

Reviewer #1 (Recommendations for the authors): 

(1) The distinction between arrestin 2S and arrestin 2L as relates to the canonical and non-canonical clathrin binding sites would benefit from clarification, particularly because the second binding site depends on the splice variant. This is something that some readers may not be familiar with (particularly young ones that are hopefully part of the intended readership).

We thank the referee for this suggestion. We would like to emphasize that in our work, only the long arrestin2 splice variant was used, which contains both binding sites. We have now introduced the splice variants and their relation to the clathrin binding sites in the text. 

In section ‘Localizing and quantifying the arrestin2-clathrin interaction by NMR spectroscopy’:

“Clathrin and arrestin interact in their basal state (Goodman et al., 1996), and a structure of a complex between arrestin2 and the clathrin heavy chain N-terminal domain (residues 1-363, named clathrin-N in the following) has been solved by X-ray crystallography (PDB:3GD1) in the absence of an arrestin2-activating phosphopeptide (Kang et al., 2009). This structure (Figure 1-figure supplement 1B) suggests a 2:1 binding model between arrestin2 and clathrinN. The first interaction (site I) is observed between the ³⁷⁶LIELD³⁸⁰ clathrin-binding motif of the arrestin2 CBL and the edge of the first two β-sheet blades of clathrin-N, whereas the second interaction (site II) occurs between arrestin2 residues ³³⁴LLGDLA³³⁹ and the 4th and 5th blade of clathrin-N. The latter arrestin interaction site is not present in the arrestin2 splice variant arrestin2S (for short) where an 8-amino acid insert (residues 334-341) between β-strands 18 and 19 is removed (Kang et al., 2009)”.

Section ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Figure 2A (left) shows the intensity changes (full spectra in Figure 2-figure supplement 1A) of the clathrin-N ¹H-¹⁵N TROSY resonances [assignments transferred from BMRB, ID:25403 (Zhuo et al., 2015)] upon addition of a one-molar equivalent of arrestin2^1-393. A significant intensity reduction due to line broadening is detected for clathrin-N residues 39-40, 48-50, 62-72, 83-90, 101-106, and 108. These residues form a clearly defined binding region at the edges of blade 1 and blade 2 of clathrin-N (Figure 2A, right), which corresponds to interaction site I in the 3GD1 crystal structure, involving the conserved arrestin2 ³⁷⁶LIELD³⁸⁰ motif. However, no significant signal attenuation was observed for clathrin-N residues in blade 4 and blade 5, which would correspond to the crystal interaction site II with arrestin2 residues ³³⁴LLGDLA³³⁹ that are absent in the arrestin2S splice variant. Thus only one arrestin2 binding site in clathrin-N is detected in solution, and site II of the crystal structure may be a result of crystal packing”.

(2) Acronym density is high throughout. While many are standard in the clathrin literature, this could hinder accessibility for readers with a GPCR or arrestin focus.

We agree with the referee. The acronyms were hard to avoid. The most non-obvious acronym seems ‘CLTC-NTD’ for the N-terminal domain of the clathrin heavy chain, which uses the non-obvious, but common gene name CLTC for the clathrin heavy chain. We have now replaced ‘CLTC-NTD’ by ‘clathrin-N’ and hope that this makes the text easier to follow.

(3) The NMR section, while impressive in scope, had writing that was more difficult to follow than the rest. I am curious what percentage of resonance could be assigned. 

We apologize if the NMR sections of this manuscript were unclear. We attempted to provide a very detailed description of the experimental setup and the spectral results. Being experienced NMR spectroscopists, we have tried very hard to obtain good 3D triple resonance spectra for assignments, but their sensitivity is very low. We believe that this is due to the microsecond dynamics present in the system, which makes the heteronuclear transfers inefficient. So far, we have been able to assign ~30% of the visible arrestin2 resonances. We are still validating the assignments and are working on the analysis and an explanation for this arrestin2 behavior. Therefore, at this point, we want to refrain from stronger statements besides that considerable intrinsic microsecond dynamics is impeding the assignment process.

(4) It may be worth noting in the main text that truncated arrestins have slightly higher basal activation. I was curious why the truncated arrestin was not chosen for the AP2 NMR titrations. Presumably, an effect would be more likely to be seen.

While some truncated arrestin2 variants (comprising residues 1-382 or 1-360) indeed show higher basal activity than the full-length arrestin2, they typically completely lack the b20 strand (residues 386-390), which is crucial for the formation of a parallel b-sheet with strand b1, and whose release governs arrestin activation. Our truncated arrestin2 construct comprises residues 1-393 and contains strand b20. In our experience, no significant difference in basal activity, as assessed by Fab30 binding, was detected for arrestin2^1-393 and arrestin2^1-418 (Author response image 1).

Author response image 1.

SEC profiles showing arrestin2^1–393 (left) and arrestin2^1-418 (right) activation by the CCR5pp6 phosphopeptide as assayed by Fab30 binding. The active ternary arrestin2-phosphopeptide-Fab30 complex elutes at a lower volume than the inactive apo arrestin2 or the binary arrestin2-phosphopeptide complex. Both arrestin2 constructs are activated by the phosphopeptide to a similar level as assessed by the integrated SEC volumes.

We want to emphasize that we used full-length arrestin2^1-418 in order to assess the AP2 interaction, as the crystal structure of arrestin2 peptide-AP2 (PDB:2IV8) shows residues past the residue 393 involved in binding.

PDB codes are currently not accompanied by corresponding literature citations throughout. Please add these. 

Thank you for this suggestion. In the manuscript, we were careful to provide the full literature citation the first time each PDB code is mentioned. To avoid redundancy and maintain clarity, we rather do not want to repeat the citations with every subsequent mentioning of the PDB code.

(5) The AlphaFold model could benefit from a more transparent discussion of prediction confidence and caveats. The younger crowd (part of the presumed intended readership) tends to be more certain that computational output is 'true'. Figure 1A shows long loops that are likely regions of low confidence in the prediction. Displaying expected disordered regions as transparent or color-coded would help highlight these as flexible rather than stable, especially for that same younger readership. 

We need to explain that the AlphaFold model of arrestin2 was only used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available apo bovine (PDB:1G4M) and apo human (PDB:8AS4) arrestin2 crystal structures. However, the AlphaFold model of arrestin2 is basically identical to the crystal structures in the regions that are visible in the crystal structures. We have clarified this now in the caption to Figure 1.

“The model was used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available crystal structures of apo arrestin2 [bovine: PDB 1G4M (Han et al., 2001), human: PDB 8AS4 (Isaikina et al., 2023)]. In the other structured regions, the model is virtually identical to the crystal structures”.

(6) Several figure panels were difficult to interpret due to their small size. Especially microscopy insets, where I needed to simply trust that the authors were accurately describing the data. Enlarging panels is essential, and this may require separating them into different figures.

We appreciate the referee’s concern regarding figure readability. However, we want to indicate that all our figures are provided as either high-resolution pixel or scalable vector graphics, which allow for zooming in to very fine detail, either electronically or in print. This ensures that microscopy insets and other small panels can be examined clearly when viewed appropriately. We believe the current layout of the figures is necessary to be able to efficiently compare the data between different conditions.

Many figure panels had text size that was too small. Font inconsistencies across figures also stand out. 

We apologize for this. We have now enlarged the font size in the figures and made the styles more consistent.

For Fig. 1F, consider adding individual data points and error bars.

Thank you for this suggestion. However, Figure 1F already contains the individual data points, with colored circles corresponding to the titration condition. As we did not have replicates of the titration, no error bars are shown. However, the close agreement of the theoretical fit with the individual measured data points stemming from different experiments shows that the statistical errors are indeed very small. We have estimated an overall error for the Kd (as indicated in panel F, right) by error propagation based on an estimate of the chemical shift error as obtained in the NMR software POKY (based on spectral noise). 

Reviewer #2 (Recommendations for the authors):

(1) I don't observe two overlapping spectra of Arrestin2 (1393) +/- CLTC NTD in Supplementary Figure 1.

As explained above all the spectra are shown as scalable vector graphics. The overlapping spectra are visible when zoomed in.

(2) I'd be tempted to move the discussion of class A and class B GPCRs and their presumed differences to the intro and then motivate the paper with specific questions.

We appreciate the referee’s suggestion and had a similar idea previously. However, as we do not have data on other class-A or class-B receptors, we rather don’t want to motivate the entire manuscript by this question.

Reviewer #3 (Recommendations for the authors): 

(1) What happens with full-length arr2 (1-418) when the phospho-peptide pp6 is added to the reaction? It's unclear to me that 1-418 would behave the same as 1-393 because the arr2 tail of 1-393 is likely sufficiently mobile to accommodate binding to CLTC NTD. I suggest attempting this experiment for added rigor.

We believe that there is a misunderstanding. The 1-393 and 1-418 constructs differ by the disordered C-terminal tail, which is not involved in the clathrin interaction with the arrestin2 376-380 (LIELD) residues. Accordingly, both 1-393 and 1-418 constructs show almost identical interactions with clathrin (Figure 2A and 2C). Moreover, the phospho-activated arrestin2^1-393 (Figure 2B) interacts identically with clathrin as inactive arrestin2^1-393 and inactive arrestin2^1-418. We believe that this comparison is sufficient for the conclusion that arrestin activation does not play a role in arrestin-clathrin binding.

(2) If the tags were moved to the N-terminus of the receptor and/or arr2, I wonder if the complex is as stable (Figure 4)? 

We thank the referee for their suggestion. We have indeed attempted to perform our experiments using an N-terminally SNAP-tagged CCR5. Unfortunately, this construct did not express in the HeLa cells indicating that SNAP-CCR5 was either toxic or degraded. Unfortunately, as the lab is closing due to the retirement of the PI, we are not able to repeat these experiments with further differently positioned tags. We refer also to our answer above that the experiments with the antagonist [5P12]CCL5 present a certain control.

(3) A biochemical assay to measure receptor internalization, in addition to the cell biological approach (Figure 5), would add additional rigor to the study and conclusions.

We tried to measure internalization using a biochemical approach. We tried to pull-down CCR5 from HeLa cells and assess arrestin binding. Unfortunately, even using different buffer conditions, we found that CCR5 was aggregating once solubilized from membranes, preventing us from doing this analysis. We had a similar problem when we exogenously expressed CCR5 in insect cells for purification purposes. We have long experience with CCR5, and this receptor is very aggregation-prone due to extended charged surfaces, which interact with the chemokines.

As an alternative, and in support of the cellular immunofluorescence assays, we also attempted to obtain internalization data via FACS using a CCR5 surface antibody (CD195 Monoclonal Antibody eBioT21/8). CD195 recognizes the N-terminus of the receptor. Unfortunately, the presence of the chemokine ligand (~ 8 kDa) interferes with antibody binding, precluding the quantitative biochemical assessment of the arrestin2 mutants on the CCR5 internalization.

For these reasons, we were particularly careful to quantify CCR5 internalization from the immunofluorescence microscopy data using colocalization coefficients as well as puncta counting (Figure 4+5).

eLife Assessment

In this manuscript Taujale et al describe an interdisciplinary approach to mine the human channelome and further discover orthologues across diverse organisms. Further, this work provides evidence that supports a role for conserved residues in CALHM channel gating. Overall this important work presents findings that can be helpful to the ion channel community, as well as to those interested in improved methods for mining sequence space for their protein of interest. However, further validation of the improvements their approach shows over previous approaches is needed, making this a solid contribution to the literature in this field.

Reviewer #1 (Public review):

Summary:

In the manuscript "Identification and classification of ion-channels across the tree of life: Insights into understudied CALHM channels" Taujale et al describe an interdisciplinary approach to mine the human channelome and further discover orthologues across diverse organisms, culminating in delineating co-conserved patterns in an example ion channel: CALHM. Overall, this paper comes in two sections, one where 419 human ion channels and 48,000+ channels from diverse organisms are found through a multidisciplinary data mining approach, and a second where this data is used to find co-conserved sequences, whose functional significance is validated via experiments on CALHM1 and CALHM6. Overall, this is an intriguing data-first approach to better understand even understudied ion channels like CALHM6. However, more needs to be done to pull this story together into a single coherent narrative.

Strengths:

This manuscript takes advantage of modern-day LLM tools to better mine the literature for ion channel sequences in humans and other species with orthologous ion channel sequences. They explore the 'dark channome' of understudied ion channels to better reveal the information evolution has to tell us about our own proteins, and illustrate the information this provides access to in experimental studies in the final section of the paper. Finally, they provide a wealth of information in the supplementary tables (in the form of Excel spreadsheets and a dataset on Zenodo) for others to explore. Overall, this is a creative approach to a wide-reaching problem that can be applied to other families of proteins.

Weaknesses:

Overall, while a considerable amount of work has been done for this manuscript, the presentation, both in terms of writing and figures, still can use more work even after a first round of revisions. While they have improved their discussion to more clearly describe the need for a better-curated sequence database of ion channels, and how existing resources fall short, some aspects of this process and the motivation remain unclear, especially when it comes to the CALHM sequences.

Overall, this manuscript is a valuable contribution to the field, but requires a few main things to make it truly useful. Namely, how has this approach really improved their ability to identify conserved residues in CALHM over a less-involved approach? And better organization of the first results section of the paper, which is critical to the downstream understanding of the paper, as well as some cosmetic improvements.

Reviewer #2 (Public review):

Summary:

In this paper, the authors defined the "channelome," consisting of 419 predicted human ion channels as well as 48,000 ion channel orthologs from other organisms. Using this information, the ion channels were clustered into groups, which can potentially be used to make predictions about understudied ion channels in the groups. The authors then focused on the CALHM ion channel family, mutating conserved residues and assessing channel function.

Strengths:

The curation of the channelome provides an excellent resource for researchers studying ion channels. Supplemental Table 1 is well organized with an abundance of useful information.

Comments on revisions:

The authors have thoroughly addressed my concerns and the manuscript is substantially improved. I have just a few suggestions regarding wording/clarification.

In Supplemental Figure 4, the Western blots (n=3) were quantitated, but the surface biotinylation was not. While I suppose that it is fine to just show one representative experiment for the biotinylation assay, the authors should indicate in the legend how many times this was done. It is essential to know whether these data in Supplemental Figure 4E, F are reproducible as they are absolutely critical for interpretation of all of the data in Figure 5.

Author response:

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

Reviewing Editor Comments:

(A) Revisions related to the first part, regarding data mining and curation:

(1) One question that arises with the part of the manuscript that discusses the identification and classification of ion channels is whether these will be made available to the wider public. For the 419 human sequences, making a small database to share this result so that these sequences can be easily searched and downloaded would be desirable. There are a variety of acceptable formats for this: GitHub/figshare/zenodo/university website that allows a wider community to access their hard work. Providing such a resource would greatly expand the impact of this paper. The same question can be asked of the 48,000+ ion channels from diverse organisms.

We thank the reviewer for providing this important feedback. While the long term plan is to provide access to these sequences and annotations through a knowledge base resource like Pharos, we agree with the comments that it would be beneficial to have these sequences made available with the manuscript as well. We have compiled 3 fasta files containing the following: 1) Full length sequences for the curated 419 ion channel sequences. 2) Pore containing domain sequences for the 343 pore domain containing human ion channel sequences. 3) All the identified orthologs for the human ion channels.

For each sequence in these files, we have extended the ID line to include the most pertinent annotation information to make it readily available. For example, the id>sp|P48995|TRPC1_HUMAN|TRP:VGIC--TRP-TRPC|pore-forming|dom:387-637 provides the classification, unit and domain bounds for the human TRPC1 in the fasta file itself.

These files have been uploaded to Zenodo and are available for download with doi 10.5281/zenodo.16232527. We have included this in the Data Availability statement of the manuscript as well.

(2) Regarding the 48,000+ sequences, what checks have been done to confirm that they all represent bona fide, full-length ion channel sequences? Uniprot contains a good deal of unreviewed sequences, especially from single-celled organisms. The process by which true orthologues were identified and extraneous hits discarded should be discussed in more detail, and all inclusion criteria should be described and justified, clearly illustrating that the risk of gene duplicates and fragments in this final set of ion channel orthologues has been avoided. Related to this, does this analysis include or exclude isoforms?

We thank the reviewer for raising this important point. Our selection of curated proteomes and the KinOrtho pipeline for orthology detection returns, up to an extent, reliable orthologous sequence sets. In brief, our database sequences are retrieved from full proteomes that only include proteins that are part of an official proteome release. Thus, they are mapped from a reference genome to ensure species-specific relevance and avoid redundancy. The >1500 proteomes in this analysis were selected based on their wider use in other orthology detection pipelines like OMA and InParanoid. Our orthology detection pipeline, KinOrtho, performs a fulllength and a domain-based orthology detection which ensures that the orthologous relationships are being defined based on the pore-domain sequence similarity. 

But we agree with the reviewer that this might leave room for extraneous, fragments or misannotated sequences to be included in our results. Taking this into careful consideration, we have expanded our sequence validation pipeline to include additional checks such as checking the uniport entry type, protein existence evidence and sequence level checks such as evaluating the compositional bias, non-standard codons and sequence lengths. These validation steps are now described in detail in the Methods section under orthology analysis (lines 768-808). All the originally listed orthologous sequences passed this validation pipeline and thus provide additional confidence that they are bona fide full length ion channel sequences.

We have also expanded this section (lines 758 – 766) to provide more details of the KinOrtho pipeline for orthology detection, which is a previously published method used for orthology detection in kinases by our lab.

Finally, our orthology analysis excludes isoforms and only spans the primary canonical sequences that are part of the UniProt Proteomes annotated sequence set. The isoforms that are generally available in UniProt Proteomes in a separate file named *_additional.fasta were not included in this analysis.

(3) The decision to show the families of ion channels in Figure 1 as pie charts within a UMAP embedding is intriguing but somewhat non-intuitive and difficult to understand. Illustrating these results with a standard tree-like visualization of the relationship of these channels to each other would be preferred.

We appreciate the feedback provided by the reviewer, and understand that a standard tree-like visualization would be much easier to interpret and familiar than a bubble chart based on UMAP embeddings. However, we opted to use the bubble chart for the following reasons:

Low sequence similarity: the 419 human ICs share very minimal sequence similarity, falling in the twilight zone or lower ( Dolittle, 1992; PMID:1339026). Thus, traditional multiple sequence alignment and phylogenetic reconstruction methods perform very poorly and generate unreliable or even misleading results. To explore the practicality of this option, we pursued performing a multiple sequence alignment of just 3 of the possibly related IC families as suggested by reviewer 2 (CALHM, Pannexins, and Connexins) using the state of the art structure based sequence alignment method Foldmason (doi: https://doi.org/10.1101/2024.08.01.606130). Even then, the sequence alignment and the resulting tree for just these 3 families were poor and unreliable, as illustrated in the attached Author response Image 2.

Protein embeddings based clustering: Novel LLM based approaches such as the protein language model embeddings offer ways to overcome these limitations by capturing sequence, structure, function and evolutionary properties in a high-dimensional space. Thus, we employed this model using DEDAL followed by UMAP for dimensionality reduction, which preserves biologically meaningful local and global relationships.

Abstraction at family level: In Figure 1, we aggregate individual channels into family bubbles with their positions representing the average UMAP coordinates of their members. This offers a balance between an intuitive view of how IC families are distributed in the embedding space and reflects potential functional and evolutionary proximities, while not being impeded by individual IC relationships across families.

We have revised the figure legend (lines 1221 – 1234) with additional description of the visualization and the process used to generate it, and the manuscript text (lines 248-270) provides the rationale behind the selection of this method.

(4) A strength of this paper is the visualization of 'dark' ion channels. However, throughout the paper, this could be emphasized more as the key advantage of this approach and how this or similar approaches could be used for other families of proteins. Specifically, in the initial statement describing 'light' vs 'dark channels', the importance of this distinction and the historical preference in science to study that which has already been studied can be discussed more, even including references to other studies that take this kind of approach. An example of a relevant reference here is to the Structural Genomics Consortium and its goals to achieve structures of proteins for which functions may not be well-characterized. Clarifying these motivations throughout the entire paper would strengthen it considerably.

We thank the reviewer for this constructive comment and agree that highlighting the strength of visualizing “dark” channels and prioritizing them for future studies would strengthen the paper. As suggested, we have revised the text throughout the paper (lines 84-89, 176-180) to contextualize and emphasize this distinction. We have also added a reference for the Structural Genomics Consortium, which, along with resources like IDG, has provided significant resources for prioritizing understudied proteins.

(5) Since the authors have generated the UMAP visualization of the channome, it would be interesting to understand how the human vs orthologue gene sets compare in this space.

We appreciate the reviewer’s input. It is an interesting idea to explore the UMAP embedding space for the human ICs along with their orthologs. The large number of orthologous sequences (>37,000) would certainly impose a computational challenge to generate embeddings-based pairwise alignments across all of them. Downstream dimensionality reduction from such a large set and the subsequent visualization would also suffer from accuracy and interpretability concerns. However, to follow up on the reviewer’s comments, we selected orthologous sequences from a subset of 12 model organisms spanning all taxa (such as mouse, zebrafish, fruit fly, C. elegans, A. thaliana, S. cerevisiae, E. coli, etc.).This increased the number of sequences for analysis to 1094 from 343, which is still manageable for UMAP. Using the exact same method, we generated the UMAP embeddings plot for this set as shown below. 

Author response image 1.

UMAP embeddings of the human ICs alongside orthologs from 12 model organisms

As shown above, we observed that each orthologous set forms tight, well-defined clusters, preserving local relationships among closely related sequences. For example, a large number of VGICs cluster more closely together compared to Supplementary Figure 1 (with only the human ICs). However, families that were previously distant from others now appear to be even more scattered or pushed further away, indicating a loss of global structure. This pattern suggests that while local distances are well preserved, the global topology of the embedding space could be compromised. Moreover, we find that the placement of ICs with respect to other families is highly sensitive to the parameter choices (e.g., n_neighbors and min_dist), an issue which we did not encounter when using only the human IC sequences. The inclusion of a large number of orthologous sequences that are highly similar to a single human IC but dissimilar to others skews the embedding space, emphasizing local structure at the expense of global relationships.

Since UMAP and similar dimensionality reduction methods prioritize local over global structure, the resulting embeddings accurately reflect strong ortholog clustering but obscure broader interfamily relationships. Consequently, interpreting the spatial arrangement of human IC families with respect to one another becomes unreliable. We have made this plot available as part of this response, and anyone interested can access this in the response document.   

(6) Figure 1 should say more clearly that this is an analysis of the human gene set and include more of the information in the text: 419 human ion channel sequences, 75 sequences previously unidentified, 4 major groups and 55 families, 62 outliers, etc. Clearer visualizations of these categories and numbers within the UMAP (and newly included tree) visualization would help guide the reader to better understand these results. Specifically, which are the 75 previously unidentified sequences?

We thank the reviewer for the comments. To address this, we have revised Figure 1 and added more information, including a clear header that states that these are only human IC sets, numbers showing the total number of ICs, and the number of ICs in each group. We have further included new Supplementary Figure 2 and Supplementary Table 2, which show the overlap of IC sequences across the different resources. Supplementary Figure 2 is an upset plot that provides a snapshot of the overlap between curated human ICs in this study compared to KEGG, GtoP, and Pharos. Supplementary Table 2 provides more details on this overlap by listing, for each human IC, whether they are curated as an IC in the 3 IC annotation resources. We believe these additions should provide all the information, including the unidentified sequences we are adding to this resource.

(7) Overall, the manuscript needs to provide a clearer description of the need for a better-curated sequence database of ion channels, as well as how existing resources fall short.

We thank the reviewer for pointing out this important gap in the description. As suggested, we have revised the text thoroughly in the Introduction section to address this comment. Specifically, we have added sections to describe existing resources at sequence and structure levels that currently provide details and/or classification of human ion channels. Then, we highlight the facts that these resources are missing some characterized pore-containing ICs, do not include any information on auxiliary channels, and lack a holistic evolutionary perspective, which raises the need for a better-curated database of ion channels. Please refer to lines 57-63, 73-79, and 95 – 119 for these changes and additions.

(8) Some of the analysis pipeline is unclear. Specifically, the RAG analysis seems critical, but it is unclear how this works - is it on top of the GPT framework and recursively inquires about the answer to prompts? Some example prompts would be useful to understand this.

We thank the reviewer for highlighting this gap in explanation. We understand that the details provided in the Methods and Supplementary Figure 1 may not have sufficiently explained the pipeline, and are missing some important details. The RAG pipeline leverages vector-based retrieval integrated with OpenAI’s GPT-4o model to systematically search literature and generate evidence-based answers. The process is as follows:

Literature sources (PubMed articles) relevant to the annotated ion channels were converted into vector representations stored in a Qdrant database.

Queries constructed from the annotated IC dataset were submitted to the vector database, retrieving contextually relevant literature segments.

Retrieved contexts served as inputs to the GPT-4o model, which produced structured JSON-formatted responses containing direct evidence regarding ion selectivity and gating mechanisms, along with associated confidence scores.

To clarify this further, we have rewritten the relevant subsection in lines 649 - 718. Now, this section provides a detailed description of the RAG pipeline. Also, we have improved Supplementary Figure 1 to provide a clearer description of the pipeline. We have also provided an example prompt template to illustrate the query. These additions clarify how the pipeline functions and demonstrate its practical utility for IC annotation.

(9) The existence of 76 auxiliary non-pore containing 'ion channel' genes in this analysis is a little confusing, as it seems a part of the pipeline is looking for pore-lining residues. Furthermore, how many of these are picked up in the larger orthologues search? Are these harder to perform checks on to ensure that they are indeed ion channel genes? A further discussion of the choice to include these auxiliary sequences would be relevant. This could just be further discussion of the literature that has decided to do this in the past.

We thank the reviewer for this comment, and agree that further clarification of our selection and definition of auxiliary IC sequences would be helpful. As the reviewer has pointed out, one of the annotation pipeline steps is indeed looking for the pore-lining residues. Any sequences that do not have a pore-containing domain are then considered to be auxiliary, and we search for additional evidence of their binding with one of the annotated pore-containing ICs. If such evidence is not found in the literature, we remove them from our curated IC list. 

In response to the above comment, we have revised the manuscript text to provide these details. In the Introduction section, we have added references to previous literature that have described auxiliary ICs and also pointed out that the existing ion channel resources do not account for such auxiliary channels (lines 73-79, 107-108,148-149). We have also expanded the Methods section to describe the selection and definition of auxiliary channels (lines 640-646).

With regards to the orthology analysis, since auxiliary channels do not have a pore domain, and our orthology pipeline requires a pore domain similarity search and hit, we did not include them in this part of the analysis. We have clarified the text in the Results section to ensure this is communicated properly throughout the manuscript (lines 212-215, 260-263). 

(10) Why are only evolutionary relationships between rat, mouse, and human shown in Figure 3A? These species are all close on the evolutionary timeline.

We thank the reviewer for this comment. Figure 3A currently provides a high-level evolutionary relationship across the 6 human CALHM members as a pretext for the pattern based Bayesian analysis. However, since this analysis is based on a wider set of orthologs that span taxa, we agree that a larger tree that includes more orthologs is warranted.

We have now revised Figure 3A to include an expanded tree that includes 83 orthologs from all 6 human CALHM members spanning 14 organisms from different taxa, ranging from mammals, fishes, birds, nematodes, and cnidarians. The overall structure of the tree is still consistent with 2 major clades as before, with CALHM 1 and 3 in the first clade and CALHM 2,4,5, and 6 in the second clade, with good branch support.

(B) Revisions related to the second part, regarding the analysis of CAHLM channel mutations:

(1) It would strengthen the manuscript if it included additional discussion and references to show that previous methods to analyze conserved residues in CALHM were significantly lacking. What results would previous methods give, and why was this not enough? Were there just not enough identified CALHM orthologues to give strong signals in conservation analysis? Also, the amino acid conservation between CLHM-1 and CALHM1 is extremely low. Thus, there are other CALHM orthologs that give strong signals in conservation analysis. There are ~6 papers that perform in-depth analysis of the role of conserved residues in the gating of CALHM channels (human and C. elegans) that were not cited (Ma et al, Am J Physiol Cell Physiol, 2025; Syrjanen et al, Nat Commun, 2023; Danielli et al, EMBO J, 2023; Kwon et al, Mol Cells, 2021; Tanis et al, Am J Physiol Cell Physiol, 2017; Tanis et al, J Neurosci, 2013; Ma et al, PNAS, 2013) - these data needs to be discussed in the context of the present work.

We thank the reviewer for the comment and agree that these are excellent studies that have advanced understanding of conserved residues in CALHM gating. While their analyses compared a limited set of sequences, focusing on residues conserved in specific CALHM homologs or species like C. elegans, our analysis encompasses thousands of sequences across the entire CALHM family, allowing us to identify residues conserved across all family members over evolution. We also coupled this sequence analysis with hypotheses derived from our published structural studies (Choi et al., Nature, 2019), which highlighted the NTH/S1 region as a critical element in channel gating. Based on this, we focused on evolutionarily conserved residues in the S1–S2 linker and at the interface of S1 with the rest of the TMD, reasoning that if S1 movement is essential for gating, these two structural elements (acting as a hinge and stabilizing interface, respectively) would be key determinants of the conformational dynamics of S1. These regions have been largely overlooked in previous studies. As a result, the residues highlighted in our study do not overlap with those previously reported but instead provide complementary insights into gating mechanisms in this unique channel family. Together, our study and the published literature suggest that many regions and residues in CALHM proteins are critical for gating: while some are conserved across the entire family evolutionarily, others appear conserved only within certain species or subfamilies.

To address the reviewer’s comment, and to highlight the points mentioned above, we have added a brief discussion of these studies and the relevant citations in the revised manuscript (lines 378– 385, 563–576).

(2) Whereas the current-voltage relations for WT channels are clearly displayed, the data that is shown for the mutants does not allow for determining if their gating properties are indeed different than WT.

First, the current amplitudes for the mutants were quantified at just one voltage, which makes it impossible to determine if their voltage-dependence was different than WT, which would be a strong indicator for an effect in gating. Current-voltage relations as done for the WT channels should be included for at least some key mutations, which should include additional relevant controls like the use of Gd3+ as an inhibitor to rule out the contribution of some endogenous currents.

We thank the reviewer for this comment. To address this, we performed additional experiments using a multi-step pulse protocol to obtain current-voltage relations for WT CALHM1, CALHM1(I109W), WT CALHM6, and CALHM6(W113A). Our initial two-step protocol (−80 mV and +120 mV) covers both the physiological voltage range and the extended range commonly used in biophysical characterization of ion channels. Most mutants did not exhibit channel activation even within this broad range. We therefore focused on the three mutants that did show substantial activation to perform full I–V analysis as suggested. In all groups, currents activated at 37 °C were significantly inhibited by Gd³⁺, consistent with published reports (Ma et al., AJP 2025; Danielli et al., EMBO J 2023; Syrjänen et al., Nat Commun 2023). Notably, for CALHM6(Y51A), while this mutation did not significantly alter current amplitudes at positive membrane potentials, it markedly reduced currents at negative potentials, rendering the channel outwardly rectifying and altering its voltage dependence. These new data are incorporated into Figure 5 (panels A–O) and discussed in the manuscript. Figure 5 now also shows current amplitudes at both +120 mV and −80 mV in 0 mM Ca²⁺ at 37 °C to facilitate direct comparison between WT and mutants. The previous data at 5 mM Ca²⁺ and 0 mM Ca²⁺ at 22 °C have been moved to Supplementary Figure 5 as requested.

Second, it is unclear whether the three experimental conditions (5 mM Ca²⁺, and 0 Ca²⁺, at 22 and 37C) were measured in the same cell in each experiment, or if they represent different experiments. This should be clarified. If measurements at each condition were done in the same experiment, direct comparison between the three conditions within each individual experiment could further help identify mutations with altered gating.

We thank the reviewer for pointing this out and apologize for the confusion. All three conditions (5 mM Ca²⁺ at 22 °C, 0 mM Ca²⁺ at 22 °C, and 0 mM Ca²⁺ at 37 °C) were sequentially measured in the same cell within each experiment. The currents were then averaged across cells and plotted for each group.

Third, in line 334, the authors state that "expression levels of wild-type proteins and mutants are comparable." However, Western blots showing CALHM protein abundance (Supplementary Fig. 3) are not of acceptable quality; in the top blot, WT CALHM1 appears too dim, representative blots were not shown for all mutants, and individual data points should be included on the group data quantitation of the blots, together with a statistical test comparing mutants with the WT control.

We thank the reviewer for the comment and agree that representative blots were not shown for all mutants. Supplementary Figure 4 (previously Supplementary Figure 3) has been updated to include representative blots for all mutants, individual data points in the quantification, and statistical tests comparing each mutant to the WT control.

A more serious concern is that the total protein quantitation is not very informative about the functional impact of mutations in ion channels, because mutations can severely impact channel localization in the plasma membrane without reducing the total protein that is translated. In mammalian cells, CALHM6 is localized to intracellular compartments and only translocates to the plasma membrane in response to an activating stimulus (Danielli et al, EMBO J, 2023). Thus, if CALHM6 is only intracellular, the protein amount would not change, but the measured current would. Abundant intracellular CALHM1 has also been observed in mammalian cells transfected with this protein (Dreses-Werringloer et al., Cell, 2008). Quantitation of surface-biotinylated channels would provide information on whether there are differences between the constructs in relation to surface expression rather than gating. An alternative approach to biotinylation would be to express GFP-tagged constructs in Xenopus oocytes and look for surface expression. This is what has been done in previous CALHM channel studies.

Without evidence for the absence of defects in localization or clear alterations in gating properties, it is not possible to conclude whether mutant channels have altered activity. Does the analysis of sequences provide any testable hypotheses about substitutions with different side chains at the same position in the sequence?

We thank the reviewer for this very important comment. We agree that total protein levels alone do not distinguish between intracellular retention and proper trafficking to the plasma membrane. To address this, we performed surface biotinylation assays for all WT and mutant CALHM1 and CALHM6 constructs to assess their plasma membrane localization. The results show that mutants have either comparable or substantially higher surface expression levels than WT, consistent with the Western blot data. Together, these findings support our original interpretation that the observed differences in electrophysiological currents are not due to trafficking defects but reflect functional effects. These new data are presented in Supplementary Figure 5.

(3) Line 303 - 13 aligned amino acids were conserved across all CALHM homologs - are these also aligned in related connexin and pannexin families? It is likely that cysteines and proline in TM2 are since CALHM channels overall share a lot of similarities with connexins and pannexins (Siebert et al, JBC, 2013). As in line 207, it would be expected that pannexins, connexins, and CALHM channel families would group together. Related to this, see Line 406 - in connexins, there is also a proline kink in TM2 that may play a role in mediating conformational changes between channel states (Ri et al, Biophysical Journal, 1999). This should be discussed.

We thank the reviewer for the suggestion. We attempted a structure based sequence alignment of representative structures from all 3 families (CALHM, connexins and pannexins), but the resulting alignments are very poor and have a lot of gapped regions, making it very difficult to comment on the similarities mentioned in this comment. This is actually expected, as although CALHM, connexins, and pannexins are all considered “large-pore” channels, the TMD arrangement and conformation of CALHM are distinct from those of connexins and pannexins. Below, we have included a snapshot of the alignment at the conserved cysteine regions of the CALHM homologs, along with the resulting tree, which has very low support values and has difficulty placing the connexins properly, making it difficult to interpret.

Author response image 2.

Structure based sequence alignment and phylogenetic analysis of available crystal structures of members from the CALHM, Pannexin and Connexin families. Top: The resulting sequence alignment is very sparse and does not show conservation of residues in the TM regions. The CPC motif with conserved cysteines in CALHM family is shown. Bottom: Phylogenetic tree based on the alignment has low support values making it difficult to interpret.

(4) Line 36 - This work does not have experimental evidence to show that the selected evolutionarily conserved residues alter gating functions.

Our electrophysiology data demonstrate that the selected evolutionarily conserved residues have a major impact on CALHM1 and CALHM6 gating. As shown in Figure 5, mutations at these residues produce two distinct phenotypes: (1) nonconductive channels, and (2) altered voltage dependence, resulting in outward rectification. Importantly, these functional changes occur despite normal total expression and surface trafficking, as confirmed by Western blotting and surface biotinylation (Supplementary Figure 4). These findings indicate that the affected residues are critical for the conformational dynamics underlying channel gating rather than for protein expression or localization.

(5) Line 296-297 - This could also be put in the context of what we already know about CALHM gating. While all cryo EM structures of CALHM channels are in the open state, we still do understand some things about gating mechanism (Tanis et al Am J Physiol Cell Physiol, Cell Physiol 2017; Ma et al Am J Physiol Cell Physiol, Cell Physiol 2025) with the NT modulating voltage dependence and stabilizing closed channel states and the voltage dependent gate being formed by proximal regions of TM1.

Thank you for providing this suggestion. As suggested, we have revised the text to place our findings in the context of current knowledge about CALHM gating and have added the relevant citations (lines 370-373).

(6) Lines 314-315 - Just because residues are conserved does not mean that they play a role in channel gating. These residues could also be important for structure, ion selectivity, etc.

We agree that evolutionary conservation alone does not imply a role in gating. However, our hypothesis derives from the positioning of these conserved residues, and previous studies that have indicated the importance of the NTH/S1 region for channel gating function. More importantly, our electrophysiology data indicate that these conserved residues specifically impact channel gating in CALHM1 and CALHM6. We have revised the text in lines 404-406 to clarify this further.

(7) Line 333 - while CALHM6 is less studied than CALHM1, there is knowledge of its function and gating properties. Should CALHM6 be considered a "dark" channel? The IDG development level in Pharos is Tbio. There have been multiple papers published on this channel (ex: Ebihara et al, J Exp Med, 2010; Kasamatsu et al, J Immunol 2014; Danielli et al, EMBO J, 2023).

We thank the reviewer for noting this important discrepancy. We have updated the text and labels related to CALHM6 to reflect its status as Tbio in the manuscript.

(8) Please cite Jeon et al., (Biochem Biophys Res Commun, 2021), who have already shown temperature-dependence of CALHM1.

Thank you for the comment. We have added the citation.  

(9) It would be helpful to have a schematic showing amino acid residues, TM domains, highlighted residues mutated, etc.

Thank you for the suggestion. We have revised the figure and added labels for the TM domains, and highlighted the mutated residues.

Reviewer #1 (Recommendations for the authors):

(1) Why in the title is 'ion-channels' hyphenated but in the text it is not?

This has been changed.

(2) Line 78: 'Cryo-EM' is not defined before the acronym is used.

This has been fixed.

(3) Typo in line 519: KinOrthto.

This has been fixed.

(4) Capitalizing 'Tree of Life' is a bit strange in section 2 of the results and the Discussion.

We have removed the capitalization as suggested.

(5) In Figure 3 and Supplementary Figure 4A, the gene names in the tree are CAHM and not CALHM - I assume this is an error.

This has been made consistent to CALHM.

(6) Font sizes throughout all figures, with the exception of Figure 1, need to be more legible. The X-axis labels in Figure 2A are hard to read, for example (though I can see that there is also the CAHM/CALHM typo here...). A good rule of thumb is that they should be the same size as the manuscript text. Furthermore, the grey backgrounds of Figure 4 and Figure 5 are off-putting; just having a white background here should be sufficient.

This has been addressed. We have increased the font size in all figures with these revisions. The styling for Figure 4 and 5 has also been made consistent with other figures.

Reviewer #2 (Recommendations for the authors):

(1) Line 36 - This work does not have experimental evidence to show that the selected evolutionarily conserved residues alter gating functions.

Addressed in comment #4 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(2) Line 168 - should also be Supplemental Table 1.

This has been addressed.

(3) Line 170 - 419 human ion channel sequences were identified and this was an increase of 75 sequences over previous number. Which 75 proteins are these?

This is now shown in Supplementary Figure 2 and Supplementary Table 2. Supplementary Figure 2 shows an Upset plot with the number of sequences that overlap across databases and the novel sequences that we have added as part of this study. The 75 specifically refers to the sequences that were not included in Pharos, which was chosen to refer to this number since it has the highest number of ICs listed out of all the other resources. Further, Supplementary Table 2 now provides a list of individual ICs and whether they were present in each of the 3 databases compared.

(4) Line 289 - Ca2+ (not Ca); other similar mistakes throughout the manuscript

These have been fixed.

(5) Line 291-292 - Please include more about functions for CALHM channels; ex. CALHM1 regulates cortical neuron excitability (Ma et al, PNAS 2012), CLHM-1 regulates locomotion and induces neurodegeneration in C. elegans (Tanis et al. Journal of Neuroscience 2013); see above for references on CALHM6 function.

We have added the functions as suggested.

(6) Line 296-297 - This could also be put in the context of what we already know about CALHM gating. While all cryo EM structures of CALHM channels are in the open state, we still do understand some things about gating mechanism (Tanis et al Am J Physiol Cell Physiol, Cell Physiol 2017; Ma et al Am J Physiol Cell Physiol, Cell Physiol 2025) with the NT modulating voltage dependence and stabilizing closed channel states and the voltage dependent gate being formed by proximal regions of TM1.

Addressed in comment #5 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(7) Lines 314-315 - Just because residues are conserved does not mean that they play a role in channel gating. These residues could also be important for structure, ion selectivity, etc.

Addressed in comment #6 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(8) Line 333 - While CALHM6 is less studied than CALHM1, there is knowledge of its function and gating properties. Should CALHM6 be considered a "dark" channel? The IDG development level in Pharos is Tbio. There have been multiple papers published on this channel (ex: Ebihara et al, J Exp Med, 2010; Kasamatsu et al, J Immunol 2014; Danielli et al, EMBO J, 2023).

Addressed in comment #7 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(9) Line 627 - Do you mean that 5 mM CaCl2 was replaced with 5 mM EGTA in 0 Ca2+ solution?

This is correct.  

(10) Why are only evolutionary relationships between rat, mouse, and human shown in Figure 3A? These species are all close on the evolutionary timeline.

Addressed in comment #10 for Part A Revisions related to the first part, regarding data mining and curation above.

(11) Figure 5 - no need to show the currents at room temperature in the main text since there are robust currents at 37 degrees; this could go into the supplement. Also, please cite Jeon et al. (Biochem Biophys Res Commun, 2021), who have already shown temperature-dependence of CALHM1.

Addressed in comment #8 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(12) It would be helpful to have a schematic showing amino acid residues, TM domains, highlighted residues mutated etc.

Addressed in comment #9 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(13) Use of S1-S4 to refer to the transmembrane "segments" is not standard; rather, TM1-TM4 would generally be used to refer to transmembrane domains.

We have used the S1–S4 helix notation to maintain consistency with the nomenclature employed in our previous study (Choi et al., Nature, 2019).

Author Response:

Reviewer #1 (Public Review):

[...] The major limitation of the manuscript lies in the framing and interpretation of the results, and therefore the evaluation of novelty. Authors claim for an important and unique role of beliefs-of-other-pain in altruistic behavior and empathy for pain. The problem is that these experiments mainly show that behaviors sometimes associated with empathy-for-pain can be cognitively modulated by changing prior beliefs. To support the notion that effects are indeed relating to pain processing generally or empathy for pain specifically, a similar manipulation, done for instance on beliefs about the happiness of others, before recording behavioural estimation of other people's happiness, should have been performed. If such a belief-about-something-else-than-pain would have led to similar results, in terms of behavioural outcome and in terms of TPJ and MFG recapitulating the pattern of behavioral responses, we would know that the results reflect changes of beliefs more generally. Only if the results are specific to a pain-empathy task, would there be evidence to associate the results to pain specifically. But even then, it would remain unclear whether the effects truly relate to empathy for pain, or whether they may reflect other routes of processing pain.

We thank Reviewer #1's for these comments/suggestions regarding the specificity of belief effects on brain activity involved in empathy for pain. Our paper reported 6 behavioral/EEG/fMRI experiments that tested effects of beliefs of others’ pain on empathy and monetary donation (an empathy-related altruistic behavior). We showed not only behavioral but also neuroimaging results that consistently support the hypothesis of the functional role of beliefs of others' pain in modulations of empathy (based on both subjective and objective measures as clarified in the revision) and altruistic behavior. We agree with Reviewer 1# that it is important to address whether the belief effect is specific to neural underpinnings of empathy for pain or is general for neural responses to various facial expressions such as happy, as suggested by Reviewer #1. To address this issue, we conducted an additional EEG experiment (which can be done in a limited time in the current situation), as suggested by Reviewer #1. This new EEG experiment tested (1) whether beliefs of authenticity of others’ happiness influence brain responses to perceived happy expressions; (2) whether beliefs of happiness modulate neural responses to happy expressions in the P2 time window as that characterized effects of beliefs of pain on ERPs.

Our behavioral results in this experiment (as Supplementary Experiment 1 reported in the revision) showed that the participants reported less feelings of happiness when viewing actors who simulate others' smiling compared to when viewing awardees who smile due to winning awards (see the figure below). Our ERP results in Supplementary Experiment 1 further showed that lack of beliefs of authenticity of others’ happiness (e.g., actors simulate others' happy expressions vs. awardees smile and show happy expressions due to winning an award) reduced the amplitudes of a long-latency positive component (i.e., P570) over the frontal region in response to happy expressions. These findings suggest that (1) there are possibly general belief effects on subjective feelings and brain activities in response to facial expressions; (2) beliefs of others' pain or happiness affect neural responses to facial expressions in different time windows after face onset; (3) modulations of the P2 amplitude by beliefs of pain may not be generalized to belief effects on neural responses to any emotional states of others. We reported the results of this new ERP experiment in the revision as Supplementary Experiment 1 and also discussed the issue of specificity of modulations of empathic neural responses by beliefs of others' pain in the revised Discussion (page 49-50).

Supplementary Experiment Figure 1. EEG results of Supplementary Experiment 1. (a) Mean rating scores of happy intensity related to happy and neutral expressions of faces with awardee or actor/actress identities. (b) ERPs to faces with awardee or actor/actress identities at the frontal electrodes. The voltage topography shows the scalp distribution of the P570 amplitude with the maximum over the central/parietal region. (c) Mean differential P570 amplitudes to happy versus neutral expressions of faces with awardee or actor/actress identities. The voltage topographies illustrate the scalp distribution of the P570 difference waves to happy (vs. neutral) expressions of faces with awardee or actor/actress identities, respectively. Shown are group means (large dots), standard deviation (bars), measures of each individual participant (small dots), and distribution (violin shape) in (a) and (c).

In the revised Introduction we cited additional literatures to explain the concept of empathy, behavioral and neuroimaging measures of empathy, and how, similar to previous research, we studied empathy for others' pain using subjective (self reports) and objective (brain responses) estimation of empathy (page 6-7). In particular, we mentioned that subjective estimation of empathy for pain depends on collection of self-reports of others' pain and ones' own painful feelings when viewing others' suffering. Objective estimation of empathy for pain relies on recording of brain activities (using fMRI, EEG, etc.) that differentially respond to painful or non-painful stimuli applied to others. fMRI studies revealed greater activations in the ACC, AI, and sensorimotor cortices in response to painful or non-painful stimuli applied to others. EEG studies showed that event-related potentials (ERPs) in response to perceived painful stimulations applied to others' body parts elicited neural responses that differentiated between painful and neutral stimuli over the frontal region as early as 140 ms after stimulus onset (Fan and Han, 2008; see Coll, 2018 for review). Moreover, the mean ERP amplitudes at 140–180 ms predicted subjective reports of others' pain and ones' own unpleasantness. Particularly related to the current study, previous research showed that pain compared to neutral expressions increased the amplitude of the frontal P2 component at 128–188 ms after stimulus onset (Sheng and Han, 2012; Sheng et al., 2013; 2016; Han et al., 2016; Li and Han, 2019) and the P2 amplitudes in response to others' pain expressions positively predicted subjective feelings of own unpleasantness induced by others' pain and self-report of one's own empathy traits (e.g., Sheng and Han, 2012). These brain imaging findings indicate that brain responses to others' pain can (1) differentiate others' painful or non-painful emotional states to support understanding of others' pain and (2) predict subjective feelings of others' pain and one's own unpleasantness induced by others' pain to support sharing of others' painful feelings. These findings provide effective subjective and objective measures of empathy that were used in the current study to investigate neural mechanisms underlying modulation of empathy and altruism by beliefs of others’ pain.

In addition, we took Reviewer #1’s suggestion for VPS analyses which examined specifically how neural activities in the empathy-related regions identified in the previous research (Krishnan et al., 2016, eLife) were modulated by beliefs of others’ pain. The results (page 40) provide further evidence for our hypothesis. We also reported new results of RSA analyses(page 39) that activities in the brain regions supporting affective sharing (e.g., insula), sensorimotor resonance (e.g., post-central gyrus), and emotion regulation (e.g., lateral frontal cortex) provide intermediate mechanisms underlying modulations of subjective feelings of others' pain intensity due to lack of BOP. We believe that, putting all these results together, our paper provides consistent evidence that empathy and altruistic behavior are modulated by BOP.

Reviewer #2 (Public Review):

[...] 1. In laying out their hypotheses, the authors write, "The current work tested the hypothesis that BOP provides a fundamental cognitive basis of empathy and altruistic behavior by modulating brain activity in response to others' pain. Specifically, we tested predictions that weakening BOP inhibits altruistic behavior by decreasing empathy and its underlying brain activity whereas enhancing BOP may produce opposite effects on empathy and altruistic behavior." While I'm a little dubious regarding the enhancement effects (see below), a supporting assumption here seems to be that at baseline, we expect that painful expressions reflect real pain experience. To that end, it might be helpful to ground some of the introduction in what we know about the perception of painful expressions (e.g., how rapidly/automatically is pain detected, do we preferentially attend to pain vs. other emotions, etc.).

Thanks for this suggestion! We included additional details about previous findings related to processes of painful expressions in the revised Introduction (page 7-8). Specifically, we introduced fMRI and ERP studies of pain expressions that revealed structures and temporal procedure of neural responses to others' pain (vs. neutral) expressions. Moreover, neural responses to others' pain (vs. neutral) expressions were associated with self-report of others' feelings, indicating functional roles of pain-expression induced brain activities in empathy for pain.

1. For me, the key takeaway from this manuscript was that our assessment of and response to painful expressions is contextually-sensitive - specifically, to information reflecting whether or not targets are actually in pain. As the authors state it, "Our behavioral and neuroimaging results revealed critical functional roles of BOP in modulations of the perception-emotion-behavior reactivity by showing how BOP predicted and affected empathy/empathic brain activity and monetary donations. Our findings provide evidence that BOP constitutes a fundamental cognitive basis for empathy and altruistic behavior in humans." In other words, pain might be an incredibly socially salient signal, but it's still easily overridden from the top down provided relevant contextual information - you won't empathize with something that isn't there. While I think this hypothesis is well-supported by the data, it's also backed by a pretty healthy literature on contextual influences on pain judgments (including in clinical contexts) that I think the authors might want to consider referencing (here are just a few that come to mind: Craig et al., 2010; Twigg et al., 2015; Nicolardi et al., 2020; Martel et al., 2008; Riva et al., 2015; Hampton et al., 2018; Prkachin & Rocha, 2010; Cui et al., 2016).

Thanks for this great suggestion! Accordingly, we included an additional paragraph in the revised Discussion regarding how social contexts influence empathy and cited the studies mentioned here (page 46-47).

1. I had a few questions regarding the stimuli the authors used across these experiments. First, just to confirm, these targets were posing (e.g., not experiencing) pain, correct? Second, the authors refer to counterbalancing assignment of these stimuli to condition within the various experiments. Was target gender balanced across groups in this counterbalancing scheme? (e.g., in Experiment 1, if 8 targets were revealed to be actors/actresses in Round 2, were 4 female and 4 male?) Third, were these stimuli selected at random from a larger set, or based on specific criteria (e.g., normed ratings of intensity, believability, specificity of expression, etc.?) If so, it would be helpful to provide these details for each experiment.

We'd be happy to clarify these questions. First, photos of faces with pain or neutral expressions were adopted from the previous work (Sheng and Han, 2012). Photos were taken from models who were posing but not experience pain. These photos were taken and selected based on explicit criteria of painful expressions (i.e., brow lowering, orbit tightening, and raising of the upper lip; Prkachin, 1992). In addition, the models' facial expressions were validated in independent samples of participants (see Sheng and Han, 2012). Second, target gender was also balanced across groups in this counterbalancing scheme. We also analyzed empathy rating score and monetary donations related to male and female target faces and did not find any significant gender effect (see our response to Point 5 below). Third, because the face stimuli were adopted from the previous work and the models' facial expressions were validated in independent samples of participants regarding specificity of expression, pain intensity, etc (Sheng and Han, 2012), we did not repeat these validation in our participants. Most importantly, we counterbalanced the stimuli in different conditions so that the stimuli in different conditions (e.g., patient vs. actor/actress conditions) were the same across the participants in each experiment. The design like this excluded any potential confound arising from the stimuli themselves.

1. The nature of the charitable donation (particularly in Experiment 1) could be clarified. I couldn't tell if the same charity was being referenced in Rounds 1 and 2, and if there were multiple charities in Round 2 (one for the patients and one for the actors).

Thanks for this comment! Yes, indeed, in both Rounds 1 and 2, the participants were informed that the amount of one of their decisions would be selected randomly and donated to one of the patients through the same charity organization (we clarified these in the revised Method section, page 55-56). We made clear in the revision that after we finished all the experiments of this study, the total amount of the participants' donations were subject to a charity organization to help patients who suffer from the same disease after the study.

1. I'm also having a hard time understanding the authors' prediction that targets revealed to truly be patients in the 2nd round will be associated with enhanced BOP/altruism/etc. (as they state it: "By contrast, reconfirming patient identities enhanced the coupling between perceived pain expressions of faces and the painful emotional states of face owners and thus increased BOP.") They aren't in any additional pain than they were before, and at the outset of the task, there was no reason to believe that they weren't suffering from this painful condition - therefore I don't see why a second mention of their pain status should increase empathy/giving/etc. It seems likely that this is a contrast effect driven by the actor/actress targets. See the Recommendations for the Authors for specific suggestions regarding potential control experiments. (I'll note that the enhancement effect in Experiment 2 seems more sensible - here, the participant learns that treatment was ineffective, which may be painful in and of itself.)

Thanks for comments on this important point! Indeed, our results showed that reassuring patient identities in Experiment 1 or by noting the failure of medical treatment related to target faces in Experiment 2 increased rating scores of others' pain and own unpleasantness and prompted more monetary donations to target faces. The increased empathy rating scores and monetary donations might be due to that repeatedly confirming patient identity or knowing the failure of medical treatment increased the belief of authenticity of targets' pain and thus enhanced empathy. However, repeatedly confirming patient identity or knowing the failure of medical treatment might activate other emotional responses to target faces such as pity or helplessness, which might also influence altruistic decisions. We agree with Reviewer #2 that, although our subjective estimation of empathy in Exp. 1 and 2 suggested enhanced empathy in the 2nd_round test, there are alternative interpretations of the results and these should be clarified in future work. We clarified these points in the revised Discussion (page 41-42).

1. I noted that in the Methods for Experiment 3, the authors stated "We recruited only male participants to exclude potential effects of gender difference in empathic neural responses." This approach continues through the rest of the studies. This raises a few questions. Are there gender differences in the first two studies (which recruited both male and female participants)? Moreover, are the authors not concerned about target gender effects? (Since, as far as I can tell, all studies use both male and female targets, which would mean that in Experiments 3 and on, half the targets are same-gender as the participants and the other half are other-gender.) Other work suggests that there are indeed effects of target gender on the recognition of painful expressions (Riva et al., 2011).

Thanks for raising this interesting question! Therefore, we reanalyzed data in Exp. 1 by including participants' gender or face gender as an independent variable. The three-way ANOVAs of pain intensity scores and amounts of monetary donations with Face Gender (female vs. male targets) × Test Phase (1st vs. 2nd_round) × Belief Change (patient-identity change vs. patient-identity repetition) did not show any significant three-way interaction (F(1,59) = 0.432 and 0.436, p = 0.514 and 0.512, ηp2 = 0.007 and 0.007, 90% CI = (0, 0.079) and (0, 0.079), indicating that face gender do not influence the results (see the figure below). Similarly, the three-way ANOVAs with Participant Gender (female vs. male participants) × Test Phase × Belief Change did not show any significant three-way interaction (F(1,58) = 0.121 and 1.586, p = 0.729 and 0.213, ηp2 = 0.002 and 0.027, 90% CI = (0, 0.055) and (0, 0.124), indicating no reliable difference in empathy and donation between men and women. It seems that the measures of empathy and altruistic behavior in our study were not sensitive to gender of empathy targets and participants' sexes.

Figure legend: (a) Scores of pain intensity and amount of monetary donations are reported separately for male and female target faces. (b) Scores of pain intensity and amount of monetary donations are reported separately for male and female participants.

1. I was a little unclear on the motivation for Experiment 4. The authors state "If BOP rather than other processes was necessary for the modulation of empathic neural responses in Experiment 3, the same manipulation procedure to assign different face identities that do not change BOP should change the P2 amplitudes in response to pain expressions." What "other processes" are they referring to? As far as I could tell, the upshot of this study was just to demonstrate that differences in empathy for pain were not a mere consequence of assignment to social groups (e.g., the groups must have some relevance for pain experience). While the data are clear and as predicted, I'm not sure this was an alternate hypothesis that I would have suggested or that needs disconfirming.

Thanks for this comment! We feel sorry for not being able to make clear the research question in Exp. 4. In the revised Results section (page 27-28) we clarified that the learning and EEG recording procedures in Experiment 3 consisted of multiple processes, including learning, memory, identity recognition, assignment to social groups, etc. The results of Experiment 3 left an open question of whether these processes, even without BOP changes induced through these processes, would be sufficient to result in modulation of the P2 amplitude in response to pain (vs. neutral) expressions of faces with different identities. In Experiment 4 we addressed this issue using the same learning and identity recognition procedures as those in Experiment 3 except that the participants in Experiment 4 had to learn and recognize identities of faces of two baseball teams and that there is no prior difference in BOP associated with faces of beliefs of the two baseball teams. If the processes involved in the learn and reorganization procedures rather than the difference in BOP were sufficient for modulation of the P2 amplitude in response to pain (vs. neutral) expressions of faces, we would expect similar P2 modulations in Experiments 4 and 3. Otherwise, the difference in BOP produced during the learning procedure was necessary for the modulation of empathic neural responses, we would not expect modulations of the P2 amplitude in response to pain (vs. neutral) expressions in Experiment 4. We believe that the goal and rationale of Exp. 4 are clear now.

Author Response:

We thank the editors and the reviewers for their careful reading and rigorous evaluation of our manuscript. We thank them for their positive comments and constructive feedback, which led us to add further lines of evidence in support of our central hypothesis that intrinsic neuronal resonance could stabilize heterogeneous grid-cell networks through targeted suppression of low-frequency perturbations. In the revised manuscript, we have added a physiologically rooted mechanistic model for intrinsic neuronal resonance, introduced through a slow negative feedback loop. We show that stabilization of patterned neural activity in a heterogeneous continuous attractor network (CAN) model could be achieved with this resonating neuronal model. These new results establish the generality of the stabilizing role of neuronal resonance in a manner independent of how resonance was introduced. More importantly, by specifically manipulating the feedback time constant in the neural dynamics, we establish the critical role of the slow kinetics of the negative feedback loop in stabilizing network function. These results provide additional direct lines of evidence for our hypothesis on the stabilizing role of resonance in the CAN model employed here. Intuitively, we envisage intrinsic neuronal resonance as a specific cellular-scale instance of a negative feedback loop. The negative feedback loop is a well-established network motif that acts as a stabilizing agent and suppresses the impact of internal and external perturbations in engineering applications and biological networks.

Reviewer #1 (Public Review):

The authors succeed in conveying a clear and concise description of how intrinsic heterogeneity affects continuous attractor models. The main claim, namely that resonant neurons could stabilize grid-cell patterns in medial entorhinal cortex, is striking.

We thank the reviewer for their time and effort in evaluating our manuscript, and for their rigorous evaluation and positive comments on our study.

I am intrigued by the use of a nonlinear filter composed of the product of s with its temporal derivative raised to an exponent. Why this particular choice? Or, to be more specific, would a linear bandpass filter not have served the same purpose?

Please note that the exponent was merely a mechanism to effectively tune the resonance frequency of the resonating neuron. In the revised manuscript, we have introduced a new physiologically rooted means to introduce intrinsic neuronal resonance, thereby confirming that network stabilization achieved was independent of the formulation employed to achieve resonance.

The magnitude spectra are subtracted and then normalized by a sum. I have slight misgivings about the normalization, but I am more worried that, as no specific formula is given, some MATLAB function has been used. What bothers me a bit is that, depending on how the spectrogram/periodogram is computed (in particular, averaged over windows), one would naturally expect lower frequency components to be more variable. But this excess variability at low frequencies is a major point in the paper.

We have now provided the specific formula employed for normalization as equation (16) of the revised manuscript. We have also noted that this was performed to account for potential differences in the maximum value of the homogeneous vs. heterogeneous spectra. The details are provided in the Methods subsection “Quantitative analysis of grid cell temporal activity in the spectral domain” of the revised manuscript. Please note that what is computed is the spectra of the entire activity pattern, and not a periodogram or a scalogram. There was no tiling of the time-frequency plane involved, thus eliminating potential roles of variables there on the computation here.

In addition to using variances of normalized differences to quantify spectral distributions, we have also independently employed octave-based analyses (which doesn’t involve normalized differences) to strengthen our claims about the impact of heterogeneities and resonance on different bands of frequency. These octave-based analyses also confirm our conclusions on the impact of heterogeneities and neuronal resonance on low-frequency components.

Finally, we would like to emphasize that spectral computations are the same for different networks, with networks designed in such a way that there was only one component that was different. For instance, in introducing heterogeneities, all other parameters of the network (the specific trajectory, the seed values, the neural and network parameters, the connectivity, etc.) remained exactly the same with the only difference introduced being confined to the heterogeneities. Computation of the spectral properties followed identical procedures with activity from individual neurons in the two networks, and comparison was with reference to identically placed neurons in the two networks. Together, based on the several routes to quantifying spectral signatures, based on the experimental design involved, and based on the absence of any signal-specific tiling of the time-frequency plane, we argue that the impact of heterogeneities or the resonators on low-frequency components is not an artifact of the analysis procedures.

We thank the reviewer for raising this issue, as it helped us to elaborate on the analysis procedures employed in our study.

Which brings me to the main thesis of the manuscript: given the observation of how heterogeneities increase the variability in the low temporal frequency components, the way resonant neurons stabilize grid patterns is by suppressing these same low frequency components.

I am not entirely convinced that the observed correlation implies causality. The low temporal frequeny spectra are an indirect reflection of the regularity or irregularity of the pattern formation on the network, induced by the fact that there is velocity coupling to the input and hence dynamics on the network. Heterogeneities will distort the pattern on the network, that is true, but it isn't clear how introducing a bandpass property in temporal frequency space affects spatial stability causally.

Put it this way: imagine all neurons were true oscillators, only capable of oscillating at 8 Hz. If they were to synchronize within a bump, one will have the field blinking on and off. Nothing wrong with that, and it might be that such oscillatory pattern formation on the network might be more stable than non-oscillatory pattern formation (perhaps one could even demonstrate this mathematically, for equivalent parameter settings), but this kind of causality is not what is shown in the manuscript.

The central hypothesis of our study was that intrinsic neuronal resonance could stabilize heterogeneous grid-cell networksthrough targeted suppression of low-frequency perturbations.

In the revised manuscript, we present the following lines of evidence in support of this hypothesis (mentioned now in the first paragraph of the discussion section of the revised manuscript):

1. Neural-circuit heterogeneities destabilized grid-patterned activity generation in a 2D CAN model (Figures 2–3).

2. Neural-circuit heterogeneities predominantly introduced perturbations in the lowfrequency components of neural activity (Figure 4).

3. Targeted suppression of low-frequency components through phenomenological (Figure 5C) or through mechanistic (new Figure 9D) resonators resulted in stabilization of the heterogeneous CAN models (Figure 8 and new Figure 11). We note that the stabilization was achieved irrespective of the means employed to suppress low-frequency components: an activity-independent suppression of low-frequencies (Figure 5) or an activity-dependent slow negative feedback loop (new Figure 9).

4. Changing the feedback time constant τm in mechanistic resonators, without changes to neural gain or the feedback strength allowed us to control the specific range of frequencies that would be suppressed. Our analyses showed that a slow negative feedback loop, which results in targeted suppression of low-frequency components, was essential in stabilizing grid-patterned activity (new Figure 12). As the slow negative feedback loop and the resultant suppression of low frequencies mediates intrinsic resonance, these analyses provide important lines of evidence for the role of targeted suppression of low frequencies in stabilizing grid patterned activity.

5. We demonstrate that the incorporation of phenomenological (Figure 13A–C) or mechanistic (new Figure panels 13D–F) resonators specifically suppressed lower frequencies of activity in the 2D CAN model.

6. Finally, the incorporation of resonance through a negative feedback loop allowed us to link our analyses to the well-established role of network motifs involving negative feedback loops in inducing stability and suppressing external/internal noise in engineering and biological systems. We envisage intrinsic neuronal resonance as a cellular-scale activitydependent negative feedback mechanism, a specific instance of a well-established network motif that effectuates stability and suppresses perturbations across different networks (Savageau, 1974; Becskei and Serrano, 2000; Thattai and van Oudenaarden, 2001; Austin et al., 2006; Dublanche et al., 2006; Raj and van Oudenaarden, 2008; Lestas et al., 2010; Cheong et al., 2011; Voliotis et al., 2014). A detailed discussion on this important link to the stabilizing role of this network motif, with appropriate references to the literature is included in the new discussion subsection “Slow negative feedback: Stability, noise suppression, and robustness”.

We thank the reviewer for their detailed comments. These comments helped us to introducing a more physiologically rooted mechanistic form of resonance, where we were able to assess the impact of slow kinetics of negative feedback on network stability, thereby providing more direct lines of evidence for our hypothesis. This also allowed us to link resonance to the wellestablished stability motif: the negative feedback loop. We also note that our analyses don’t employ resonance as a route to introducing oscillations in the network, but as a means for targeted suppression of low-frequency perturbations through a negative feedback loop. Given the strong quantitative links of negative feedback loops to introducing stability and suppressing the impact of perturbations in engineering applications and biological networks, we envisage intrinsic neuronal resonance as a stability-inducing cellular-scale activity-dependent negative feedback mechanism.

Reviewer #2 (Public Review):

[...] The pars construens demonstrates that similar networks, but comprised of units with different dynamical behavior, essentially amputated of their slowest components, do not suffer from the heterogeneities - they still produce grids. This part proceeds through 3 main steps: a) defining "resonator" units as model neurons with amputated low frequencies (Fig. 5); b) showing that inserted into the same homogeneous CAN network, "resonator" units produce the same grids as "integrator" units (Figs. 6,7); c) demonstrating that however the network with "resonator" units is resistant to heterogeneities (Fig. 8). Figs. 9 and 10 help understand what has produced the desired grid stabilization effect. This second part is on the whole also well structured, and its step c) is particularly convincing.

We thank the reviewer for their time and effort in evaluating our manuscript, and for their rigorous evaluation and positive comments on our study.

Step b) intends to show that nothing important changes, in grid pattern terms, if one replaces the standard firing rate units with the ad hoc defined units without low frequency behavior. The exact outcome of the manipulation is somewhat complex, as shown in Figs. 6 and 7, but it could be conceivably summed up by stating that grids remain stable, when low frequencies are removed. What is missing, however, is an exploration of whether the newly defined units, the "resonators", could produce grid patterns on their own, without the CAN arising from the interactions between units, just as a single-unit effect. I bet they could, because that is what happens in the adaptation model for the emergence of the grid pattern, which we have studied extensively over the years. Maybe with some changes here and there, but I believe the CAN can be disposed of entirely, except to produce a common alignment between units, as we have shown.

Step a), finally, is the part of the study that I find certainly not wrong, but somewhat misleading. Not wrong, because what units to use in a model, and what to call them, is a legitimate arbitrary choice of the modelers. Somewhat misleading, because the term "resonator" evokes a more specific dynamical behavior that than obtained by inserting Eqs. (8)-(9) into Eq. (6), which amounts to a brute force amputation of the low frequencies, without any real resonance to speak of. Unsurprisingly, Fig. 5, which is very clear and useful, does not show any resonance, but just a smooth, broad band-pass behavior, which is, I stress legitimately, put there by hand. A very similar broad band-pass would result from incorporating into individual units a model of firing rate adaptation, which is why I believe the "resonator" units in this study would generate grid patterns, in principle, without any CAN.

We thank the reviewer for these constructive comments and questions, as they were extremely helpful in (i) formulating a new model for rate-based resonating neurons that is more physiologically rooted; (ii) demonstrating the stabilizing role of resonance irrespective of model choices that implemented resonance; and (iii) mechanistically exploring the impact of targeted suppression of low frequency components in neural activity. We answer these comments of the reviewer in two parts, the first addressing other models for grid-patterned activity generation and the second addressing the reviewer’s comment on “brute force amputation of the low frequencies” in the resonator neuron presented in the previous version of our manuscript.

I. Other models for grid-patterned activity generation.

In the adaptation model (Kropff and Treves, 2008; Urdapilleta et al., 2017; Stella et al., 2020), adaptation in conjunction with place-cell inputs, Hebbian synaptic plasticity, and intrinsic plasticity (in gain and threshold) to implement competition are together sufficient for the emergence of the grid-patterned neural activity. However, the CAN model that we chose as the substrate for assessing the impact of neural circuit heterogeneities on functional stability is not equipped with the additional components (place-cell inputs, synaptic/intrinsic plasticity). Therefore, we note that decoupling the single unit (resonator or integrator) from the network does not yield grid-patterned activity.

However, we do agree that a resonator neuron endowed with additional components from the adaptation model would be sufficient to elicit grid-patterned neural activity. This is especially clear with the newly introduced mechanistic model for resonance through a slow feedback loop (Figure 9). Specifically, resonating conductances such as HCN and M-type potassium channels can effectuate spike-frequency adaptation. One of the prominent channels that is implicated in introducing adaptation, the calcium-activated potassium channels implement a slow activitydependent negative feedback loop through the slow calcium kinetics. Neural activity drives calcium influx, and the slow kinetics of the calcium along with the channel-activation kinetics drive a potassium current that completes a negative feedback loop that inhibits neural activity. Consistently, one of the earliest-reported forms of electrical resonance in cochlear hair cells was shown to be mediated by calcium-activated potassium channels (Crawford and Fettiplace, 1978, 1981; Fettiplace and Fuchs, 1999). Thus, adaptation realized as a slow negative-feedback loop, in conjunction with place-cell inputs and intrinsic/synaptic plasticity would elicit gridpatterned neural activity as demonstrated earlier (Kropff and Treves, 2008; Urdapilleta et al., 2017; Stella et al., 2020).

There are several models for the emergence of grid-patterned activity, and resonance plays distinct roles (compared to the role proposed through our analyses) in some of these models (Giocomo et al., 2007; Kropff and Treves, 2008; Burak and Fiete, 2009; Burgess and O'Keefe, 2011; Giocomo et al., 2011b; Giocomo et al., 2011a; Navratilova et al., 2012; Pastoll et al., 2012; Couey et al., 2013; Domnisoru et al., 2013; Schmidt-Hieber and Hausser, 2013; Yoon et al., 2013; Schmidt-Hieber et al., 2017; Urdapilleta et al., 2017; Stella et al., 2020; Tukker et al., 2021). However, a common caveat that spans many of these models is that they assume homogeneous networks that do not account for the ubiquitous heterogeneities that span neural circuits. Our goal in this study was to take a step towards rectifying this caveat, towards understanding the impact of neural circuit heterogeneities on network stability. We chose the 2D CAN model for grid-patterned activity generation as the substrate for addressing this important yet under-explored question on the role of biological heterogeneities on network function. As we have mentioned in the discussion section, this choice implies that our conclusions are limited to the 2D CAN model for grid patterned generation; these conclusions cannot be extrapolated to other networks or other models for grid-patterned activity generation without detailed analyses of the impact of neural circuit heterogeneities in those models. As our focus here was on the stabilizing role of resonance in heterogeneous neural networks, with 2D CAN model as the substrate, we have not implemented the other models for grid-patterned generation. The impact of biological heterogeneities and resonance on each of these models should be independently addressed with systematic analyses similar to our analyses for the 2D CAN model. As different models for grid-patterned activity generation are endowed with disparate dynamics, and have different roles for resonance, it is conceivable that the impact of biological heterogeneities and intrinsic neuronal resonance have differential impact on these different models. We have mentioned this as a clear limitation of our analyses in the discussion section, also presenting future directions for associated analyses(subsection: “Future directions and considerations in model interpretation”).

II. Brute force amputation of the low frequencies in the resonator model.

We completely agree with the reviewer on the observation that the resonator model employed in the previous version of our manuscript was rather artificial, with the realization involving brute force amputation of the lower frequencies. To address this concern, in the revised manuscript, we constructed a new mechanistic model for single-neuron resonance that matches the dynamical behavior of physiological resonators. Specifically, we noted that physiological resonance is elicited by a slow activity-dependent negative feedback (Hutcheon and Yarom, 2000). To incorporate resonance into our rate-based model neurons, we mimicked this by introducing a slow negative feedback loop into our single-neuron dynamics (the motivations are elaborated in the new results subsection “Mechanistic model of neuronal intrinsic resonance: Incorporating a slow activity-dependent negative feedback loop”). The singleneuron dynamics of mechanistic resonators were defined as follows:

Here, S governed neuronal activity, τ defined the feedback state variable, g represented the integration time constant, Ie was the external current, and g represented feedback strength. The slow kinetics of the negative feedback was controlled by the feedback time constant (τm). In order to manifest resonance, τm > τ (Hutcheon and Yarom, 2000). The steady-state feedback kernel (m∞) of the negative feedback is sigmoidally dependent on the output of the neuron (S), defined by two parameters: half-maximal activity (S1/2) and slope (k). The single-neuron dynamics are elaborated in detail in the methods section (new subsection: Mechanistic model for introducing intrinsic resonance in rate-based neurons).

We first demonstrate that the introduction of a slow-negative feedback loop introduce resonance into single-neuron dynamics (new Figure 9D–E). We performed systematic sensitivity analyses associated with the parameters of the feedback loop and characterized the dependencies of intrinsic neuronal resonance on model parameters (new Figure 9F–I). We demonstrate that the incorporation of resonance through a negative feedback loop was able to generate grid-patterned activity in the 2D CAN model employed here, with clear dependencies on model parameters (new Figure 10; new Figure 10-Supplements1–2). Next, we incorporated heterogeneities into the network and demonstrated that the introduction of resonance through a negative feedback loop stabilized grid-patterned generation in the heterogeneous 2D CAN model (new Figure 11).

The mechanistic route to introducing resonance allowed us to probe the basis for the stabilization of grid-patterned activity more thoroughly. Specifically, with physiological resonators, resonance manifests only when the feedback loop is slow (new Figure 9I; Hutcheon and Yarom, 2000). This allowed us an additional mechanistic handle to directly probe the role of resonance in stabilizing the grid patterned activity. We assessed the emergence of grid-patterned activity in heterogeneous CAN models constructed with networks constructors with neurons with different τm values (new Figure 12). Strikingly, we found that when τm value was small (resulting in fast feedback loops), there was no stabilization of gridpatterned activity in the CAN model, especially with the highest degree of heterogeneities (new Figure 12). With progressive increase in τm, the patterns stabilized with grid score increasing with τm=25 ms (new Figure 12) and beyond (new Figure 11B; τm=75 ms). Finally, our spectral analyses comparing frequency components of homogeneous vs. heterogeneous resonator networks (new Figure panels 13D–F) showed the suppression of low-frequency perturbations in heterogeneous CAN networks.

We gratefully thank the reviewer for raising the issue with the phenomenological resonator model. This allowed us to design the new resonator model and provide several new lines of evidence in support of our central hypothesis. The incorporation of resonance through a negative feedback loop also allowed us to link our analyses to the well-established role of network motifs involving negative feedback loops in inducing stability and suppressing external/internal noise in engineering and biological systems. We envisage intrinsic neuronal resonance as a cellular-scale activity-dependent negative feedback mechanism, a specific instance of a well-established network motif that effectuates stability and suppresses perturbations across different networks (Savageau, 1974; Becskei and Serrano, 2000; Thattai and van Oudenaarden, 2001; Austin et al., 2006; Dublanche et al., 2006; Raj and van Oudenaarden, 2008; Lestas et al., 2010; Cheong et al., 2011; Voliotis et al., 2014). A detailed discussion on this important link to the stabilizing role of this network motif, with appropriate references to the literature is included in the new discussion subsection “Slow negative feedback: Stability, noise suppression, and robustness”.

eLife Assessment

Antibodies that selectively bind distinct amyloid-beta variants are vital tools for Alzheimer's disease research. This valuable manuscript aims to delineate the epitope specificity in a panel of anti-amyloid-beta antibodies, including some with clinical relevance. The experiments were rigorously conducted, employing an interesting combination of established and state-of-the-art methodologies, yielding convincing findings.

Reviewer #1 (Public review):

The manuscript by Ivan et al aimed to identify epitopes on the Abeta peptide for a large set of anti-Abeta antibodies, including clinically relevant antibodies. The experimental work was well done and required a major experimental effort including peptide mutational scanning, affinity determinations, molecular dynamics simulations, IP-MS, WB and IHC. The first part of the work is focused on an assay in which peptides (15-18-mers) based on the human Abeta sequence, including some containing known PTMs, are immobilized, thus preventing aggregation and for this reason provide limited biologically-relevant information. Although some results are in agreement with previous experimental structural data (e.g. for 3D6), and some responses to disease-associated mutations were different when compared to wild-type sequences (e.g. in the case of Aducanumab) - which may have implications for personalized treatment. On the other hand, the contribution of conformation (as in oligomers and large aggregates) in antibody recognition patterns was took into consideration in the second part of the study, in which both full-length Abeta in monomeric or aggregated forms and human CSF was employed to investigate the differential epitope interaction between Aducanumab, donanemab and lecanemab. Interestingly, these results confirmed the expected preference of these antibodies for aggregated Abeta. Overall, I understand that the work is of interest to the field.

Comments on revisions:

I have no additional recommendations.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

The manuscript by Ivan et al aimed to identify epitopes on the Abeta peptide for a large set of anti-Abeta antibodies, including clinically relevant antibodies. The experimental work was well done and required a major experimental effort, including peptide mutational scanning, affinity determinations, molecular dynamics simulations, IP-MS, WB, and IHC. Therefore, it is of clear interest to the field. The first part of the work is mainly based on an assay in which peptides (15-18-mers) based on the human Abeta sequence, including some containing known PTMs, are immobilized, thus preventing aggregation. Although some results are in agreement with previous experimental structural data (e.g. for 3D6), and some responses to diseaseassociated mutations were different when compared to wild-type sequences (e.g. in the case of Aducanumab) - which may have implications for personalized treatment - I have concerns about the lack of consideration of the contribution of conformation (as in small oligomers and large aggregates) in antibody recognition patterns. The second part of the study used fulllength Abeta in monomeric or aggregated forms to further investigate the differential epitope interaction between Aducanumab, Donanemab, and Lecanemab (Figures 5-7). Interestingly, these results confirmed the expected preference of these antibodies for aggregated Abeta, thus reinforcing my concerns about the conclusions drawn from the results obtained using shorter and immobilized forms of Abeta. Overall, I understand that the work is of interest to the field and should be published without the need for additional experimental data. However, I recommend a thorough revision of the structure of the manuscript in order to make it more focused on the results with the highest impact (second part).

We thank the reviewer for highlighting this critical aspect. Our rationale for beginning with the high-resolution, aggregation-independent peptide microarray was to systematically dissect sequence requirements, including PTMs, truncations, and elongations, at single–amino acid resolution. This platform defines linear epitope preferences without the confounding influence of aggregation and enabled analyses that would not have been technically feasible with fulllength Aβ. This rationale is now clarified in the Introduction (lines 72–77).

At the same time, the physiological relevance of antibody binding can only be assessed in the context of aggregation. Prompted by the reviewer’s comments, we restructured the manuscript to foreground the full-length, aggregation-dependent data (Figures 5–7). These assays demonstrate that Aducanumab preferentially recognizes aggregated peptide over monomers and that pre-adsorption with fibrils, but not monomers, blocks tissue reactivity (lines 585–599; Fig. 5B). They also show that Lecanemab can capture soluble Aβ in CSF by IP-MS (lines 544–547; Fig. 4B, Fig. 6–Supplement 1), and that Donanemab strongly binds low-molecular-weight pyroGlu-Aβ while also recognizing highly aggregated Aβ1-42 (lines 668–684; Fig. 7).

The revised Conclusion now explicitly states the complementarity of the two approaches: microarrays for precise sequence and modification mapping, and full-length aggregation assays for context and physiological relevance (lines 705–714).

Finally, prompted by the reviewer’s feedback, we refined the discussion of therapeutic antibodies to move beyond a descriptive dataset and provide mechanistic clarity. Specifically, the dimerization-supported, valency-dependent binding mode of Aducanumab and the additional structural contributions required for Lecanemab binding to aggregated Aβ are now integrated into the reworked Conclusion (lines 725–741).

Reviewer #2 (Public review):  

This paper investigates binding epitopes of different anti-Abeta antibodies. Background information on the clinical outcome of some of the antibodies in the paper, which might be important for readers to know, is lacking. There are no references to clinical outcomes from antibodies that have been in clinical trials. This paper would be much more complete if the status of the antibodies were included. The binding characteristics of aducanumab, donanemab, and Lecanemab should be compared with data from clinical phase 3 studies. 

Aducanumab was identified at Neurimmune in Switzerland and licensed to Biogen and Eisai. Aducanumab was retracted from the market due to a very high frequency of the side-effect amyloid-related imaging abnormalities-edema (ARIA-E). Gantenerumab was developed by Roche and had two failed phase 3 studies, mainly due to a high frequency of ARIA-E and low efficacy of Abeta clearance. Lecanemab was identified at Uppsala University, humanized by BioArctic, and licensed to Eisai, who performed the clinical studies. Eisai and Biogen are now marketing Lecanemab as Leqembi on the world market. Donanemab was developed by Ely Lilly and is sold in the US as Kisunla. 

We thank the reviewer for this valuable suggestion. In the revised manuscript, we have included a concise overview of the clinical status and outcomes of the therapeutic antibodies in the Introduction. This new section (lines 81–99) summarizes the origins, phase 3 trial outcomes, and current regulatory status of Aducanumab, Lecanemab, and Donanemab, as well as mentioning Gantenerumab as a comparator. Key aspects such as ARIA-E incidence, amyloid clearance efficacy, and regulatory decisions are now referenced to provide the necessary clinical context.

These additions directly link our epitope mapping data with the clinical performance and safety profiles of the antibodies, thereby making the translational implications of our results clearer for both research and therapeutic applications.

Limitations: 

(1) Conclusions are based on Abeta antigens that may not be the primary targets for some conformational antibodies like aducanumab and Lecanemab. There is an absence of binding data for soluble aggregated species.

We thank the reviewer for raising this important point. To address the absence of data on soluble aggregated species, we added IP-MS experiments using pooled human CSF as a physiologically relevant source of endogenous Aβ. Lecanemab enriched several endogenous soluble Aβ variants (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42), whereas Aducanumab did not yield detectable signals (Figure 4B; lines 544–547). These results directly distinguish between synthetic and patient-derived Aβ and highlight Lecanemab’s capacity to capture soluble Aβ species under biologically relevant conditions.

(2) Quality controls and characterization of different Abeta species are missing. The authors need to verify if monomers remain monomeric in the blocking studies for Figures 5 and 6. 

We thank the reviewer for this comment. In Figure 5 we show that pre-adsorption with monomeric Aβ1–42 does not prevent Aducanumab binding, whereas fibrillar Aβ1–42 completely abolishes staining, consistent with Aducanumab’s avidity-driven preference for higher-order aggregates.

For Lecanemab (Figure 6), we observed a partial preference for aggregated Aβ1–42 over HFIP-treated monomeric and low-n oligomeric forms. We note, as now stated in the revised manuscript (lines 622–623), that monomeric preparations may partially re-aggregate under blocking conditions, which represents an inherent limitation of such experiments.

To further address this, we performed additional blocking experiments using shorter Aβ peptides, which are less prone to aggregation. These peptides did not block immunohistochemical staining (Figure 6 – Supplement 1), underscoring that both epitope length and conformational state contribute to Lecanemab binding. This conclusion is also consistent with recent data presented at AAIC 2023.

(3) The authors should discuss the limitations of studying synthetic Abeta species and how aggregation might hide or reveal different epitopes. 

We thank the reviewer for this important comment. We now explicitly discuss the limitations of using synthetic Aβ peptides, including that aggregation state can mask or expose epitopes in ways that differ from endogenous species. This discussion has been added in the revised manuscript (lines 737–742).

As noted in our replies to Points (2) and (4) here, and to Reviewer #1, we addressed this experimentally by complementing the high-resolution, aggregation-independent mapping with blocking studies using aggregated and monomeric Aβ preparations, and by validating key findings with IP-MS of human CSF as a physiologically relevant source of soluble Aβ. Together, these complementary approaches mitigate the limitations of synthetic peptides and provide a more comprehensive picture of antibody–Aβ interactions

(4) The authors should elaborate on the differences between synthetic Abeta and patientderived Abeta. There is a potential for different epitopes to be available. 

We thank the reviewer for this comment. In the revised manuscript we now discuss how comparisons between synthetic and patient-derived Aβ species reveal additional, likely conformational epitopes that are not accessible in short or monomeric synthetic forms. To address this directly, we performed IP-MS with pooled human CSF. Lecanemab enriched a diverse set of endogenous soluble Aβ1–X species (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42), whereas Aducanumab did not yield measurable pull-down (Figure 4B; lines 544– 547). These results emphasize that patient-derived Aβ displays distinct aggregation dynamics and epitope accessibility.

We have expanded on this point in the Conclusion (lines 737–742), underscoring the

importance of integrating both synthetic and native Aβ sources to capture the full range of antibody targets. 

Reviewer #1 (Recommendations for the authors): 

This revision should prioritize the presentation of results obtained using the full-length Abeta peptide, given its more direct relevance to expected antibody recognition patterns in physiological contexts, and discuss the evidence for using synthetic Abeta. 

We thank the reviewer for this recommendation. The revised manuscript now places stronger emphasis on results obtained with full-length Aβ peptides, particularly in Figures 5–7, which analyze binding preferences across monomeric, oligomeric, and fibrillar states (lines 585–599, 609–623, 668–684). We also expanded the Discussion to outline both the rationale and the limitations of using synthetic Aβ. The microarray approach provides high-resolution, aggregation-independent sequence and modification mapping, but must be complemented by experiments with full-length Aβ1–42 under physiologically relevant conditions, such as IP-MS from CSF (lines 544–547) and blocking in IHC (lines 585–599, 622–623, 684), to capture conformational epitopes and validate functional relevance.

Figure 6. = Please review/better explain the following statement "Lecanemab recognized Aβ140, Aβ1-42, Aβ3-40, Aβ-3-40 and phosphorylated pSer8-Aβ1-40 on CIEF-immunoassay and Bicine-Tris SDS-PAGE/ Western blot, indicating that the Lecanemabbs epitope is located in the N-terminal region of the Aβ sequence". Is it possible that N-truncated peptides do not form aggregates as efficiently as (or conformationally distinct from) full-length ones? 

In the revised text we now clarify that Lecanemab recognized Aβ1-40, Aβ1-42, Aβ3-40, Aβ-340, and phosphorylated pSer8-Aβ1-40 on CIEF-immunoassay (Figure 6A; lines 612–619) and Bicine-Tris SDS-PAGE/Western blot (Figure 6C; lines 639–640). In contrast, shorter Ntruncated variants such as Aβ4-40 and Aβ5-40 did not generate detectable signals under the tested conditions. This is consistent with our initial microarray data (Figure 1), which indicated that Lecanemab binding depends on residues 3–7 of the N-terminus.

On gradient Bistris SDS-PAGE/Western blot, Lecanemab showed a partial but not exclusive preference for aggregated Aβ1-42 over monomeric or low-n oligomeric forms in the HFIPtreated preparation (Figure 6B; lines 632–633). Immunohistochemical detection of Aβ deposits in AD brain sections was efficiently blocked by pre-adsorption with monomerized, oligomeric, or fibrillar Aβ1-42 (Figure 6E; lines 643–645), but not by shorter synthetic peptides such as Aβ1-16, Aβ1-34, or Aβ1-38 (Figure 6 – Supplement 1; lines 654–663).

We also note, as now stated in the Results, that re-aggregation of HFIP-treated Aβ1-42 monomers during incubation cannot be entirely excluded (lines 622–623). Taken together, these experiments indicate that both N-terminal sequence length and conformational context are critical for Lecanemab binding, and that truncated peptides may indeed fail to reproduce the aggregate-associated conformations required for full recognition.

Reviewer #2 (Recommendations for the authors): 

Introduction: 

(1) Include examples of Lecanemab, donanemab, and gantenerumab, along with relevant references. 

We expanded the clinical-context paragraph that already covers Aducanumab, Lecanemab, and Donanemab (lines 81–96) and added Gantenerumab. 

(2) Address why gantenerumab was not included in the study. 

Due to the focus of our current study on antibodies with recently approved or late-stage clinical use (Aducanumab, Donanemab, Lecanemab), Gantenerumab was not included. 

(3) Table 1: Correct the reference for Lecanemab, should be reference 44. 

Table 1 has been updated to correct the Lecanemab reference.

(4) Line 84: Add Uppsala University and Eisai alongside Biogen for Lecanemab. 

Line 84 has been revised to acknowledge Uppsala University and Eisai alongside Biogen for the development of Lecanemab (lines 90–96).

(5) Line 539: Include the reference: "Lecanemab, Aducanumab, and Gantenerumab - Binding Profiles to Different Forms of Amyloid-Beta Might Explain Efficacy and Side Effects in Clinical Trials for Alzheimer's Disease. doi: 10.1007/s13311-022-01308-6. 

We thank the reviewer for drawing attention to this important reference (now cited as Ref. 83) provides a state-of-the-art comparison of binding profiles of Lecanemab, Aducanumab, and Gantenerumab, and we have now properly incorporated it into our manuscript. 

(6) Line 657-659: State that the findings are also applicable to Lecanemab. 

Discrepancies between analysis of the short synthetic fragments and the full-length Abeta are now resolved for Aducanumab and Lecanemab and put into context in the results section and the conclusion lines 725-740. 

(7) Figures 5 and 6: Discuss how to ensure that monomers remain monomers under the study conditions, considering the aggregation-prone nature of Abeta1-42. This aggregation could impact Lecanemab's binding to "monomers." To our knowledge, Lecanemab does not bind to monomers. The binding properties observed diverge from previously described properties for Lecanemab. Explore reasons for these discrepancies and suggest conducting complementary experiments using a solution-based assay, as per Söderberg et al, 2023. In Figure 6, note that Lecanemab is strongly avidity-driven, potentially causing densely packed monomers to expose Abeta as aggregated, affecting binding interpretation on SDS-PAGE. 

We thank the reviewer for this important point. In the revised Results and Discussion we explicitly note that HFIP-treated Aβ1–42 monomers may partially re-aggregate during incubation, which cannot be fully excluded (lines 622–623).

To complement these data, we show that Lecanemab successfully enriched soluble endogenous Aβ species (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42) in IP-MS from pooled CSF (lines 544–547; Fig. 4B), demonstrating its ability to bind soluble Aβ under physiologically relevant conditions.

We also now cite the Söderberg et al. (2023, PMID: 36253511) study, which reported weak but detectable binding of Lecanemab to monomeric Aβ (their Fig. 1 and Table 6). This supports our interpretation that Lecanemab is aggregation-sensitive rather than strictly aggregationdependent, in contrast to Aducanumab.

To further address sequence and conformational contributions, we performed blocking experiments with shorter, non-HFIP-treated Aβ peptides (Aβ1–16, Aβ1–34, Aβ1–38). These peptides did not block Lecanemab staining in IHC (lines 654–657; Fig. 6 – Supplement 1), indicating that both extended sequence and conformational context are necessary for recognition.

Finally, our findings are in line with preliminary data by Yamauchi et al. (AAIC 2023, DOI: 10.1002/alz.065104), who proposed that Lecanemab recognizes either a conformational epitope spanning the N-terminus and mid-region, or a structural change in the mid-region induced by the N-terminus.

eLife Assessment

This valuable work provides new insights into the role of lysine acetylation of alpha-synuclein, the protein involved in Parkinson's Disease. The evidence is mostly solid, but the claims around the potential disease relevance based on seeding assays and structural work need to be toned down, or else supported by additional experimental evidence. Overall, the work will be of interest to researchers in the fields of protein biophysics and post-translational modifications, as well as Parkinson's Disease.

Reviewer #1 (Public review):

Summary:

This paper describes experiments with alpha-synuclein (aS) with acetylated lysines (acK) at various positions. Their findings on how to use non-canonical amino acid (ncAA) mutagenesis to generate aS with acetylated lysines are valuable. The paper then continues with a range of experiments to characterise the acetylated alpha-synuclein constructs at different positions, with the aim of providing insights into which sites are relevant to disease or their function inside cells. The paper concludes these experiments with the suggestion that inhibiting the Zn2+-dependent histone deacetylase HDAC8 to potentially increase acetylation at lysine 80 may have therapeutic benefit. However, the relevance of most of these experiments is unclear, mainly as the filaments that form from these constructs are different from those observed in human disease (but see below for more details). Moreover, using the recombinantly produced acetylated versions of alpha-synuclein to normalise mass-spectrometry data, the authors themselves report that acetylation of alpha-synuclein does not differ between individuals with Parkinson's disease or healthy controls.

Strengths:

The authors report difficulties with chemical synthesis, and then decide to make these constructs using non-canonical amino acid (ncAA) mutagenesis, which seems to work reasonably well (yields vary somewhat). In the Conclusion section, the authors report that they used these recombinant proteins to obtain quantitative insights into the levels of acetylation of lysines in individuals with PD versus healthy controls, for which they find no significant differences. This part of the work is valuable.

Weaknesses:

The authors then use circular dichroism to show that aSyn with acK at position 43 has less alpha-helical content. From this result, they deduce that "only this site could potentially perturb aS function in neurotransmitter trafficking", but no experiments on neurotransmitter trafficking were performed.

Subsequently, they measure the aggregation speed of the variants in seeded aggregation experiments with preformed fibrils (PFFs) from WT aSyn, and conclude that acK at positions 12, 43, and 80 yields slower aggregation. They reach similar conclusions when measuring seeded aggregation in primary cultures. As far as I understand it, the seeding experiments in cells use seeds that are assembled from partially acetylated alpha-synuclein, but that are made of non-acetylated wildtype alpha-synuclein, and the alpha-synuclein that is endogenous in the cells is also non-acetylated (or at least not beyond what happens in these cells at endogenous levels). It is therefore unclear how the cellular seeding experiments relate to the in vitro aggregation assays with (partially) acetylated substrates. Anyway, both aggregation experiments ignore that the structures of aSyn filaments in Parkinson's disease (PD) or multiple system atrophy (MSA) are different from those formed in these experiments, and that, therefore, the observed aggregation kinetics are likely irrelevant for the speed with which disease-relevant filaments form in the brain.

NMR and FCS experiments show that acK at positions 12 and 43 may reduce binding to vesicles, which then leaves only acK80.

Finally, the authors describe the cryo-EM structure of mixtures of acK80:WT aSyn filaments, which are predominantly made of WT aSyn, with a previously described structure. Filaments made of only acK80 aSyn have a modified arrangement of this structure, where the now neutral side chain of residue 80 packs inside a hydrophobic pocket. The authors discuss differences between the acK80 structures and those of other structures from in vitro assembled aSyn filaments, none of which are the same as those observed from PD or MSA brains, nor are any attempts made to transfer observations from the in vitro experiments to the structures of disease. The relevance of the cryo-EM structures for human disease, therefore, remains unclear.

The Conclusion on p.20 mentions an interesting and valuable result: the authors used the acetylated recombinant proteins to determine the extent of acetylation within human protein samples by quantitative liquid chromatography MS (SI, Figures S41-S49). Their conclusion is that "The level of acetylation was variable - no clear trend was observed between healthy control and patients - nor between patients of different diseases (SI, Table S4, Supplementary Data 1)" This result implies that acetylation of aS is not directly related to its pathogenicity, which again adds doubts on the disease-relevance of the results described in the rest of the paper.

Reviewer #2 (Public review):

Summary:

Shimogawa et al. studied the effect of lysine acetylation at different sites in the alpha-synuclein (aS) sequence on the protein-membrane affinity, seeding capacity in the test tube and in cells, and on the structure of fibrils, using a range of biophysical methods. They use non-canonical amino acid (ncAA) mutagenesis to prepare aS lysine acetylated variant at different sites.

Strengths:

The major strength of this paper is the approach used for the production of site-specific lysine acetylated variants of aS using ncAA mutagenesis, as well as the combination of a range of biophysical methods together with cellular assays and structure biology to decipher the effect of lysine acetylation on aS-membrane binding, seeding propensity, and fibril structure. This approach allowed the author to find that lysine acetylation at positions 12, 43, and 80 led to lower seeding capacity of aS in the test tube and in cells, but only acetylation at lysine 80 did not affect aS-membrane interaction. These results suggest that lysine acetylation at position 80 may be protective against aggregation without perturbing the proposed functional role of aS in synaptic plasticity.

Weaknesses:

SDS is not a good membrane model to investigate the effect of lysine acetylation on aS membrane-binding because it is a harsh detergent and solubilizes membranes. Negatively charged vesicles or vesicles made of a mixture of lipids mimicking the lipid composition of synaptic vesicles are more accepted in the field to study aS-membrane interactions. The authors used such vesicles for the FCS experiments, and they could be used for the initial screening of the 12 lysine acetylated variants of aS.

It would help the reader to have the experimental details (e.g., buffer, protein/lipid concentrations) for the different assays written in the figure legend.

The authors use an assay consisting of mixing 10% fibrils + 90% monomer to investigate the effect of lysine acetylation on aS. However, the assay only probes fibril elongation and/or secondary processes. The current wording can be misleading, and the term aggregation could be replaced by seeding capacity for clarity. For example, the authors state that lysine acetylation at sites 12, 43, and 80 each inhibits aggregation, but this statement is not supported by the data. Instead, the data show that the acetylation at these sites slows down the fibril elongation and thus decreases the seeding capacity of aS fibrils. In order to state that lysine acetylation has an effect on aS aggregation, fibril formation, the author should use an assay where the de novo formation of fibrils is assessed, such as in the presence of lipid vesicles or under shaking conditions.

It is not clear from the EM data that the structures of the different lysine acetylated variants are different, unlike what is stated in the text.

Reviewer #3 (Public review):

Shimogawa et al. describe the generation of acetylated aSyn variants by genetic code expansion to elucidate effects on vesicle binding, aggregation, and seeding effects. The authors compared a semi-synthetic approach to obtain acetylated aSyn variants with genetic code expansion and concluded that the latter was more efficient in generating all 12 variants studied here, despite the low yields for some of them. Selected acetylated variants were used in advanced NMR, FCS, and cryo-EM experiments to elucidate structural and functional changes caused by acetylation of aSyn. Finally, site-specific differences in deacetylation by HDAC 8 were identified.

The study is of high scientific quality, andthe results are convincingly supported by the experimental data provided. The challenges the authors report regarding semi-synthetic access to aSyn are somewhat surprising, as this protein has been made by a variety of different semi-synthesis strategies in satisfactory yields and without similar problems being reported.

The role of PTMs such as acetylation in neurodegenerative diseases is of high relevance for the field, and a particular strength of this study is the use of authentic acetylated aSyn instead of acetylation-mimicking mutations. The finding that certain lysine acetylations can slow down aggregation even when present only at 10-25% of total aSyn is exciting and bears some potential for diagnostics and therapeutic intervention.

Author response:

We thank you for your efforts in reviewing our manuscript.  We sincerely appreciate that the reviewers were all enthusiastic about our comparison of native chemical ligation (NCL) and non-canonical amino acid (ncAA) mutagenesis methods for installing acetyl lysine (AcK) in alpha-synuclein, as well as the wide variety of biochemical experiments enabled by our ncAA approach.  We respond to the critiques specific to each reviewer here.

Reviewer #1:

Expressed concern that in vitro studies of effects on membrane binding were not followed up with neurotransmitter trafficking experiments.  While we certainly think that such studies would be interesting, they would presumably require the use of acetylation mimic mutants (Lys-to-Gln mutations), which we would want to validate by comparison to our semi-synthetic proteins with authentic AcK.  Such experiments are planned for a follow-up manuscript, and we will investigate the reviewer’s suggested experiment at that time.

Reviewer #1 Noted that the method of in vitro seeding really reports on the impact of acetylation on the elongation phase of aggregation.  We will clarify this in our revisions.  They also expressed concern that this was different than the role that acetylation would play in seeding cellular aggregation with pre-acetylated fibrils.  We will also acknowledge and clarify this in our revisions.  Having the monomer population acetylated in cells presents technical challenges that might also be addressed with Gln mutant mimics, and we plan to pursue such experiments in the follow-up manuscript noted above.

Reviewer #1 Criticized the fact that the pre-formed fibrils used in seeding would not have the same polymorph as PD or MSA fibrils derived from patient material.  They were also critical of how our cryo-EM structure of AcK80 fibrils related to the PD and MSA polymorphs.  Finally, while the reviewer liked the MS experiments used to quantify acetylation levels from patient samples, they felt that our findings then threw the physiological relevance of our structural and biochemical experiments into question.  We believe that all of these critiques can be addressed by clarifying our purpose.  We are not necessarily trying to claim that our AcK80 fold is populated in health or disease, but that by driving Lys80 acetylation, one could push fibrils to adopt this conformation, which is less aggregation-prone.  A similar argument has been made in investigations of alpha-synuclein glycosylation and phosphorylation.  Our results in Figure 9 imply that this could be done with HDAC8 inhibition.  We will revise the manuscript to make these ideas clearer, while being sure to acknowledge the limitations noted by Reviewer #1.

Reviewer #2:

Expressed concern over our use of SDS micelles for initial investigation of the 12 AcK variants, rather than the phospholipid vesicles used in later FCS and NMR experiments.  We will note this shortcoming in revisions of our manuscript, but we do not believe that using vesicles instead would change the conclusions of these experiments (that only AcK43 produces an effect, and a modest one at that).

We will add additional detail to the figure captions, as requested by Reviewer #2.

Reviewer #2 shared some of the concerns of Reviewer #1 regarding the distinctions of which phase of aggregation we were investigating in our in vitro experiments.  As noted above, we will clarify this language.

Finally, Reviewer #2 stated that “It is not clear from the EM data that the structures of the different lysine acetylated variants are different.”  We feel that it is quite clear from structures in Figure 8 and the EM density maps in Figure S38 that the AcK80 fold is indeed different.  Although the overall polymorphs are somewhat similar to WT, the position of K80 clearly changes upon acetylation, altering the local fold significantly and the global fold more moderately.

Reviewer #3:

Found the results convincing, including the potential therapeutic implications.  The only concern noted was that they found the difficulties in semi-synthesis of AcK-modified alpha-synuclein surprising given that it has been made many times before through NCL.  Indeed, our own laboratory has made alpha-synuclein through NCL, and the yields reported here are in keeping with our own previous results.  However, since NCL did not give higher yields than ncAA methods, and it is significantly easier to scan AcK positions using ncAAs, we felt that ncAAs are the method of choice in this case.  We will clarify this position in the revised manuscript.

In conclusion, on behalf of all authors, I again thank the reviewers for both their positive and negative observations in helping us to improve our manuscript.  We will revise it to strive for greater clarity as we have noted in this letter.

eLife Assessment

This study seeks to expand the understanding of insulin and glucose responses in the brain, specifically by implicating a family of protein kinases responsive to insulin. The significance of the study to the field is valuable, given this study is very emblematic of the new field of interoception (Brain-Body physiology). The evidence supporting the conclusions about brain glucose utilization is convincing and is relevant to many age-related diseases, such as Alzheimer's disorder.

Reviewer #1 (Public review):

Summary:

The study by Akita B. Jaykumar et al. explored an interesting and relevant hypothesis whether serine/threonine With-No-lysine (K) kinases (WNK)-1, -2, -3, and -4 engage in insulin-dependent glucose transporter-4 (GLUT4) signaling in the murine central nervous system. The authors especially focused on the hippocampus as this brain region exhibits high expression of insulin and GLUT4. Additionally, disrupted glucose metabolism in the hippocampus has been associated with anxiety disorders, while impaired WNK signaling has been linked to hypertension, learning disabilities, psychiatric disorders or Alzheimer's disease. The study took advantage of selective pan-WNK inhibitor WNK 643 as the main tool to manipulate WNK 1-4 activity both in vivo by daily, per-oral drug administration to wild-type mice, and in vitro by treating either adult murine brain synaptosomes, hippocampal slices, primary cortical cultures, and human cell lines (HEK293, SH-SY5Y). Using a battery of standard behavior paradigms such as open field test, elevated plus maze test, and fear conditioning, the authors convincingly demonstrate that the inhibition of WNK1-4 results in behavior changes, especially in enhanced learning and memory of WNK643-treated mice. To shed light on the underlying molecular mechanism, the authors implemented multiple biochemical approaches including immunoprecipitation, glucose-uptake assay, surface biotylination assay, immunoblotting, and immunofluorescence. The data suggest that simultaneous insulin stimulation and WNK1-4 inhibition results in increased glucose uptake and the activity of insulin's downstream effectors, phosphorylated Akt and phosphorylated AS160. Moreover, the authors demonstrate that insulin treatment enhances the physical interaction of the WNK effector OSR1/SPAK with Akt substrate AS160. As a result, combined treatment with insulin and the WNK643 inhibitor synergistically increases the targeting of GLUT4 to the plasma membrane. Collectively, these data strongly support the initial hypothesis that neuronal insulin- and WNK-dependent pathways do interact and engage in cognitive functions.

In response to our initial comments, the authors mildly revised the manuscript, which did not improve the weaknesses to a sufficient level. Our follow-up comments are labeled under "Revisions 1".

Strengths:

The insulin-dependent signaling in the central nervous system is relatively understudied. This explorative study delves into several interesting and clinically relevant possibilities, examining how insulin-dependent signaling and its crosstalk with WNK kinases might affect brain circuits involved in memory formation and/or anxiety. Therefore, these findings might inspire follow-up studies performed in disease models for disorders that exhibit impaired glucose metabolism, deficient memory, or anxiety, such as Diabetes mellitus, Alzheimer's disease, or most of psychiatric disorders.

The graphical presentation of the figures is of high quality, which helps the reader to obtain a good overview and to easily understand the experimental design, results, and conclusions.

The behavioral studies are well conducted and provide valuable insights into the role of WNK kinases in glucose metabolism and their effect on learning and memory. Additionally, the authors evaluate the levels of basal and induced anxiety in Figures 1 and 2, enhancing our understanding of how WNK signaling might engage in cognitive function and anxiety-like behavior, particularly in the context of altered glucose metabolism.

The data presented in Figures 3 and 4 are notably valuable and robust. The authors effectively utilize a variety of in vivo and in vitro models, combining different treatments in a clear manner. The experimental design is well-controlled, efficiently communicated, and well-executed, providing the reader with clear objectives and conclusions. Overall, these data represent particularly solid and reproducible evidence on the enhanced glucose uptake, GLUT4 targeting, and downstream effectors' activation upon insulin and WNK/OSR1 signaling crosstalk.

Weaknesses:

(1) The study used a WNK643 inhibitor as the only tool to manipulate WNK1-4 activity. This inhibitor seems selective; however, it has been reported that it exhibits different efficiency in inhibiting the individual WNK kinases among each other (e.g. PMID: 31017050, PMID: 36712947). Additionally, the authors do not analyze nor report the expression profiles or activity levels of WNK1, WNK2, WNK3, and WNK4 within the relevant brain regions (i.e. hippocampus, cortex, amygdala). Combined, these weaknesses raise concerns about the direct involvement of WNK kinases within the selected brain regions and behavior circuits. It would be beneficial if the authors provided gene profiling for WNK1, 2, 3, and -4 (e.g. using Allen brain atlas). To confirm the observations, the authors should either add results from using other WNK inhibitors or, preferentially, analyze knock-down or knock-out animals/tissue targeting the single kinases.

Revisions 1: The authors added Fig. S1A during the revisions to show expression of Wnt1-4. While the expression data from humans is interesting, the experimental part of the study is performed in mice. It would be more informative for the authors to add expression profiles from mice or overview the expression pattern with suitable references in the introduction to address this point. The authors did not add data from knock down or knockout tissue targeting the single kinases.

(2) The authors do not report any data on whether the global inhibition of WNKs affects insulin levels as such. Since the authors demonstrate the synergistic effect of simultaneous insulin treatment and WNK1-4 inhibition, such data are missing.

Revisions 1: The authors added Fig. S5A to address this point. It is appreciated that authors performed the needed experiment. Unfortunately, no significant change was found, therefore, the authors still cannot conclude that they demonstrate a synergistic effect of simultaneous insulin treatment and WNT1-4 inhibition. It is a missed opportunity that the authors did not measure insulin in the CSF or tissue lysate to support the data.

(3) The study discovered that the Sortilin receptor binds to OSR1, leading the authors to speculate that Sortilin may be involved in the insulin-dependent GLUT4 surface trafficking. The authors conclude in the result section that "WNK/OSR1/SPAK influences insulin-sensitive GLUT4 trafficking by balancing GLUT4 sequestration in the TGN via regulation of Sortilin with GLUT4 release from these vesicles upon insulin stimulation via regulation of AS160." However, the authors do not provide any evidence supporting Sortilin's involvement in such regulation, thus, this conclusion should be removed from the section. Accordingly, the first paragraph of the discussion should be also rephrased or removed.

Revisions 1: The authors added Fig. 5M-N to address this point. The new experiment is appreciated. However, the authors still do not show that sortilin is involved in insulin or WNK-dependent GLUT4 trafficking in their set up since the authors do not demonstrate any changes in GLUT4 sorting or binding. The conclusions should therefore be rephrased or included purely in the discussion. Moreover, the discussion was not adjusted either, leading to over interpretation based on the available data.

(4) The background relevant to Figure 5, as well as the results and conclusions presented in Figure 5 are quite challenging to follow due to the lack of a clear introduction to the signaling pathways. Consequently, understanding the conclusions drawn from the data is also difficult. It would be beneficial if the authors addressed this issue with either reformulations or additional sections in the introduction. Furthermore, the pulldown experiments in this figure lack some of the necessary controls.

Revisions 1: The Authors insufficiently addressed this point during the revisions and did not rewrite the introduction as suggested.

(5) The authors lack proper independent loading controls (e.g. GAPDH levels) in their immunoblots throughout the paper, and thus their quantifications lack this important normalization step. The authors also did not add knock-out or knock-down controls in their co-IPs. This is disappointing since these improvements were central and suggested during the revision process.

(6) The schemes that represent only hypotheses (Fig. 1K, 4A) are unnecessary and confusing and thus should be omitted or placed at the end of each figure if the conclusions align.

(7) Low-quality images, such as Fig. 5H should be replaced with high-resolution photos, moved to the supplementary, or omitted.

Reviewer #2 (Public review):

This study by Jaykumar and colleagues seeks to expand the field's appreciation of insulin responses in the brain, specifically by implicating WNK kinase function in various neuronal responses, ranging from behavioral / memory changes to GLUT4 trafficking to the cell surface with subsequent glucose uptake. This revised study is now comprehensive and presents a logical and reasonably documented cascade of molecular interactions responsible in part for GLUT4 trafficking under the regulation of WKK and insulin. Additional data allow the authors to dissect a plausible WNK/OSR1/SPAK-sortilin pathway for the modulation of GLUT4 trafficking, in part by capitalizing on a overlay of various techniques and systems. The data - much of it in vivo or ex vivo - showing a potential role for WNK function in brain glucose utilization remains a compelling part of the story, with the dissection of the signaling cascade and a potential role for sortilin in mediating WNK function via effects on GLUT4 cellular localization now more convincing.

Initially, the group shows that oral WNK463 treatment - an inhibitor of WNKs broadly - in mice augments a number of memory readouts. These findings fit within the context of the overall story the authors present: that WNK function is critical to brain glucose utilization, which impacts learning. Multiple approaches are used to show that WNK463 treatment, i.e. inhibition of WNKs, increases glucose uptake, including labeled 2-deoxyglucose uptake in vivo in the brain and in isolated synaptosome, and uptake in ex vivo hippocampal slices. These findings are solid and consistent. With the exception of some relatively minor comments regarding the data presentation made to the authors and now fully addressed, the findings showing that WNK463 treatment increases GLUT4-mediated glucose uptake and surface localization of GLUT4 are reasonable, with the hippocampal slice data being particularly relevant.

While the details of the WNK signaling cascade is dense, in the revised application one clearly appreciates the molecular interrogation and interactions the group is dissecting, supported by the use of multiple models. With the additional findings, these systems and the data now reinforce each other, presenting a strongly documented overall story.

A limitation of the study with the initial submission was the authors' reliance upon a single pharmacological tool (WNK463) to inhibit WNK kinases. WNK463 apparently has substantial specificity for WNKs and WNK463 treatment lessened OSR1 phosphorylation (a WNK substrate). Nevertheless, the cohesiveness of the findings in terms of the broader pathway engagement (GLUT4 trafficking, glucose uptake) is consistent with the author's proposed mechanisms and conclusions. The authors have additionally addressed this concern in the revised manuscript with more information supporting the specificity of WNK463 as well as the multiple approaches to confirm the effect of WNK463 on the WNK signaling pathway of interest.

The final few paragraphs of the discussion that weave the author's findings into the field more broadly, including Sortilin function and neurological disorders, are appreciated. Additional clarity in the Methods section is also helpful.

Author response:

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

Joint Public Review:

Summary:

The major issues are the need for more information concerning WNK expression in brain regions and additional confirmation of the role of sortilin on WNT signaling. There is a lack of sufficient evidence supporting sortilin's involvement in insulin- and WNK-dependent GLUT4 regulation. The recommendation is to examine what WNK kinase is selectively expressed in the region of interest and then explore its engagement with the sortilin and GLUT4 pathways. Further identification of components of the WNK/OSr1/SPAK-sortilin pathway that regulate GLUT4 in brain slices or primary neurons will be helpful in confirming the results. The use of knock-down or knock-out models would be helpful to explore the direct interaction of the pathways. Immortalized and primary cells also represent useful models.

Together our results indicate that one or more WNK family members regulate insulin sensitivity.  As all WNK family members are expressed in relevant brain regions, whether the results are due to actions of a single WNK family member or more likely due to their combined impact will be an important question to ask in the future.  

There are multiple publications describing how sortilin is involved in insulin-dependent Glut4 trafficking; thus, we did not further address that issue.  We have added data on an additional action of WNK463 which indicates that it can block association of OSR1 with sortilin.  While these results do not delve further into how sortilin works, they support the conclusion that WNK/OSR1/SPAK can influence insulin-dependent glucose transport via distinct cellular events (AS160, sortilin, Akt) which are WNK463 sensitive.  

Altogether we added 12 new panels of data from new and previously performed experiments and we modified 3 existing subfigures in response to comments.

Weaknesses:

(1) The study used a WNK643 inhibitor as the only tool to manipulate WNK1-4 activity. This inhibitor seems selective; however, it has been reported that it exhibits different efficiency in inhibiting the individual WNK kinases among each other (e.g. PMID: 31017050, PMID: 36712947). Additionally, the authors do not analyze nor report the expression profiles or activity levels of WNK1, WNK2, WNK3, and WNK4 within the relevant brain regions (i.e. hippocampus, cortex, amygdala). Combined, these weaknesses raise concerns about the direct involvement of WNK kinases within the selected brain regions and behavior circuits. It would be beneficial if the authors provided gene profiling for WNK1, 2, 3, and -4 (e.g. using Allen brain atlas). To confirm the observations, the authors should either add results from using other WNK inhibitors or, preferentially, analyze knock-down or knock-out animals/tissue targeting the single kinases.

Thank you for the excellent suggestion to include mRNA data for the four WNKs. We have included a supplementary figure showing expression of WNK1-4 mRNAs in prefrontal cortex and the hippocampus curated from the Allen Brain Atlas. As per the Allen Brain Atlas, all four WNKs are detected in these regions with WNK4 mRNA the most highly expressed followed by WNK2, WNK3 and then WNK1 (Figure S1A).   

With regard to the use of WNK463, we continue to use WNK463 because we have examined its actions in cell lines that only express WNK1, e.g. A549 (Haman Center lung cancer RNA-seq data), and in A549 with WNK1 deleted using CRISPR in which we saw no effects of WNK463 on several assays we use for WNK1 including suppression of autophagy.  WNK463 was reported in the literature to inhibit only the four WNKs out of more than 400 kinases tested, indicating more selectivity than many small molecules used to target other enzymes.  In other cell lines, we also use WNK1 knockdown which replicates the effect of WNK463 (Figure S7A-D). However, in SHSY5Y cells, WNK1 knockdown did not replicate the effect of WNK463 on pAKT levels (Figure S7E-F), suggesting a cooperativity among other WNK family members in neuronal cells. This makes WNK463 an ideal tool to test our hypotheses in this study as it targets all 4 WNKs (WNK1-4).  

(2) The authors do not report any data on whether the global inhibition of WNKs affects insulin levels. Since the authors wish to demonstrate the synergistic effect of simultaneous insulin treatment and WNK1-4 inhibition, such data are missing.

Thank you for this comment. To obtain this information, we treated C57BL/6J mice with WNK463 for 3 days once daily at a dose of 6 mg/kg and then fasted overnight. Plasma insulin levels were measured. Results showed that the plasma insulin levels trended upwards in the WNK463 treated animals compared to the vehicle treated groups but failed to reach any statistical significance. We have now included these data in supplementary figure S5A.

The study discovered that the Sortilin receptor binds to OSR1, leading the authors to speculate that Sortilin may be involved in the insulin-dependent GLUT4 surface trafficking. However, the authors do not provide any evidence supporting Sortilin's involvement in insulin- or WNKdependent GLUT4 trafficking. Thus, this conclusion should be qualified, rephrased, or additional data included.

Work from several groups have shown that sortilin is involved in insulin-dependent GLUT4 trafficking, for example [9-11,135-139] as we noted in the manuscript. We now show that WNK463 blocks co-immunoprecipitation of Flag-tagged sortilin with endogenous OSR1 in HEK293T cells. This result supports our model for WNK/OSR1/SPAK- insulin mediated regulation of sortilin.  We included these data in figures 5M, 5N.

Minor issues:

(1) The method and result sections lack information regarding the gender and age of mice used in the behavioral experiments. This information should be added.

Thank you for pointing this out. We apologize for the omission. The requested information has now been added in the methods section.

(2) The authors present an analysis of relative protein levels in Figure 1B and Figure 4B, however, the original immunoblots (?) are not included in the study. These data should be added to provide complete and transparent evidence for the analysis.

Thank you for this request. The blots have now been included in the supplementary figure S2A and Figure 4B, respectively.  

(3) The basis for Figure 3A needs to be explained and supported with suitable references either in the background or in the result section.

Thank you for pointing this out. Figure 3A has been moved to Figure 3H as it represents the model summary of the data presented in Figure 3. Other figure numbers have been changed accordingly.  This figure 3A (now 3H) and the model diagram of Figure 5 (now Figure 5O) are now cited in the Discussion, where the results are considered in detail.      

(4) Figure 4E should be labeled as 'Primary cortical neurons' for clarity, as the major focus is on the hippocampus. To increase consistency, the authors should consider performing the same experiment on hippocampal cultures or explaining using cortical neurons.

Thank you for the suggestion. Figure 4E (now 4F) has been labelled as Primary cortical neurons for clarity. The major focus of this study is to understand the regulation of WNKmediated regulation of insulin signaling in the areas of the brain that are insulin sensitive such as the hippocampus and the prefrontal cortex. Therefore, we included cortical neurons to test this hypothesis.  

(5) Figure 5B: The use of whole brain extracts is inconsistent with the rest of the study, especially considering the indication of differing insulin activity in selected brain regions. The authors should explain why they could not use only hippocampal tissue.

In this manuscript, we are trying to test our hypothesis in insulin-sensitive neuronal cells which includes, but not limited to, the hippocampus. Figure 5B used whole brain extracts, which contain brain regions that are insulin-sensitive as well as insulin-insensitive regions, to show the association between OSR1 and AS160. However, this observation was replicated in the insulin-sensitive SH-SY5Y cell model suggesting that association of OSR1 and AS160 is modulated in the presence of insulin as shown in Figure 5B, 5C. We added data from SH-SY5Y cells showing effects of WNK463. These data support the concept that this is an interaction that is modulated by WNKs and will occur as long as both OSR1/SPAK and AS160 are expressed.

(6) Figure 5B-C - Knock-out or knock-down condition should be included in the co-IP experiment. This is especially straightforward to generate in the SH-SY5Y cells. Moreover, these figures lack loading controls.

If we understand correctly, the issue with regard to including knockdown conditions stems from the issues raised regarding specificity of the antibody which we have addressed in point 10 below. We have now included input blots for both AS160 and OSR1 which serve as the loading control for the IP experiment in figure 5B and 5C.

(7) Figure 5C-D - A condition with WNK463 inhibition alone is missing. This condition is necessary for evaluating the effects of WNK643 inhibition with and without insulin stimulation.

Thank you for this observation. We have now added the data for that condition.  The aim of this experiment in Figure 5C (now 5B and 5C) is to show that insulin is important to facilitate interaction between OSR1 and AS160 in differentiated SHSY5Y cells and the effect of WNK463 to diminish this insulin-dependent interaction. With only WNK463, there was minimal interaction between AS160 and OSR1 as now shown in Figure 5B, 5C.

(8) Figure 5G - This figure shows the overexpression of plasmids in HEK cells, however, it lacks samples that overexpress the plasmid individually (single expression). Such data should be added, especially when the addition of the blocking peptide does not fully disable the interaction between AS160 and SPAK. Additionally, this figure also lacks a loading control, which is essential for validating the results.

Thank you for this comment. Figure 5G (now Figure 5F, 5G) is an in vitro IP in which we have mixed a purified Flag-SPAK fragment residues 50-545 with a lysate from cells expressing Myc-AS160 (residues 193-446). This is essentially an in vitro IP; because it is not an IP experiment from cell lysates where we overexpressed these plasmids which would require a loading control. The lysates were divided in half and one half did not receive the blocking peptide while the other half did, creating a control. From our experience, this blocking peptide does not completely block interactions between SPAK/OSR1 and NKCC2 fragments which are well-characterized interacting partners [a]. The reason for the partial block in interactions could also be attributed to the multivalent nature of interaction between these proteins. This confusion in our methodology used has been noted and we have tried to explain it with more clarity in the methods, results and the figure legend section. Our Commun. Biol. paper [134] that describes this assay and uses it extensively is now available online.

(a) Piechotta K, Lu J, Delpire E. Cation chloride cotransporters interact with the stressrelated kinases Ste20-related proline-alanine-rich kinase (SPAK) and oxidative stress response 1 (OSR1) J Biol Chem. 2002;277:50812–50819. doi: 10.1074/jbc.M208108200.

(9) Figure 5J, L - These figures are missing negative controls. The authors should add Sortilin knock-down or knock-out conditions for the immunoprecipitation experiments. Also, the figures lack loading controls. Moreover, the labeling "Control" should be specified, as it is unclear what this condition represents.

Thank you for noting the lack of clarity in the controls provided. Controls in Figure 5J and 5L refer to IgG Control which serves as the negative control in this case. This has now been specified in the figures (and added Figures 5M and 5N, as well). The issue with OSR1 and sortilin antibody specificity and cross-reaction has been addressed in point 10.

(10) Figure 5I - The fluorescent signals for the individual channels of OSR1 and Sortilin appear identical (even within the background signal). This raises concerns about potential antibody cross-reaction. One potential solution would be to include additional stainings with different antibodies and perform staining of each protein alone to ensure the specificity of the colocalization.

Thank you for pointing this out and giving us an opportunity to provide better images that will address the issues raised regarding antibody cross-reaction and antibody specificity. We realize that the images that we originally provided appeared to show all the puncta colocalize which could give rise to the concern about potential antibody cross-reaction. We have replaced them with more appropriate representative images that clearly show some selected regions of common staining as well as regions where there is no overlap.  

(11) Figures 5D, 5F, 5H, 5L, 5M: These analyses should be first normalized to the loading control such as GAPDH.

In Figure 5F (now 5E), the analysis has been normalized to the total AS160 protein levels. Because we are reporting changes in pAS160 protein, normalizing it to the total AS160 gives a better idea about the changes in the phosphorylated AS160 form compared to the whole protein and this is more appropriate compared to other loading controls such as GAPDH.  

In Figure 5H (now Figure 5G), the analysis is an in vitro IP assay using purified protein fragments. Therefore, using GAPDH as a control is not applicable in this case. Please refer to our response to comment 8 for details.

In Figures 5L, 5M and 5D (now 5K, 5L, 5C) shown, the IP proteins have been normalized to the input protein levels serving as a loading control for the IP experiment. 

(12) Figure 5K: The significance/meaning of the red star is unclear. It should be explained in the figure legend.

Thank you for the opportunity to enhance the readability of our manuscript. The meaning of red star denotes the condition in the yeast two-hybrid assay which shows the binding of CCT of OSR1 with C-terminus of sortilin. This has now been clarified in the figure legend.

(13) Differences in WNK643 dosage and administration periods can affect the results. There is a lack of explanation with regard to the divergent WNK643 treatments of mice across different behavior conditions of fear conditioning, the novel object test, and the elevated plus maze test. This should be considered.

Thank you for pointing out that the explanation regarding the WNK463 dosage and times are unclear. WNK463 was dosed 3 days before the start of the behavior experiment daily at a dose of 6 mg/kg and continued throughout the test protocol. This is the same protocol used for all experiments.  The text describing the protocol has been reworded with more clarity on dosage and times in methods and result section.

eLife Assessment

This study provides valuable data on the role of Hsd17b7, a gene involved in cholesterol biosynthesis, as a potential regulator of mechanosensory hair cell function. The authors used both zebrafish and the HEI cell line to examine the effects of deletion of Hsd17b7 on hair cell function and survival. While the results do show a reduction in hair cells in the lateral line neuromasts of Hsd17b7 mutant fish, the reduction was limited. The findings are considered incomplete, with additional experiments required to confirm the conclusions.

Reviewer #1 (Public review):

Summary:

This study identifies HSD17B7 as a cholesterol biosynthesis gene enriched in sensory hair cells, with demonstrated importance for auditory behavior and potential involvement in mechanotransduction. Using zebrafish knockdown and rescue experiments, the authors show that loss of hsd17b7 reduces cholesterol levels and impairs hearing behavior. They also report a heterozygous nonsense variant in a patient with hearing loss. The gene mutation has a complex and somewhat inconsistent phenotype, appearing to mislocalize, reduce mRNA and protein levels, and alter cholesterol distribution, supporting HSD17B7 as a potential deafness gene.

While the study presents an interesting candidate and highlights an underexplored role for cholesterol in hair cell function, several important claims are insufficiently supported, and the mechanistic interpretations remain somewhat murky.

Strengths:

(1) HSD17B7 is a new candidate deafness gene with plausible biological relevance.

(2) Cross-species RNAseq convincingly shows hair-cell enrichment.

(3) Lipid metabolism, particularly cholesterol homeostasis, is an emerging area of interest in auditory function.

(4) The connection between cholesterol levels and MET is potentially impactful and, if substantiated, would represent a significant advance.

Weaknesses:

(1) The pathogenic mechanism of the E182STOP variant is unclear: The mutant protein presumably does not affect WT protein localization, arguing against a dominant-negative effect. Yet, overexpression of HSD17B7-E182* alone causes toxicity in zebrafish, and it binds and mislocalizes cholesterol in HEI-OC1 cells, suggesting some gain-of-function or toxic effect. In addition, the mRNA of the variant has a low expression level, suggesting nonsense-mediated decay. This complexity and inconsistency need clearer explanation.

(2) The link to human deafness is based on a single heterozygous patient with no syndromic features. Given that nearly all known cholesterol metabolism disorders are syndromic, this raises concerns about causality or specificity. The term "novel deafness gene" is premature without additional cases or segregation data.

(3) The localization of HSD17B7 should be clarified better: In HEI-OC1 cells, HSD17B7 localizes to the ER, as expected. In mouse hair cells, the staining pattern is cytosolic and almost perfectly overlaps with the hair cell marker used, Myo7a. This needs to be discussed. Without KO tissue, HSD17B7 antibody specificity remains uncertain.

Reviewer #2 (Public review):

A summary of what the authors were trying to achieve.

The authors aim to determine whether the gene Hsb17b7 is essential for hair cell function and, if so, to elucidate the underlying mechanism, specifically the HSB17B7 metabolic role in cholesterol biogenesis. They use animal, tissue, or data from zebrafish, mouse, and human patients.

Strengths:

(1) This is the first study of Hsb17b7 in the zebrafish (a previous report identified this gene as a hair cell marker in the mouse utricle).

(2) The authors demonstrate that Hsb17b7 is expressed in hair cells of zebrafish and the mouse cochlea.

(3) In zebrafish larvae, a likely KO of the Hsb17b7 gene causes a mild phenotype in an acoustic/vibrational assay, which also involves a motor response.

(4) In zebrafish larvae, a likely KO of the Hsb17b7 gene causes a mild reduction in lateral line neuromast hair cell number and a mild decrease in the overall mechanotransduction activity of hair cells, assayed with a fluorescent dye entering the mechanotransduction channels.

(5) When HSB17B7 is overexpressed in a cell line, it goes to the ER, and an increase in Cholesterol cytoplasmic puncta is detected. Instead, when a truncated version of HSB17B7 is overexpressed, HSB17B7 forms aggregates that co-localize with cholesterol.

(6) It seems that the level of cholesterol in crista and neuromast hair cells decreases when Hsb17b7 is defective (but see comment below).

Weakness:

(1) The statement that HSD17B7 is "highly" expressed in sensory hair cells in mice and zebrafish seems incorrect for zebrafish:

(a) The data do not support the notion that HSB17B7 is "highly expressed" in zebrafish. Compared to other genes (TMC1, TMIE, and others), the HSB17B7 level of expression in neuromast hair cells is low (Figure 1F), and by extension (Figure 1C), also in all hair cells. This interpretation is in line with the weak detection of an mRNA signal by ISH (Figure 1G I"). On this note, the staining reported in I" does not seem to label the cytoplasm of neuromast hair cells. An antisense probe control, along with a positive control (such as TMC1 or another), is necessary to interpret the ISH signal in the neuromast.

(b) However, this is correct for mouse cochlear hair cells, based on single-cell RNA-seq published databases and immunostaining performed in the study. However, the specificity of the anti-HSD17B7 antibody used in the study (in immunostaining and western blot) is not demonstrated. Additionally, it stains some supporting cells or nerve terminals. Was that expression expected?

(2) A previous report showed that HSD17B7 is expressed in mouse vestibular hair cells by single-cell RNAseq and immunostaining in mice, but it is not cited:

Spatiotemporal dynamics of inner ear sensory and non-sensory cells revealed by single-cell transcriptomics.

Jan TA, Eltawil Y, Ling AH, Chen L, Ellwanger DC, Heller S, Cheng AG.

Cell Rep. 2021 Jul 13;36(2):109358. doi: 10.1016/j.celrep.2021.109358.

(3) Overexpressed HSD17B7-EGFP C-terminal fusion in zebrafish hair cells shows a punctiform signal in the soma but apparently does not stain the hair bundles. One limitation is the consequence of the C-terminal EGFP fusion to HSD17B7 on its function, which is not discussed.

(4) A mutant Zebrafish CRISPR was generated, leading to a truncation after the first 96 aa out of the 340 aa total. It is unclear why the gene editing was not done closer to the ATG. This allele may conserve some function, which is not discussed.

(5) The hsd17b7 mutant allele has a slightly reduced number of genetically labeled hair cells (quantified as a 16% reduction, estimated at 1-2 HC of the 9 HC present per neuromast). On a note, it is unclear what criteria were used to select HC in the picture. Some Brn3C:mGFP positive cells are apparently not included in the quantifications (Figure 2F, Figure 5A).

(6) The authors used FM4-64 staining to evaluate the hair cell mechanotransduction activity indirectly. They found a 40% reduction in labeling intensity in the HCs of the lateral line neuromast. Because the reduction of hair cell number (16%) is inferior to the reduction of FM4-64 staining, the authors argue that it indicates that the defect is primarily affecting the mechanotransduction function rather than the number of HCs. This argument is insufficient. Indeed, a scenario could be that some HC cells died and have been eliminated, while others are also engaged in this path and no longer perform the MET function. The numbers would then match. If single-cell staining can be resolved, one could determine the FM4-64 intensity per cell. It would also be informative to evaluate the potential occurrence of cell death in this mutant. On another note, the current quantification of the FM4-64 fluorescence intensity and its normalization are not described in the methods. More importantly, an independent and more direct experimental assay is needed to confirm this point. For example, using a GCaMP6-T2A-RFP allele for Ca2+ imaging and signal normalization.

(7) The authors used an acoustic startle response to elicit a behavioral response from the larvae and evaluate the "auditory response". They found a significative decrease in the response (movement trajectory, swimming velocity, distance) in the hsd17b7 mutant. The authors conclude that this gene is crucial for the "auditory function in zebrafish".

This is an overstatement:

(a) First, this test is adequate as a screening tool to identify animals that have lost completely the behavioral response to this acoustic and vibrational stimulation, which also involves a motor response. However, additional tests are required to confirm an auditory origin of the defect, such as Auditory Evoked Potential recordings, or for the vestibular function, the Vestibulo-Ocular Reflex.

(b) Secondly, the behavioral defects observed in the mutant compared to the control are significantly different, but the differences are slight, contained within the Standard Deviation (20% for velocity, 25% for distance). To this point, the Figure 2 B and C plots are misleading because their y-axis do not start at 0.

(8) Overexpression of HSD17B7 in cell line HEI-OC1 apparently "significantly increases" the intensity of cholesterol-related signal using a genetically encoded fluorescent sensor (D4H-mCherry). However, the description of this quantification (per cell or per surface area) and the normalization of the fluorescent signal are not provided.

(9) When this experiment is conducted in vivo in zebrafish, a reduction in the "DH4 relative intensity" is detected (same issue with the absence of a detailed method description). However, as the difference is smaller than the standard deviation, this raises questions about the biological relevance of this result.

(10) The authors identified a deaf child as a carrier of a nonsense mutation in HSB17B7, which is predicted to terminate the HSB17B7 protein before the transmembrane domain. However, as no genetic linkage is possible, the causality is not demonstrated.

(11) Previous results obtained from mouse HSD17B7-KO (citation below) are not described in sufficient detail. This is critical because, in this paper, the mouse loss-of-function of HSD17B7 is embryonically lethal, whereas no apparent phenotype was reported in heterozygotes, which are viable and fertile. Therefore, it seems unlikely that heterozygous mice exhibit hearing loss or vestibular defects; however, it would be essential to verify this to support the notion that the truncated allele found in one patient is causal.

Hydroxysteroid (17beta) dehydrogenase 7 activity is essential for fetal de novo cholesterol synthesis and for neuroectodermal survival and cardiovascular differentiation in early mouse embryos.

Jokela H, Rantakari P, Lamminen T, Strauss L, Ola R, Mutka AL, Gylling H, Miettinen T, Pakarinen P, Sainio K, Poutanen M.<br /> Endocrinology. 2010 Apr;151(4):1884-92. doi: 10.1210/en.2009-0928. Epub 2010 Feb 25.

(12) The authors used this truncated protein in their startle response and FM4-64 assays. First, they show that contrary to the WT version, this truncated form cannot rescue their phenotypes when overexpressed. Secondly, they tested whether this truncated protein could recapitulate the startle reflex and FM4-64 phenotypes of the mutant allele. At the homozygous level (not mentioned by the way), it can apparently do so to a lesser degree than the previous mutant. Again, the differences are within the Standard Deviation of the averages. The authors conclude that this mutation found in humans has a "negative effect" on hearing, which is again not supported by the data.

(13) The authors looked at the distribution of the HSB17B7 in a cell line. The WT version goes to the ER, while the truncated one forms aggregates. An interesting experiment consisted of co-expressing both constructs (Figure S6) to see whether the truncated version would mislocalize the WT version, which could be a mechanism for a dominant phenotype. However, this is not the case.

(14) Through mass spectrometry of HSB17B7 proteins in the cell line, they identified a protein involved in ER retention, RER1. By biochemistry and in a cell line, they show that truncated HSB17B7 prevents the interaction with RER1, which would explain the subcellular localization.

Hydroxysteroid (17beta) dehydrogenase 7 activity is essential for fetal de novo cholesterol synthesis and for neuroectodermal survival and cardiovascular differentiation in early mouse embryos.

Jokela H, Rantakari P, Lamminen T, Strauss L, Ola R, Mutka AL, Gylling H, Miettinen T, Pakarinen P, Sainio K, Poutanen M.<br /> Endocrinology. 2010 Apr;151(4):1884-92. doi: 10.1210/en.2009-0928. Epub 2010 Feb 25.

(15) Information and specificity validation of the HSB17B7 antibody are not presented. It seems that it is the same used on mice by IF and on zebrafish by Western. If so, the antibody could be used on zebrafish by IF to localize the endogenous protein (not overexpression as done here). Secondly, the specificity of the antibody should be verified on the mutant allele. That would bring confidence that the staining on the mouse is likely specific.

eLife Assessment

Zebra finches are a prominent model system for vocal learning and auditory system function, yet little is known about the functional development of the auditory system. Here, the authors convincingly show that newly hatched zebra finches lack detectable auditory brainstem responses and that auditory neural signals emerge only days after hatching, challenging influential claims of prenatal acoustic communication in altricial birds. This important work clarifies the developmental timeline for auditory communication and highlights the value of neuroscientific methods for validating and complementing behavioral ecological studies of animal perception.

Reviewer #1 (Public review):

This work by Antonnen et al. was triggered by claims of auditory-mediated effects on altricial avian embryos, which were published without any direct evidence that the relevant parental vocalizations were actually heard. I agree with Anttonen et al. that, based on the available evidence about avian auditory development, those claims are highly speculative and therefore necessitate more direct experimental verification.

Attonen et al. have embarked on a comprehensive series of experiments to:

(1) Better characterize acoustically the relevant parental vocalizations (heat whistles; in a separate preprint, not reviewed here)

(2) Characterize the auditory sensitivity of zebra finches at various stages of their posthatching development. Despite the long-standing importance of the zebra finch as a songbird model in neuroethology of learned vocalizations, the auditory development of the species has not been studied so far.

(3) Explore an alternative hypothesis of how the parental vocalizations might be perceived.

The principal method used here is the non-invasive recording of ABR (auditory brainstem response), a standard neurophysiological method in auditory research. The click-evoked ABR provides a quick and objective assessment of basic hearing sensitivity that does not require animal training. Weaknesses of the technique include its limited frequency specificity and low signal-to-noise ratio. The authors are experienced with ABR measurements and well aware of those issues. ABR responses in zebra finches are shown to gradually appear during the first week posthatching and to mature in subsequent weeks, consistent with the auditory development in other altricial bird species studied previously. When matching the acoustic properties of parental heat whistles and auditory sensitivities, hearing of the parental heat whistles by zebra finch hatchlings was convincingly excluded. Although not directly measured, this also convincingly extrapolates to zebra finch embryos. Finally, the authors tested the hypothesis that parental heat whistles could induce perceptible vibrations of the egg and thus stimulate the embryo via a different modality. The method used here was laser doppler vibrometry, an appropriate, state-of-the-art technique that the authors also have proven experience with. The induced vibrations were shown to be several orders of magnitude below known vibrotactile sensitivities in mammals and birds. Thus, although zebra finch vibrotactile thresholds were not obtained directly, the hypothesis of vibrotactile perception of parental heat whistles by zebra finch embryos could also be rejected convincingly.

In summary, even when considering some weaknesses of the techniques (which the authors are aware of), the conclusions of the paper are well supported: Auditory and/or vibration perception of parental heat whistles can be excluded as an explanation for previous reports of developmental programming for high ambient temperatures. As a constructive suggestion towards resolving the apparent paradox, the authors recommend repeating some of the crucial, previous playback experiments at lower sound levels that better match the natural parental vocalizations.

Reviewer #2 (Public review):

This study by Anttonen, Christensen-Dalsgaard, and Elemans describes the development of hearing thresholds in an altricial songbird species, the zebra finch. The results are very clear and along what might have been expected for altricial birds: at hatch (2 days post-hatch), the chicks are functionally deaf. Auditory evoked activity in the form of auditory brainstem responses (ABR) can start to be detected at 4 days post-hatch, but only at very loud sound levels. The study also shows that ABR response matures rapidly and reaches adult-like properties around 25 days post-hatch. The functional development of the auditory system is also frequency dependent, with a low-to-high frequency time course. All experiments are very well performed. The careful study throughout development and with the use of multiple time-points early in development is important to further ensure that the negative results found right after hatching are not the result of the experimental manipulation. The results themselves could be classified as somewhat descriptive, but, as the authors point out, they are particularly relevant and timely. Since 2016, there have been a series of studies published in high-profile journals that have presumably shown the importance of prenatal acoustic communication in altricial birds, mostly in zebra finches. This early acoustic communication would serve various adaptive functions. Although acoustic communication between embryos in the egg and parents has been shown in precocial birds (and crocodiles), finding an important function for prenatal communication in altricial birds came as a surprise. Unfortunately, none of those studies performed a careful assessment of the chicks' hearing abilities. This is done here, and the results are clear: zebra finches at 2 and 6 days post-hatch are functionally deaf. Since it is highly improbable that the hearing in the egg is more developed than at birth, one can only conclude that zebra finches in the egg (or at birth) cannot hear the heat whistles. The paper also ruled out the detection on egg vibrations as an alternative path. The prior literature will have to be corrected, or further studies conducted to solve the discrepancies. For this purpose, the "companion" paper on bioRxiv that studies the bioacoustical properties of heat calls from the same group will be particularly useful. Researchers from different groups will be able to precisely compare their stimuli.

Beyond the quality of the experiments, I also found that the paper was very well written. The introduction was particularly clear and complete (yet concise).

Weaknesses:

My only minor criticism is that the authors do not discuss potential differences between behavioral audiograms and ABRs. Optimally, one would need to repeat the work of Okanoya and Dooling with your setup and using the same calibration. The ~20dB difference might be real, or it might be due to SPL measured with different instruments, at different distances, etc. Either way, you could add a sentence in the discussion that states that even with the 20 dB difference in audiogram heat whistles would not be detected during the early days post-hatch. But adding a (novel) behavioral assay in young birds could further resolve the issue.

More Minor Points:

(1) As mentioned in the main text, the duration of pips (from pips to bursts) affects the effective bandwidth of the stimulus. I believe that the authors could give an estimate of this effective bandwidth, given what is known from bird auditory filters. I think that this estimate could be useful to compare to the effective bandwidth of the heat-call, which can now also be estimated.

(2) Figure 5b. Label the green and pink areas as song and heat-call spectrum. Also note that in the legend the authors say: "Green and red areas display the frequency windows related to the best hearing sensitivity of zebra finches and to heat calls, respectively". I don't think this is what they meant. I agree that 1-4 kHz is the best frequency sensitivity of zebra finches, but they probably meant green == "song frequency spectrum" and pink == "heat call spectrum". In either case, the figure and the legend need clarification.

(3) Figure 5c. Here also, I would change the song and heat-call labels to "song spectrum", "heat call spectrum". The authors would not want readers to think that they used song and heat calls in these experiments (maybe next time?). For the same reason, maybe in 5a you could add a cartoon of the oscillogram of a frequency sweep next to your speaker.

(4) Methods. In the description of the stimulus, the authors describe "5ms long tone bursts", but these are the tone pips in the main part of the manuscript. Use the same terms.

Reviewer #3 (Public review):

Summary

Following recent findings that exposure to natural sounds and anthropogenic noise before hatching affects development and fitness in an altricial songbird, this study attempts to estimate the hearing capacities of zebra finch nestlings and the perception of high frequencies in that species. It also tries to estimate whether airborne sound can make zebra finch eggs vibrate, although this is not relevant to the question.

Strength

That prenatal sounds can affect the development of altricial birds clearly challenges the long-held assumption that altricial avian embryos cannot hear. However, there is currently no data to support that expectation. Investigating the development of hearing in songbirds is therefore important, even though technically challenging. More broadly, there is accumulating evidence that some bird species use sounds beyond their known hearing range (especially towards high frequencies), which also calls for a reassessment of avian auditory perception.

Weaknesses

Rather than following validated protocols, the study presents many experimental flaws and two major methodological mistakes (see below), which invalidate all results on responses to frequency-specific tones in nestlings and those on vibration transmission to eggs, as well as largely underestimating hearing sensitivity. Accordingly, the study fails to detect a response in the majority of individuals tested with tones, including adults, and the results are overall inconsistent with previous studies in songbirds. The text throughout the preprint is also highly inaccurate, often presenting only part of the evidence or misrepresenting previous findings (both qualitatively and quantitatively; some examples are given below), which alters the conclusions.

Conclusion and impact

The conclusion from this study is not supported by the evidence. Even if the experiment had been performed correctly, there are well-recognised limitations and challenges of the method that likely explain the lack of response. The preprint fails to acknowledge that the method is well-known for largely underestimating hearing threshold (by 20-40dB in animals) and that it may not be suitable for a 1-gram hatchling. Unlike what is claimed throughout, including in the title, the failure to detect hearing sensitivity in this study does not invalidate all previous findings documenting the impacts of prenatal sound and noise on songbird development. The limitations of the approach and of this study are a much more parsimonious explanation. The incorrect results and interpretations, and the flawed representation of current knowledge, mean that this preprint regrettably creates more confusion than it advances the field.

Detailed assessment

For brevity, only some references are included below as examples, using, when possible, those cited in the preprint (DOI is provided otherwise). A full review of all the studies supporting the points below is beyond the scope of this assessment.

(A) Hearing experiment

The study uses the Auditory Brainstem Response (ABR), which measures minute electrical signals transmitted to the surface of the skull from the auditory nerve and nuclei in the brainstem. ABR is widely used, especially in humans, because it is non-invasive. However, ABR is also a lot less sensitive than other methods, and requires very specific experimental precautions to reliably detect a response, especially in extremely small animals and with high-frequency sounds, as here.

(1) Results on nestling frequency sensitivity are invalid, for failing to follow correct protocols:

The results on frequency testing in nestlings are invalid, since what might serve as a positive control did not work: in adults, no response was detected in a majority of individuals, at the core of their hearing range, with loud 95dB sounds (Figure S1), when testing frequency sensitivity with "tone burst".

This is mostly because the study used a stimulation duration 5 times larger than the norm. It used 25ms tone bursts, when all published avian studies (in altricial or precocial birds) used stimulation of 5ms or less (when using subdermal electrodes as here; e.g., cited: Brittan-Powell et al 2004; not cited: Brittan-Powell et al 2002 (doi: 10.1121/1.1494807), Henry & Lucas 2008 (doi: 10.1016/j.anbehav.2008.08.003)). Long stimulations do not make sense and are indeed known to interfere with the detection of an ABR response, especially at high frequencies, as, for example, explicitly tested and stated in Lauridsen et al 2021 (cited).

Adult response was then re-tested with a correct 5ms tone duration ("tone-pip"), which showed that, for the few individuals that responded to 25ms tones, thresholds were abnormally high (c.a. by 30dB; Figure 2C).<br /> Yet, no nestlings were retested with a correct protocol. There is therefore no valid data to support any conclusion on nestling frequency hearing. Under these circumstances, the fact that some nestlings showed a response to 25ms tones from day 8 would argue against them having very low sensitivity to sound.

(2) Responses to clicks underestimate hearing onset by several days:

Without any valid nestling responses to tones (see # 1), establishing the onset of hearing is not possible based on responses to clicks only, since responses to clicks occur at least 4 days after responses to tones during development (Saunders et al, 1973). Here, 60% of 4-day-old individuals responding to clicks means most would have responded to tones at and before 2 days post-hatch, had the experiment been done correctly.<br /> Responses to tones are indeed observed in other songbirds at 1day post-hatch (see #6).

In budgerigars, hearing onset occurs before 5 days post hatch, since responses to both clicks and tones were detectable at the first age tested at 5dph (Brittan-Powell et al, 2004).

(3) Experimental parameters chosen lower ABR detectability, specifically in younger birds:

Very fast stimulus repetition rate inhibits the ABR response, especially in young:

(a) The stimulus presentation rate (25 stim/ sec) is 6 times faster than zebra finch heat-calls, and 5 to 25 times faster than most previous studies in young birds (e.g., cited: Saunders et al 1973, 1974: 1 stim/sec or less; Katayama 1985: 3.3 clicks/sec; Brittan-Powell et al 2004: 4 stim/sec). Faster rates saturate the neurons and accordingly are known to decrease ABR amplitude and increase ABR latency, especially in younger animals with an immature nervous system. In birds, this occurs especially in the range from 5 to 30 stim/sec (e.g., cited: Saunder et al 1973, Brittan-Powell et al 2004). Values here with 25 rather than 1-4 stim/min are therefore underestimating true sensitivity.

(b) Averaging over only 400 measures is insufficient to reliably detect weak ABR signals:

The study uses 2 to 3 times fewer measures per stimulation type than the recommended value of 1,000 (e.g., Brittan-Powell et al 2002, 2024; Henry & Lucas 2008). This specifically affects the detection of weak signals, as in small hatchlings with tiny brains (adult zebra finches are 12-14g).

(c) Body temperature is not specified and strongly affects the ABR:

Controlling the body temperature of hatchlings of 1-4 grams (with a temperature probe under a 5mm-wide wing) would be very challenging. Low body temperature entirely eliminates the ABR, and even slight deviance from optimal temperature strongly increases wave latency and decreases wave amplitude (e.g., cited: Katayama 1985).

(d) Other essential information is missing on parameters known to affect the ABR:

This includes i) the weight of the animals, ii) whether and how the response signal was amplified and filtered, iii) how the automatised S/N>2 criteria compared to visual assessment for wave detection, and iv) what measures were taken to allow the correct placement of electrodes on hatchlings less than 5 grams.

(4) Results in adults largely underestimate sensitivity at high frequencies, and are not the correct reference point:

(a) Thresholds measured here at high frequencies for adults (using the correct stimulus duration, only done on adults) are 10-30dB higher than in all 3 other published ABR studies in adult zebra finches (cited: Zevin et al 2004; Amin et al 2007; not cited: Noirot et al 2011 (10.1121/1.3578452)), for both 4 and 6 kHz tone pips.

(b) The underlying assumption used throughout the preprint that hearing must be adult-like to be functional in nestlings does not make sense. Slower and smaller neural responses are characteristic of immature systems, but it does not mean signals are not being perceived.

(5) Failure to account for ABR underestimation leads to false conclusions:

(a) Whether the ABR method is suitable to assess hearing in very small hatchlings is unknown. No previous avian study has used ABR before 5 days post-hatch, and all have used larger bird species than the zebra finch.

(b) Even when performed correctly on large enough animals, the ABR systematically underestimates actual auditory sensitivity by 20-40 dB, especially at high frequencies, compared to behavioural responses (e.g., none cited: Brittan-Powell et al 2002, Henry & Lucas 2008, Noirot et al 2011). Against common practice, the preprint fails to account for this, leading to wrong interpretations. For example, in Figure 1G (comparing to heat call levels), actual hearing thresholds would be 30-40dB below those displayed. In addition, the "heat whistle" level displayed here (from the same authors) is 15dB lower than their second measure that they do not mention, and than measures obtained by others (unpublished data). When these two corrections are made - or even just the first one - the conclusion that heat-call sound levels are below the zebra finch hearing threshold does not hold.

(c) Rather than making appropriate corrections, the preprint uses a reference in humans (L180), where ABR is measured using a much more powerful method (multi-array EEG) than in animals, and from a larger brain. The shift of "10-20dB" obtained in humans is not applicable to animals.

(6) Results are inconsistent with previous findings in developing songbirds:

As expected from all of the above, results and conclusions in the preprint are inconsistent with findings in other songbirds, which, using other methods, show for example, auditory sensitivity in:

(a) zebra finch embryos, in response to song vs silence (not cited: Rivera et al 2018, doi: 10.1097/WNR.0000000000001187)

(b) flycatcher hatchlings at 2-3d post hatch (first age tested), across a wide range of frequencies (0.3 to 5kHz), at low to moderate sound levels (45-65dB) (cited: Aleksandrov and Dmitrieva 1992, not cited: Korneeva et al 2006 (10.1134/S0022093006060056)).

(c) songbird nestlings at 2-6d post hatch, which discriminate and behaviourally respond to relevant parental calls or even complex songs. This level of discrimination requires good hearing across frequencies (e.g., not cited: Korneeva et al 2006; Schroeder & Podos 2023 (doi: 10.1016/j.anbehav.2023.06.015)).

(d) zebra finch nestlings at 13d post-hatch, which show adult-like processing of songs in the auditory cortex (CNM) (Schroeder & Remage‐Healey 2021, doi: 10.1002/dneu.22802).

(e) zebra finch juveniles, which are able to perceive and learn song syllables at 5-7kHz (fundamental frequency) with very similar acoustic properties to heat calls, and also produced during inspiration (Goller & Daley 2001, doi: 10.1098/rspb.2001.1805).

NONE of these results - which contradict results and claims in the preprint - are mentioned. Instead, the preprint focuses on very slow-developing species (parrots and owls), which take 2-4 times longer than songbirds to fledge (cited: Brittan-Powell et al 2004; Köppl & Nickel 2007; Kraemer et al 2017).

(7) Results in figures are misreported in the text, and conclusions in the abstract and headers are not supported by the data:

For example:

(a) The data on Figure 1E shows that at 4 days old, 8 out of 13 nestlings (60%) responded to clicks, but the text says only 5/13 responded (L89). When 60% (4dph) and 90% (6dph) of individuals responded, the correct term would be that "most animals", rather than "some animals" responded (L89). Saying that ABR to loud sound appeared "in the majority only after one week" (L93) is also incorrect, given the data. It follows that the title of the paragraph is also erroneous.

(b) The hearing threshold is underestimated by 40dB at 6 and 8Kz on Fig 2C, not by "10-20dB" as reported in the text (L178).

(B) Egg vibration experiment

(8) Using airborne sound to vibrate eggs is biologically irrelevant:

The measurement of airborne sound levels to vibrate eggs misunderstands bone conduction hearing and is not biologically meaningful: zebra finch parents are in direct contact with the eggs when producing heat calls during incubation, not hovering in front of the nest. This misunderstanding affects all extrapolations from this study to findings in studies on prenatal communication.

(C) Misrepresentation of current knowledge

(9) Values from published papers are misreported, which reverses the conclusions:

Most critical examples:

(a) Preprint: "Zebra finch most sensitive hearing range of 1-to-4 kHz (Amin et al., 2007; Okanoya and Dooling, 1987; Yeh et al., 2023)" (L173).<br /> Actual values in the studies cited are:

1-to-7kHz, in Amin et al 2007 (threshold [=50dB with ABR] is the same at 7kHz and 1KHz).

1-to-6 kHz, in Okanoya and Dooling (the threshold [=30dB with behaviour] is actually lower at 6kHz than at 1KHz).

1-to-7kHz, in Yeh et al (threshold [=35-38dB with behaviour] is the same at 7kHz and 1KHz).

Note that zebra finch nestlings' begging calls peaking at 6kHz (Elie & Theunissen 2015, doi: 10.1007/s10071-015-0933-6), would fall 2kHz above the parents' best hearing range if it were only up to 4kHz.

(b) The preprint incorrectly states throughout (e.g., L139, L163, L248) that heat-calls are 7-10kHz, when the actual value is 6-10kHz in the paper cited (Katsis et al, 2018).

(c) Using the correct values from these studies, and heat-calls at 45 dB SLP (as measured by others (unpublished data), or as measured by the authors themselves, but which is not reported here (Anttonen et a,l 2025), the correct conclusion is that heat calls fall within the known zebra finch hearing range.

(10) Published evidence towards high-frequency hearing, including in early development, is systematically omitted:

(a) Other studies showing birds use high frequencies above the known avian hearing range are ignored. This includes oilbirds (7-23kHz; Brinklov et al 2017; by 1 of the preprint authors, doi: 10.1098/rsos.170255) and hummingbirds (10-20kHz; Duque et al 2020, doi: 10.1126/sciadv.abb9393), and in a lesser extreme, zebra finches' inspiratory song syllables at 5-7kHz (Goller & Dalley, 2001).

(b) The discussion of anatomical development (L228-241) completely omits the well-known fact that the avian basilar papilla develops from high to low frequencies (i.e., base to apex), which - as many have pointed out - is opposite to the low-to-high development of sensitivity (e.g., cited: Cohen & Fermin 1978; Caus Capdevila et al 2021).

(c) High frequency hearing in songbirds at hatching is several orders of magnitude better than in chickens and ducks at the same age, even though songbirds are altricial (e.g., at 4kHz, flycatcher: 47dB, chicken-duck: 90dB; at 5kHz, flycatcher: 65dB, chicken-duck: 115dB; Korneeva et al 2006, Saunders et al 1974). That is because Galliformes are low-frequency specialists, according to both anatomical and ecological evidence, with calls peaking at 0.8 to 1.2kHz rather than 2-6kHz in songbirds. It is incorrect to conclude that altricial embryos cannot perceive high frequencies because low-frequency specialist precocial birds do not (L250;261).

The references used to support the statement on a very high threshold for precocial birds above 6kHz are also wrong (L250). Katayama 1985 did not test embryos, nor frequency tones. Neither of these two references tested ducks.

(11) Incorrect statements do not reflect findings from the references cited

For example:

(a) "in altricial bird species hearing typically starts after hatching" (L12, in abstract), "with little to no functional hearing during embryonic stages (Woolley, 2017)." (L33).

There is no evidence, in any species, to support these statements. This is only a - commonly repeated - assumption, not actually based on any data. On the contrary, the extremely limited evidence to date shows the opposite, with zebra finch embryos showing ZENK activation in the auditory cortex in response to song playback (Rivera et al, 2018, not cited).

The book chapter cited (Woolley 2017) acknowledges this lack of evidence, and, in the context of song learning, provides as only references (prior to 2018), 2 studies showing that songbirds do not develop a normal song if the song tutor is removed before 10d post-hatch. That nestlings cannot memorise (to later reproduce) complex signals heard before d10 does not mean that they are deaf to any sound before day 10.

Studies showing hearing in young songbird nestlings (see point 6 above) also contradict these statements.

(b) "Zebra finch embryos supposedly are epigenetically guided to adapt to high temperatures by their parents high-frequency "heat calls" " (L36 and L135).

This is an extremely vague and meaningless description of these results, which cannot be assessed by readers, even though these results are presented as a major justification for the present study. Rather than giving an interpretation of what "supposedly" may occur, it would be appropriate to simply synthesize the empirical evidence provided in these papers. They showed that embryonic exposure to heat-calls, as opposed to control contact calls, alters a suite of physiological and behavioural traits in nestlings, including how growth and cellular physiology respond to high temperatures. This also leads to carry-over effects on song learning and reproductive fitness in adulthood.

(c) "The acoustic communication in precocial mallard ducks depends specifically on the low-frequency auditory sensitivity of the embryo (Gottlieb, 1975)" (L253)

The study cited (Gottlieb, 1975) demonstrates exactly the opposite of this statement: it shows that duckling embryos, not only perceive high frequency sounds (relative to the species frequency range), but also NEED this exposure to display normal audition and behaviour post-hatch. Specifically, it shows that duckling embryos deprived of exposure to their own high-frequency calls (at 2 kHz), failed to identify maternal calls post-hatch because of their abnormal insensitivity to higher frequencies, which was later confirmed by directly testing their auditory perception of tones (Dimitrieva & Gottlieb, 1994).

(12) Considering all of the mistakes and distortions highlighted above, it would be very premature to conclude, based on these results and statements, that altricial avian embryos are not sensitive to sound. This study provides no actual scientific ground to support this conclusion.

Author Response:

We thank all reviewers for their time and effort to carefully review our paper and for the constructive comments on our manuscript. Below we outline our planned revisions to the public reviews of the three reviewers.

In our revision, we will include more details regarding our ABR measurements (including temperature, animal metadata), analysis (including filter settings) and lay out a much more detailed motivation for our ABR signal design. Furthermore, we will provide a more detailed discussion on the caveats of the technique and the interpretation of ABR data in general and our data specifically. Furthermore, we will add more discussion on differences between ABR based audiograms and behavioural data. The authors have extensive experience with the ABR technique and are well aware of its limitations, but also its strengths for use in animals that cannot be trained on behavioural tasks such as the very young zebra finches in this study. These additions will strengthen our paper. We think our conclusions remain justified by our data.

Reviewer #1 and #2:

We thank both reviewers for their positive words and suggested improvements. The planned general improvements listed above will take care of all suggestions and comments in the public review.

Reviewer #3:

We thank the reviewer for the detailed critique of our manuscript and many suggestions for improvement. The planned general improvements listed above will take care of many of the suggestions and comments listed in the public review. Here we will highlight a few first responses that we will address in detail in our resubmission.

The reviewer’s major critiques can be condensed to the following four points.

(1) ABR cannot be done in such small animals.

This critique is unfounded. ABR measures the summed activity in the auditory pathway, and with smaller distance from brainstem to electrodes in small animals, the ABR signals are expected to have higher amplitude and consequently better SNR.  Thus, smaller animals should lead to higher amplitude ABR signals. We have successfully recorded ABR in animals smaller than 2 DPH zebra finches to support this claim (zebrafish (Jørgensen et al., 2012), 10 mm froglets (Goutte et al., 2017) and 5 mm salamanders (Capshaw et al., 2020). It is more surprising the technique still provides robust signals even in very large animals such as Minke whales (Houser et al., 2024).

(2) The ABR methods used does not follow protocol for other published work in birds. Particularly the 25 ms long duration tone bursts may have underestimated high frequency hearing.

There is no fixed protocol for ABR measurements, and several studies of bird ABR have used as long or even longer durations. Longer-duration signals were chosen deliberately and are necessary to have a sufficient number of cycles and avoid frequency splatter at our lowest frequencies used (see Lauridsen et al., 2021).

(3) Sensitivity data should be corrected from ABR to behavioural data.

We present the results of our measurements on hearing sensitivity using ABR, and ABR based thresholds are generally less sensitive than thresholds based on behavioural studies (presented in Fig 2c). Correcting for these measurements to behavioural thresholds is of course possible, but presenting only the corrected thresholds would be a misrepresentation of our sensitivity data. Even so it should be done only within species and age group and such data is currently not available. In our revision, we will include elaborate discussion on this topic.

(4) Results are inconsistent with papers in developing songbirds.

We agree that our results do not support and even question the claims in earlier work. These papers however do either 1) not measure hearing physiology or 2) do so in different species. To our best knowledge there is presently no data published on the auditory physiology development in songbird embryos. Our data are consistent with what is known about the physiology of auditory development in all birds studied so far. We will provide a detailed discussion on this topic in our revision.

References

Capshaw et al. (2020) J Exp Biol 223: jeb236489

Goutte et al. (2017) Sci Rep 7: 12121, doi 10.1038/s41598-017-12145-5

Houser et al. (2024) Science 386, 902-906. DOI:10.1126/science.ado7580).

Jørgensen et al. (2012) Adv Exp Med Biol 730: 117-119

Lauridsen et al (2021) J Exp Biol 224: jeb237313. https://doi.org/10.1242/jeb.237313

eLife Assessment

This study provides evidence for distinct neurotransmitter release modalities between two subclasses of dopaminergic neurons in the olfactory bulb. Specifically, it demonstrates dendritic neurotransmitter release in anaxonic neurons and axonal release in axon-bearing neurons. The presence of GABAergic self-inhibition in anaxonic neurons further underscores the functional divergence between these subtypes. Overall, the manuscript presents solid evidence and offers biologically important insights into the organization and function of dopaminergic circuits within the olfactory bulb.

Reviewer #1 (Public review):

Summary:

Dorrego-Rivas et al. investigated two different DA neurons and their neurotransmitter release properties in the main olfactory bulb. They found that the two different DA neurons in mostly glomerular layers have different morphologies as well as electrophysiological properties. The anaxonic DA neurons are able to self-inhibit but the axon-bearing ones are not. The findings are interesting and important to increase the understanding both of the synaptic transmissions in the main olfactory bulb and the DA neuron diversity. However, there are some major questions that the authors need to address to support their conclusions.

(1) It is known that there are two types of DA neurons in the glomerular layer with different diameters and capacitances (Kosaka and Kosaka, 2008; Pignatelli et al., 2005; Angela Pignatelli and Ottorino Belluzzi, 2017). In this manuscript, the authors need to articulate better which layer the imaging and ephys recordings took place, all glomerular layers or with an exception. Meanwhile, they have to report the electrophysiological properties of their recordings, including capacitances, input resistance, etc.

(2) It is understandable that recording the DA neurons in the glomerular layer is not easy. However, the authors still need to increase their n's and repeat the experiments at least three times to make their conclusion more solid. For example (but not limited to), Fig 3B, n=2 cells from 1 mouse. Fig.4G, the recording only has 3 cells.

(3) The statistics also use pseudoreplicates. It might be better to present the biology replicates, too.

(4) In Figure 4D, the authors report the values in the manuscript. It is recommended to make a bar graph to be more intuitive.

(5) In Figure 4F and G, although the data with three cells suggest no phenotype, the kinetics looked different. So, the authors might need to explore that aside from increasing the n.

(6) Similarly, for Figure 4I and J, L and M, it is better to present and analyze it like F and G, instead of showing only the after-antagonist effect.

Comments on revisions:

In the rebuttal, the authors argued that it had been extremely hard to obtain recordings stable enough for before-and-after effects on the same cell. Alternatively, they could perform the before-and-after comparison on different cells.

Reviewer #2 (Public review):

Summary:

This study provides novel insights into the neurotransmitter release mechanisms employed by two distinct subclasses of dopaminergic neurons in the olfactory bulb (OB). The findings suggest that anaxonic neurons primarily release neurotransmitters through their dendrites, whereas axon-bearing neurons predominantly release neurotransmitters via their axons. Furthermore, the study reveals that anaxonic neurons exhibit self-inhibitory behavior, indicating that closely related neuronal subclasses may possess specialized roles in sensory processing.

Strengths:

This study introduces a novel and significant concept, demonstrating that two closely related neuron subclasses can exhibit distinct patterns of neurotransmitter release. Therefore, this finding establishes a valuable framework for future investigations into the functional diversity of neuronal subclasses and their contributions to sensory processing. Furthermore, these findings offer fundamental insights into the neural circuitry of the olfactory bulb, enhancing our understanding of sensory information processing within this critical brain region.

Weaknesses:

The reliance on synaptophysin-based presynaptic structures raises minor concerns about whether these structures represent functional synapses.

Comments on revisions:

Most of the concerns have been addressed by the authors, and there are no further comments about this manuscript.

Author response:

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

Reviewer #1 (Public review):

This Reviewer was positive about the study, stating ‘The findings are interesting and important to increase the understanding both of the synaptic transmissions in the main olfactory bulb and the DA neuron diversity.’ They provided a number of helpful suggestions for improving the paper, which we have incorporated as follows:

(1) It is known that there are two types of DA neurons in the glomerular layer with different diameters and capacitances (Kosaka and Kosaka, 2008; Pignatelli et al., 2005; Angela Pignatelli and Ottorino Belluzzi, 2017). In this manuscript, the authors need to articulate better which layer the imaging and ephys recordings took place, all glomerular layers or with an exception. Meanwhile, they have to report the electrophysiological properties of their recordings, including capacitances, input resistance, etc.

We thank the Reviewer for this clarification. Indeed, the two dopaminergic cell types we study here correspond directly to the subtypes previously identified based on cell size. Our previous work showed that axon-bearing OB DA neurons have significantly larger somas than their anaxonic neighbours (Galliano et al. 2018), and we replicate this important result in the present study (Figure 3D). In terms of electrophysiological correlates of cell size, we now provide full details of passive membrane properties in the new Supplementary Figure 4, as requested. Axon-bearing DA neurons have significantly lower input resistance and show a non-significant trend towards higher cell capacitance. Both features are entirely consistent with the larger soma size in this subtype. We apologise for the oversight in not fully describing previous categorisations of OB DA neurons, and have now added this information and the appropriate citations to the Introduction (lines 56 to 59 of the revised manuscript). 

In terms of cell location, all cells in this study were located in the OB glomerular layer. We sampled the entire glomerular layer in all experiments, including the glomerular/EPL border where the majority of axon-bearing neurons are located (Galliano et al. 2018). This is now clarified in the Materials and Methods section (lines 535 to 537 and 614 to 616 of the revised manuscript).

(2) It is understandable that recording the DA neurons in the glomerular layer is not easy. However, the authors still need to increase their n's and repeat the experiments at least three times to make their conclusion more solid. For example (but not limited to), Fig 3B, n=2 cells from 1 mouse. Fig.4G, the recording only has 3 cells.

Despite the acknowledged difficulty of these experiments, we have now added substantial extra data to the study as requested. We have increased the number of cells and animals to further support the following findings:

Fig 3B: we now have n=5 cells from N=3 mice. We have created a new Supplementary Figure 1 to show all the examples.

Figure 4G: we now have n=6 cells from N=4 mice.

Figure 5G: we now have n=3 cells from N=3 mice.

The new data now provide stronger support for our original conclusions. In the case of auto-evoked inhibition after the application of D1 and D2 receptor antagonists, a nonsignificant trend in the data suggests that, while dopamine is clearly not necessary for the response, it may play a small part in its strength. We have now included this consideration in the Results section (lines 256 to 264 of the revised manuscript).

(3) The statistics also use pseudoreplicates. It might be better to present the biology replicates, too.

Indeed, in a study focused on the structural and functional properties of individual neurons, we performed all comparisons with cell as the unit of analysis. This did often (though not always) involve obtaining multiple data points from individual mice, but in these low-throughput experiments n was never hugely bigger than N. The potential impact of pseudoreplicates and their associated within-animal correlations was therefore low. We checked this in response to the Reviewer’s comment by running parallel nested analyses for all comparisons that returned significant differences in the original submission. These are the cases in which we would be most concerned about potential false positive results arising from intra-animal correlations, which nested tests specifically take into account (Aarts et al., 2013). In every instance we found that the nested tests also reported significant differences between anaxonic and axonbearing cell types, thus fully validating our original statistical approach. We now report this in the relevant section of the Materials and Methods (lines 686 to 691 of the revised manuscript).

(4) In Figure 4D, the authors report the values in the manuscript. It is recommended to make a bar graph to be more intuitive.

This plot does already exist in the original manuscript. We originally describe these data to support the observation that an auto-evoked inhibition effect exists in anaxonic neurons (corresponding to now lines 240 to 245 of the revised manuscript). We then show them visually in their entirety when we compare them to the lack of response in axon-bearing neurons, depicted in Figure 5C. We still believe that this order of presentation is most appropriate for the flow of information in the paper, so have maintained it in our revised submission.

(5) In Figure 4F and G, although the data with three cells suggest no phenotype, the kinetics looked different. So, the authors might need to explore that aside from increasing the n.

We thank the Reviewer for this suggestion. To quantify potential changes in the autoevoked inhibition response kinetics, we fitted single exponential functions and compared changes in the rate constant (k; Methods, lines 650 to 652 of the revised manuscript). Overall, we observed no consistent or significant change in rate constant values after adding DA receptor antagonists. This finding is now reported in the Results section (lines 260 to 263 of the revised manuscript) and shown in a new Supplementary Figure 3.

(6) Similarly, for Figure 4I and J, L and M, it is better to present and analyze it like F and G, instead of showing only the after-antagonist effect.

We agree that the ideal scenario would have been to perform the experiments in Figure 4J and 4M the same way as those in Figure 4G, with a before vs after comparison. Unfortunately, however, this was not practically possible. 

When attempting to apply carbenoxelone to already-patched cells, we found that this drug highly disrupted the overall health and stability of our recordings immediately after its application. This is consistent with previous reports of similar issues with this compound (e.g. Connors 2012, Epilepsy Currents; Tovar et al., 2009, Journal of Neurophysiology). After many such attempts, the total yield of this experiment was one single cell from one animal. Even so, as shown in the traces below, we were able to show that the auto-evoked inhibition response was not eliminated in this specific case:

Author response image 1.

Traces of an AEI response recorded before (magenta) and after (green) the application of carbenoxolone (n=1 cell from N=1 mouse).

In light of these issues, we instead followed published protocols in applying the carbenoxolone directly in the bath without prior recording for 20 minutes (following Samailova et al., 2003, Journal of Neurochemistry) and ran the protocol after that time. Given that our main question was to ask whether gap junctions were strictly necessary for the presence of any auto-evoked inhibition response, our positive findings in these experiments still allowed us to draw clear conclusions.

In contrast, the issue with the NKCC1 antagonist bumetanide was time. As acknowledged by this Reviewer, obtaining and maintaining high-quality patch recordings from OB DA neurons is technically challenging. Bumetanide is a slow-acting drug when used to modify neuronal chloride concentrations, because in addition to the time it takes to reach the neurons and effectively block NKCC1, the intracellular levels of chloride subsequently change slowly. Studies using this drug in slice physiology experiments typically use an incubation time of at least 20 minutes (e.g. Huberfeld et al., 2007, Journal of Neuroscience), which was incompatible with productive data collection in OB DA neurons. Again, after many unsuccessful efforts, we were forced instead to include bumetanide in the bath without prior recording for 20-30 minutes. As with the carbenoxolone experiment, our goal here was to establish whether autoevoked inhibition was in any way retained in the presence of this drug, so our positive result again allowed us to draw clear conclusions.

Reviewer #1 (Recommendations for the authors):

(1) I suggest the authors reconsider the terminology. For example, they use "strikingly" in their title. The manuscript reported two different transmitter release strategies but not the mechanisms, and the word "strikingly" is not professional, either.

We appreciate the Reviewer’s attention to clarity and tone in the manuscript title, and have nevertheless decided to retain the original wording. The almost all-or-nothing differences between closely related cell types shown in structural and functional properties here (Figures 3F & 5C) are pronounced, extremely clear and easily spotted – all properties appropriate for the word ‘striking.’ In addition, we note that the use of this term is not at all unprofessional, with a PubMed search for ‘strikingly’ in the title of publications returning over 200 hits.

(2) Similarly, almost all confocal scopes are 3D because images can be taken at stacks. So "3D confocal" is misleading.

We understand that this is misleading. We have now replaced the sentence ‘Example snapshot of a 3D confocal stack of…’ by ‘Example confocal images of…’ in all the figure legends that apply.

(3) It is recommended to present the data in bar graphs with data dots instead of showing the numbers in the manuscript directly.

We agree entirely, and now present data plots for all comparisons reported in the study (Supplementary Figures 2, 4 and 5).

Reviewer #2 (Recommendations for the authors):

(1) Several experiments report notably small sample sizes, such as in Figures 3B and 5G, where data from only 2 cells derived from 1-2 mice are presented. Figures 4E-G also report the experimental result only from 3 cells derived from 3 mice. To enhance the statistical robustness and reliability of the findings, these experiments should be replicated with larger sample sizes.

As per our response to Reviewer 1’s comment #2 above, and to directly address the concern that some evidence was ‘incomplete’, we have now added significant extra data and analysis to this revised submission (Figures 4 and 5; and Supplementary Figure 1). We believe that this has further enhanced the robustness and reliability of our findings, as requested.

(2) The authors utilize vGAT-Cre for Figures 1-3 and DAT-tdTomato for Figures 4-5, raising concerns about consistency in targeting the same population of dopaminergic neurons. It remains unclear whether all OB DA neurons express vGAT and release GABA. Clarification and additional evidence are needed to confirm whether the same neuronal population was studied across these experiments.

Although we indeed used different mouse lines to investigate structural and functional aspects of transmitter release, we can be very confident that both approaches allowed us to study the same two distinct DA cell types being compared in this paper. Existing data to support this position are already clear and strong, so in this revision we have focused on the Reviewer’s suggestion to clarify the approaches we chose.

First, it is well characterised that in mouse and many other species all OB DA neurons are also GABAergic. This has been demonstrated comprehensively at the level of neurochemical identity and in terms of dopamine/GABA co-release, and is true across both small-soma/anaxonic and large-soma/axon-bearing subclasses (Kosaka & Kosaka 2008; 2016; Maher & Westbrook 2008; Borisovska et al., 2013; Vaaga et al., 2016; Liu et al. 2013). To specifically confirm vGAT expression, we have also now provided additional single-cell RNAseq data and immunohistochemical label in a revised Figure 1 (see also Panzanelli et al., 2007, now referenced in the paper, who confirmed endogenous vGAT colocalisation in TH-positive OB neurons). Most importantly, by using vGAT-cre mice here we were able to obtain sufficient numbers of both anaxonic and axon-bearing DA neurons among the vGAT-cre-expressing OB population. We could unambiguously identify these cells as dopaminergic because of their expression of TH protein which, due to the absence of noradrenergic neurons in the OB, is a specific and comprehensive marker for dopaminergic cells in this brain region (Hokfelt et al., 1975; Rosser et al., 1986; Kosaka & Kosaka 2016). Crucially, both axon-bearing and anaxonic OB DA subtypes strongly express TH (Galliano et al., 2018, 2021). We have now added additional text to the relevant Results section (lines 99 to 108 of the revised manuscript) to clarify these reasons for studying vGAT-cre mice here.

We were also able to clearly identify and sample both subtypes of OB DA neuron using DAT-tdT mice. Our previous published work has thoroughly characterised this exact mouse line at the exact ages studied in the present paper (Galliano et al., 2018; Byrne et al., 2022). We know that DAT-tdT mice provide rather specific label for TH-expressing OB DA neurons (75% co-localisation; Byrne et al., 2022), but most importantly we know which non-DA neurons are labelled in this mouse line and how to avoid them. All nonTH-expressing but tdT-positive cells in juvenile DAT-tdT mice are small, dimly fluorescent and weakly spiking neurons of the calretinin-expressing glomerular subtype (Byrne et al., 2022). These cells are easily detected during physiological recordings, and were excluded from our study here. This information is now provided in the relevant Methods section (lines 616 to 619 of the revised manuscript, also referenced in lines 236 to 240 of the results section), and we apologise for its previous omission. Finally, we have shown both structurally and functionally that both axon-bearing and anaxonic OB DA subtypes are labelled in DAT-tdT mice (Galliano et al., 2018, Tufo et al., 2025; present study). Overall, these additional clarifications firmly establish that the same neuronal populations were indeed studied across our experiments.

(3) The low TH+ signal in Figure 1D raises questions regarding the successful targeting of OB DA neurons. Further validation, such as additional staining, is required to ensure that the targeted neurons are accurately identified.

As noted in our response to the previous comment, TH is a specific marker for dopaminergic neurons in the mouse OB, and is widely used for this purpose. Labelling for TH in our tissue is extremely reliable, and in fact gives such strong signal that we were forced to reduce the primary antibody concentration to 1:50,000 to prevent bleedthrough into other acquisition channels. Even at this concentration it was extremely straightforward to unambiguously identify TH-positive cells based on somatic immunofluorescence. We recognise, however, that the original example image in Figure 1D was not sufficiently clear, and have now provided a new example which illustrates the TH-based identification of these cells much more effectively. 

(4) Estimating the total number of dopaminergic neurons in the olfactory bulb, along with the relative proportions of anaxonic and axon-bearing neuron subtypes, would provide valuable context for the study. Presenting such data is crucial to underscore the biological significance of the findings.

This information has already been well characterised in previous studies. Total dopaminergic cell number in the OB is ~90,000 (Maclean & Shipley, 1988; Panzanelli et al., 2007; Parrish-Aungst et al., 2007). In terms of proportions, anaxonic neurons make up the vast majority of these cells, with axon-bearing neurons representing only ~2.5% of all OB dopaminergic neurons at P28 (Galliano et al., 2018). Of course, the relatively low number of the axon-bearing subtype does not preclude its having a potentially large influence on glomerular networks and sensory processing, as demonstrated by multiple studies showing the functional effects of inter-glomerular inhibition (Kosaka & Kosaka, 2008; Liu et al., 2013; Whitesell et al., 2013; Banerjee et al., 2015). This information has now been added to the Introduction (line 47 and lines 59 to 62 of the revised manuscript).

(5) The authors report that in-utero injection was performed based on the premise that the two subclasses of dopaminergic neurons in the olfactory bulb are generated during embryonic development. However, it remains unclear whether in-utero injection is essential for distinguishing between these two subclasses. While the manuscript references a relevant study, the explanation provided is insufficient. A more detailed justification for employing in-utero injection would enhance the manuscript's clarity and methodological rigor.

We apologise for the lack of clarity in explaining the approach. In utero injection is not absolutely essential for distinguishing between the two subclasses, but it does have two major advantages. 1) Because infection happens before cells migrate to their final positions, it produces sparse labelling which permits later unambiguous identification of individual cells’ processes; and 2) Because both subclasses are generated embryonically (compared to the postnatal production of only anaxonic DA neurons), it allows effective targeting of both cell types. We have now expanded the relevant section of the Results to explain the rationale for our approach in more detail (lines 109 to 116 of the revised manuscript).

(6) In Figures 1A and 4A, it appears that data from previously published studies were utilized to illustrate the differential mRNA expression in dopaminergic neurons of the olfactory bulb. However, the Methods section and the manuscript lack a detailed description of how these dopaminergic neurons were classified or analyzed. Given that these figures contribute to the primary dataset, providing additional explanation and context is essential to ensure clarity of the findings.

We apologise for the lack of clarity. We have now extended the part of the methods referring to the RNAseq data analysis (lines 666 to 678 of the revised manuscript). 

(7) In Figure 2C, anaxonic dopamine neurons display considerable variability in the number of neurotransmitter release sites, with some neurons exhibiting sparse sites while others exhibit numerous sites. The authors should address the potential biological or methodological reasons for this variability and discuss its significance.

We thank the Reviewer for highlighting this feature of our data. We have now outlined potential methodological reasons for the variability, whilst also acknowledging that it is consistent with previous reports of presynaptic site distributions in these cells (Kiyokage et al., 2017; Results, lines 169 to 172 of the revised manuscript). We have also added a brief discussion of the potential biological significance (Discussion, lines 446 to 450).

(8) In the images used to differentiate anaxonic and axon-bearing neurons, the soma, axons, and dendrites are intermixed, making it difficult to distinguish structures specific to each subclass. Employing subclass-specific labeling or sparse labeling techniques could enhance clarity and accuracy in identifying these structures.

Distinguishing these structures is indeed difficult, and was the main reason we used viral label to produce sparse labelling (see response to comment #5 above). In all cases we were extremely careful, including cells only when we could be absolutely certain of their anaxonic or axon-bearing identity, and could also be certain of the continuity of all processes. Crucially, while the 2D representations we show in our figures may suggest a degree of intermixing, we performed all analyses on 3D image stacks, significantly improving our ability to accurately assign structures to individual cells. We have now added extra descriptions of this approach in the relevant Methods section (lines 546 to 548 of the revised manuscript).

(9) In Figure 3, the soma area and synaptophysin puncta density are compared between axon-bearing and anaxonic neurons. However, the figure only presents representative images of axon-bearing neurons. To ensure a fair and accurate comparison, representative images of both neuron subtypes should be included.

The original figures did include example images of puncta density (or lack of puncta) in both cell types (Figure 2B and Figure 3E). For soma area, we have now included representative images of axon-bearing and anaxonic neurons with an indication of soma area measurement in a new Supplementary Figure 2A.

(10) In Figure 4B, the authors state that gephyrin and synaptophysin puncta are in 'very close proximity.' However, it is unclear whether this proximity is sufficient to suggest the possibility of self-inhibition. Quantifying the distance between gephyrin and synaptophysin puncta would provide critical evidence to support this claim. Additionally, analyzing the distribution and proportion of gephyrinsynaptophysin pairs in close proximity would offer further clarity and strengthen the interpretation of these findings.

We thank the Reviewer for raising this issue. We entirely agree that the example image previously shown did not constitute sufficient evidence to claim either close proximity of gephyrin and synaptophysin puncta, nor the possibility of self-inhibition. We are not in a position to perform a full quantitative analysis of these spatial distributions, nor do we think this is necessary given previous direct evidence for auto-evoked inhibition in OB dopaminergic cells (Smith and Jahr, 2002; Murphy et al., 2005; Maher and Westbrook, 2008; Borisovska et al., 2013) and our own demonstration of this phenomenon in anaxonic neurons (Figure 4). We have therefore removed the image and the reference to it in the text. 

(11) In Figures 4J and 4M, the effects of the drugs are presented without a direct comparison to the control group (baseline control?). Including these baseline control data is essential to provide a clear context for interpreting the drug effects and to validate the conclusions drawn from these experiments.

We appreciate the Reviewer’s attention to this important point. As this concern was also raised by Reviewer 1 (their point #6), we have provided a detailed response fully addressing it in our replies to Reviewer 1 above. 

(12) In Lines 342-344, the authors claim that VMAT2 staining is notoriously difficult. However, several studies (e.g., Weihe et al., 2006; Cliburn et al., 2017) have successfully utilized VMAT2 staining. Moreover, Zhang et al., 2015 - a reference cited by the authors - demonstrates that a specific VMAT2 antibody effectively detects VMAT2. Providing evidence of VMAT2 expression in OB DA neurons would substantiate the claim that these neurons are GABA-co-releasing DA neurons and strengthen the study's conclusions.

As noted in response to this Reviewer’s comment #2 above, there is clear published evidence that OB DA neurons are GABA- and dopamine-releasing cells. These cells are also known to express VMAT2 (Cave et al., 2010; Borisovska et al., 2013; Vergaña-Vera et al., 2015). We do not therefore believe that additional evidence of VMAT2 expression is necessary to strengthen our study’s conclusions. We did make every effort to label VMAT2-positive release sites in our neurons, but unfortunately all commercially available antibodies were ineffective. The successful staining highlighted by the Reviewer was either performed in the context of virally driven overexpression (Zhang et al., 2015) or was obtained using custom-produced antibodies (Weihe et al., 2006; Cliburn et al., 2017). We have now modified the Discussion text to provide more clarification of these points (lines 393 to 395 of the revised manuscript).

eLife Assessment

This important theoretical study shows that active hexatic topological defects in epithelia enable collective cell flows. Within the general limitations of coarse-grained hydrodynamic models in fully capturing cell-scale behavior, the study provides compelling evidence supporting its conclusions. These findings will be of interest to both biophysicists studying collective cell behaviors and biologists investigating epithelial flows during development.

Reviewer #1 (Public review):

Summary:

This paper investigates the physical mechanisms underlying cell intercalation, which then enables collective cell flows in confluent epithelia. The authors show that T1 transitions (the topological transitions responsible for cell intercalation) correspond to the unbinding of groups of hexatic topological defects. Defect unbinding, and hence cell intercalation and collective cell flows, are possible when active stresses in the tissue are extensile. This result helps to rationalize the observation that many epithelial cell layers have been found to exhibit extensile active nematic behavior.

Strengths:

The authors obtain their results based on a combination of active hexanematic hydrodynamics and a multiphase field (MPF) model for epithelial layers, whose connection is a strength of the paper. With the hydrodynamic approach, the authors find the active flow fields produced around hexatic topological defects, which can drive defect unbinding. Using the MPF simulations, the authors show that T1 transitions tend to localize close to hexatic topological defects.

Reviewer #2 (Public review):

Summary:

This paper studies the role of hexatic defects in the collective migration of epithelia. The authors emphasize that epithelial migration is driven by cell intercalation events and not just isolated T1 events, and analyze this through the lens of hexatic topological defects. Finally, the authors study the effect of active and passive forces on the dynamics of hexatic defects using analytical results, and numerical results in both continuum and phase-field models. The results are very interesting, and highlight new ways of studying epithelial cell migration through the analysis of the binding and unbinding of hexatic defects.

Strengths:

(1) The authors convincingly argue that intercalation events are responsible for collective cell migration, and that these events are accompanied by the formation and unbinding of hexatic topological defects. (2) The authors clearly explain the dynamics of hexatic defects during T1 transitions, and demonstrate the importance of active and passive forces during cell migration. (3) The paper thorougly studies the T1 transition throught the viewpoint of hexatic defects. A continuum model approach to study T1 transitions in cell layers is novel and can lead to valuable new insights.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This paper investigates the physical mechanisms underlying cell intercalation, which then enables collective cell flows in confluent epithelia. The authors show that T1 transitions (the topological transitions responsible for cell intercalation) correspond to the unbinding of groups of hexatic topological defects. Defect unbinding, and hence cell intercalation and collective cell flows, are possible when active stresses in the tissue are extensile. This result helps to rationalize the observation that many epithelial cell layers have been found to exhibit extensile active nematic behavior.

Strengths

The authors obtain their results based on a combination of active hexanematic hydrodynamics and a multiphase field (MPF) model for epithelial layers, whose connection is a strength of the paper. With the hydrodynamic approach, the authors find the active flow fields produced around hexatic topological defects, which can drive defect unbinding. Using the MPF simulations, the authors show that T1 transitions tend to localize close to hexatic topological defects.

We are grateful to Reviewer #1, for appreciating and highlighting the strengths of work.

Weaknesses

Citations are sometimes not comprehensive. Cases of contractile behavior found in collective cell flows, which would seemingly contradict some of the authors’ conclusions, are not discussed.

I encourage the authors to address the comments and questions below.

We are thankful to Reviewer #1, for their questions and comments. We have addressed them point by point below, and have amended the manuscript accordingly.

(1) In Equation 1, what do the authors mean by the cluster’s size ℓ? How is this quantity defined? The calculations in the Methods suggest that ℓ indicates the distance between the p-atic defects and the center of the T1 cell cluster, but this is not clearly defined.

We are thank Reviewer #1 for their question. We define the cluster size as the initial distance between the center of the quadrupole and any defect (see Methods). In a primary cell cluster, where cells themselves are the defects, the cluster’s size is the distance between the center of the central junction and the center of any cell in the cluster. Hence, this is half the diameter of an cell which, for example in a typical, confluent MDCK epithelial monolayer, would be about 10µm. We have added this clarification in the definition of the cluster size, above Eq. (1).

(2) The multiphase field model was developed and reviewed already, before the Loewe et al. 2020 paper that the authors cite. Earlier papers include Camley et al. PNAS 2014, Palmieri et al. Sci. Rep. 2015, Mueller et al. PRL 2019, and Peyret et al. Biophys. J. 2019, as reviewed in Alert and Trepat. Annu. Rev. Condens. Matter Phys. 2020.

We thank the referee for their suggestion to incorporate further MPF literature. We have done so in the amended manuscript.

(3) At what time lag is the mean-squared displacement in Figure 3f calculated? How does the choice of a lag time affect these data and the resulting conclusions?

The scatter plot in Fig. 3f was constructed by dividing the system into square subregions of size ∆ℓ = 35 l.u., each containing approximately 4 cells. For each subregion, we analyzed a time window of ∆t = 25 × 10³ iterations, measuring both the normalized mean square displacement of cells (relative to the subregion area ∆ℓ²) and the average defect density. The normalized displacement is calculated as m.s.d. , where t∗ denotes the start time of the observation window. We chose the time window ∆t used to compute the mean square displacement to match the characteristic duration of T1 events and defect lifetimes in our simulations. Observation times much longer (∆t > 35 × 10³) than the typical T1 event duration would cause the two sets of data points to merge into a single group, suggesting no correlation between cell motility and defect density beyond defect life-time.

(4) The authors argue that their results provide an explanation for the extensile behavior of cell layers. However, there are also examples of contractile behavior, such as in Duclos et al., Nat. Phys., 2017 and in P´erez-Gonz´alez et al., Nat. Phys., 2019. In both cases, collective cell flows were observed, which in principle require cell intercalations. How would these observations be rationalized with the theory proposed in this paper? Can these experiments and the theory be reconciled?

The contractile or extensile nature of stress in epithelia depends crucially on the specific tissue type and its biological context. Different cell populations, depending on their position along the epithelial/mesenchymal spectrum, can exhibit either contractile or extensile behaviors. Our theory applies to tissues where hexatic order dominates at the cellular scale, particularly in confluent systems where neighbor exchanges occur primarily through T1 transitions. In contrast, the systems studied by Duclos et al., Nat. Phys. (2018) and Perez-Gonzalez et al. (Nat. Phys., 2019) exhibit nematic order at the cellular level, meaning their dynamics are governed by fundamentally different mechanisms. Since our framework is derived for hexatic-dominated tissues, it does not directly apply to those cases, though a hybrid hexanematic descriptions previously developed by some of the authors in Armengol-Collado et al. eLife 13:e86400 (2024) could help reconcile these observations. In general, a key distinction must be made between the contractility of individual cells and the extensile/contractile nature of the collective force network. To illustrate this, consider a cell exerting a 6- fold symmetric force distribution: each vertex force arises from an imbalance in junctional tensions with neighboring cells, which are themselves contractile due to actomyosin activity. However, the resulting vertex forces can be either contractile or extensile depending on network geometry and tension distribution. This is captured in our coarse-grained description [see Armengol-Collado et al. eLife 13:e86400 (2024)], where the active stress emerges from higher-order moments of cellular forces. Specifically, the deviatoric part of the hexatic active stress tensor , where is the cell radius, the number cell density and the intensity of cellular tension. The negative sign of the coefficient of the active stress shows that the active stress is extensile—consistently with observations in various epithelial systems (e.g., Saw et al., Nature 2017; Blanch-Mercader et al., Phys. Rev. Lett. 2018). Finally, we note that the connection between cellular-scale forces and large-scale extensility has been rationalized in other contexts, such as active nematics (Balasubramaniam et al., Nat. Mater. 2021).

Reviewer #2 (Public Review):

This paper studies the role of hexatic defects in the collective migration of epithelia. The authors emphasize that epithelial migration is driven by cell intercalation events and not just isolated T1 events, and analyze this through the lens of hexatic topological defects. Finally, the authors study the effect of active and passive forces on the dynamics of hexatic defects using analytical results, and numerical results in both continuum and phase-field models.

The results are very interesting and highlight new ways of studying epithelial cell migration through the analysis of the binding and unbinding of hexatic defects.

We are grateful to Reviewer #2, for their interest and for emphasizing the novelty of our work.

Strengths

(1) The authors convincingly argue that intercalation events are responsible for collective cell migration, and that these events are accompanied by the formation and unbinding of hexatic topological defects.

(2) The authors clearly explain the dynamics of hexatic defects during T1 transitions, and demonstrate the importance of active and passive forces during cell migration.

(3) The paper thoroughly studies the T1 transition through the viewpoint of hexatic defects. A continuum model approach to study T1 transitions in cell layers is novel and can lead to valuable new insights.

We thank the Reviewer for their kind and supporting words, and for highlighting the clarity, persuasiveness, and thoroughness.

Weaknesses

(1) The authors could expand on the dynamics of existing hexatic defects during epithelial cell migration, in addition to how they are created during T1 transitions.

We thank the referee for their comment. The detailed analysis of dislocation-pair unbinding modes and their statistical impact on the transition to collective migration is comprehensively addressed in our subsequent work Puggioni et al., arXiv:2502.09554. In the present study, we focus specifically on the fundamental mechanism enabling dislocation unbinding: active extensile stresses generate flows that drive dislocation pairs apart, while passive elastic stresses tend to pull them together (Krommydas et al., Phys. Rev. Lett. 2023; Armengol- Collado et al., arXiv:2502.13104). When active forces dominate over passive restoring forces, the dislocations unbind. This represents a crucial distinction from classical Berezinskii–Kosterlitz–Thouless or Kosterlitz–Thouless–Halperin–Nelson–Youn transitions, where thermal fluctuations drive defect unbinding. In our system, the process is fundamentally activity-driven. Nevertheless, the resulting state - characterized by unbound defects and collective migration - bears strong analogy to the melting transition in equilibrium systems. We emphasize that the dynamics of passive defects has been previously examined in Krommydas et al., Phys. Rev. Lett. 2023. A discussion of these aspects can be found in the Appendix “Numerical simulations of defect annihilation and unbinding”.

(2) The different terms in the MPF model used to study cell layer dynamics are not fully justified. In particular, it is not clear why the model includes self-propulsion and rotational diffusion in addition to nematic and hexatic stresses, and how these quantities are related to each other.

We thank the referee for their comment. The MPF model’s terms (e.g., self-propulsion, rotational diffusion), reflect the stochastic, deformable nature of cells as active droplets migrating with near-constant speed. We emphasize that self-propulsion is the only non-equilibrium mechanism in our model — no additional active stresses (nematic or hexatic) are imposed. We have clarified this point in the revised manuscript and expanded our discussion of the MPF model.

(3) The authors could provide some physical intuition on what an active extensile or contractile term in the hexatic order parameter means, and how this is related to extensility and contractility in active nematics and/or for cell layers.

We thank the referee for their comment. As we explain in the reply to comment [4] of Reviewer #1, the contractile or extensile nature of stress in epithelia depends crucially on the specific tissue type and its biological context. Different cell populations, depending on their position along the epithelial/mesenchymal spectrum, can exhibit either contractile or extensile behaviors. Our theory applies to tissues where hexatic order dominates at the cellular scale, particularly in confluent systems where neighbor exchanges occur primarily through T1 transitions. In contrast, the systems studied by Duclos et al., Nat. Phys. (2018) and Perez-Gonzalez et al. (Nat. Phys., 2019) exhibit nematic order at the cellular level, meaning their dynamics are governed by fundamentally different mechanisms. Since our framework is derived for hexatic-dominated tissues, it does not directly apply to those cases, though a hybrid hexanematic descriptions previously developed by some of the authors in Armengol-Collado et al. eLife 13:e86400 (2024) could help reconcile these observations. In general, a key distinction must be made between the contractility of individual cells and the extensile/contractile nature of the collective force network. To illustrate this, consider a cell exerting a 6-fold symmetric force distribution: each vertex force arises from an imbalance in junctional tensions with neighboring cells, which are themselves contractile due to actomyosin activity. However, the resulting vertex forces can be either contractile or extensile depending on network geometry and tension distribution. This is captured in our coarse-grained description [see Armengol-Collado et al. eLife 13:e86400 (2024)], where the active stress emerges from higher-order moments of cellular forces. Specifically, the deviatoric part of the hexatic active stress tensor , where is the cell radius, the number cell density and the intensity of cellular tension. The negative sign of the coefficient of the active stress shows that the active stress is extensile—consistently with observations in various epithelial systems (e.g., Saw et al., Nature 2017; Blanch-Mercader et al., Phys. Rev. Lett. 2018). Finally, we note that the connection between cellular-scale forces and large-scale extensility has been rationalized in other contexts, such as active nematics (Balasubramaniam et al., Nat. Mater. 2021).

Recommendations for the Authors: Reviewer #2 (Recommendations for the Authors):

(1) The authors point out that hexatic topological defects are produced in quadrupoles (L109). Does this also mean that these defects can be annihilated only in quadrupoles as well? In the same vein, are hexatic defects always bound in pairs, as suggested by the schematics, or is it possible to observe an isolated hexatic defect?

We thank the referee for their question. Hexatic disclinations (the defect monopoles discussed in this work), much like electrons and positrons, can annihilate in any number of neutral charge configuration (dipole, quadrupole, octupole, etc.). Unbinding a pair of hexatic disinclination, however, costs much more energy than unbinding a quadrupole to dipoles. Hence isolated defects appear in abundance only in late, fully disordered phase, where the system has completely “melted”. For more details on how defect unbinding modes affect tissue dynamics, please see our subsequent work Puggioni et al., arXiv:2502.09554.

(2) Could you clarify if the flows described in Figures 2(a)-(b), panel (i) are driven by a passive backflow term without activity? Could you compare the magnitudes of these flows compared to the typical active terms?

We thank the referee for their question. In panel 2(b) there is only passive backflow. In 2(a) instead, both terms are included, and are in a regime of parameters where the active flow overcomes the active flow (and hence the active force overcomes the passive force as delineated in the discussions section). In turn, the magnitude of the passive flows, is studied in detail in our previous work Krommydas et al., (Phys. Rev. Lett. 2023).

(3) Could you clarify how the continuum hexatic model and MPF model are related to each other? What are the similarities and differences in the dynamics of these models?

We thank the referee for this insightful question. A key point of our work is precisely that the continuum hexatic model and the MPF (Multi-Phase Field) model are distinct in nature.

The MPF model is an established agent-based framework used to simulate tissue dynamics at the cellular level. It captures individual cell behaviors and interactions through phase-field variables. In our work, we use the MPF model as a benchmark to extract statistical features of tissue dynamics, such as defect motion and orientational correlations. In contrast, our continuum hexatic model is a coarse-grained hydrodynamic theory that describes the dynamics of orientational order in active tissues. It is built on symmetry principles and conservation laws, and it does not rely on microscopic cell-level details. Instead, it captures the collective behavior of the system through a hexatic order parameter and its coupling to flow and activity.

Despite their conceptual differences, the MPF model and our hydrodynamic theory exhibit similar statistical features. This agreement—also observed in the independent study by Jain et al. (Phys. Rev. Res. 2024)—provides strong support for the validity and generality of our continuum description.

(4) When multiple references by the same author and year are cited using alphabets, the second alphabet is not in bold e.g. Giomi et al., 2022b, a in Line 75, and others.

We are grateful to the referee carefully going through the manuscript and pointing out these typos. We have corrected them in the amended manuscript.

Reviewer #3 (Public Review):

In this manuscript, the authors discuss epithelial tissue fluidity from a theoretical perspective. They focus on the description of topological transitions whereby cells change neighbors (T1 transitions). They explain how such transitions can be described by following the fate of hexatic defects. They first focus on a single T1 transition and the surrounding cells using a hydrodynamic model of active hexatics. They show that successful T1 intercalations, which promote tissue fluidity, require a sufficiently large extensile hexatic activity in the neighborhood of the cells attempting a T1 transition. If such activity is contractile or not sufficiently extensile, the T1 is reversed, hexatic defects annihilate, and the epithelial network configuration is unchanged. They then describe a large epithelium, using a phase field model to describe cells. They show a correlation between T1 events and hexatic defects unbinding, and identify two populations of T1 cells: one performing T1 cycles (failed T1), and not contributing to tissue migration, and one performing T1 intercalation (successful T1) and leading to the collective cell migration.

Strengths

The manuscript is scientifically sound, and the variety of numerical and analytical tools they use is impressive. The approach and results are very interesting and highlight the relevance of hexatic order parameters and their defects in describing tissue dynamics.

We thank the Reviewer for recognizing the scientific soundness of the manuscript, the breadth of numerical and analytical tools employed, as well as their interest in our work.

Weaknesses

(1) Goal and message of the paper. (a) In my opinion, the article is mainly theoretical and should be presented as such. For instance, their conclusions and the consequences of their analysis in terms of biology are not extremely convincing, although they would be sufficient for a theory paper oriented to physicists or biophysicists. The choice of journal and potential readership should be considered, and I am wondering whether the paper structure should be re-organized, in order to have side-by-side the methods and the results, for instance (see also below).

We thank the referee for their criticism. In response, we have made an effort to reword certain parts of the manuscript. As with any theoretical study, the biological implications of our work can only be fully assessed through experimental validation — a prospect we look forward to. Nevertheless, we have submitted our work to the subsection of Physics of Life, which we believe is perfectly suited to our content.

(b) Currently, the two main results sections are somewhat disconnected, because they use different numerical models, and because the second section only marginally uses the results from the first section to identify/distinguish T1.

We thank the referee, for their comment. In the second section we are using statistics from the MPF model, to support the analytical and numerical findings of our hydrodynamic theory of cell intercalation. In the time between our submission, further qualitative evidence have been brought to light in the work of Jain et al. (Phys. Rev. Res. 2024).

(2) Quite surprisingly, the authors use a cell-based model to describe the macroscopic tissuescale behavior, and a hydrodynamic model to describe the cell-based events. In particular, their hydrodynamic description (the active hexatic model) is supposed to be a coarse-grained description, valid to capture the mesoscopic physics, and yet, they use it to describe cellscale events (T1 transitions). For instance, what is the meaning of the velocity field they are discussing in Figure 2? This makes me question the validity of the results of their first part.

We thank the referee for their comment. There are many excellent discrete models of epithelial tissues in the literature (e.g., Bi et al., Phys. Rev. X 2016; Pasupalak et al., Soft Matter 2020; Graner et al., Phys. Rev. Lett. 1992), each capturing essential biological features such as cell division, apoptosis and sorting. While these models have provided invaluable insights, our work takes a different approach by developing a continuum theory aimed at describing epithelial dynamics at two levels: (1) mesoscopic intercalation events and (2) macroscopic collective migration. Crucially, our goal is not to replicate a specific discrete model — which would risk constructing a “model of a model” — but rather to derive a hydrodynamic description of tissue dynamics grounded in symmetry principles and conservation laws. Along this logic, the velocity field in our theory should be interpreted as an Eulerian (continuum) velocity, representing the coarse-grained flow of the tissue rather than the Lagrangian motion of individual cells. This distinction is central to our framework, which operates at scales where cellular details are averaged out, yet retains the essential physics of hexatic order and active stresses. We validate our predictions against the Multiphase Field (MPF) model. [We thank Reviewer 1 for their suggestion to incorporate further MPF literature.] Furthermore, Jain et al. (Phys. Rev. Res. 2024) have used the MPF to predict flow patterns around T1 transitions and obtained results compatible with those of our hydrodynamic theory. From this comparison we can conclude that both the MPF and our theory are able to capture the same aspect of cell intercalation in epithelial layer. This, however, does not imply that other discrete models of epithelia can reproduce this aspect too, nor that our theory is specifically tailored to the MPF model. We have clarified these points in the revised manuscript and expanded our discussion of the MPF model.

(3) The quality of the numerical results presented in the second part (phase field model) could be improved. (a) In terms of analysis of the defects. It seems that they have all the tools to compare their cell-resolved simulations and their predictions about how a T1 event translates into defects unbinding. However, their analysis in Figure 3e is relatively minimal: it shows a correlation between T1 cells and defects. But it says nothing about the structure and evolution of the defects, which, according to their first section, should be quite precise.

We thank the referee for their comment. Further qualitative evidence have been brought to light in the work of Jain et al. (Phys. Rev. Res. 2024), were the exact flow pattern predicted by our hydrodynamic theory is obtained, in the MPF, around cells undergoing T1 rearrangements.

(b) In terms of clarity of the presentation. For instance, in Figure 3f, they plot the mean-square displacement as a function of a defect density. I thought that MSD was a time-dependent quantity: they must therefore consider MSD at a given time, or averaged over time. They should be explicit about what their definition of this quantity is.

We thank the referee for raising this point. As clarified in our response to Reviewer 1, point 3, the mean square displacement (MSD) plotted in Fig. 3f is computed over a fixed time window of ∆t = 25×103 iterations, chosen to match the typical duration of T1 events and defect lifetimes. [See also reply to Reviewer #1, point (3).] The MSD is normalized by the subregion area and averaged over time within each window. We have now made this explicit in the amended version of the manuscript.

(c) In terms of statistics. For instance, Figure 3g is used to study the role of rotational diffusion on the average time between T1s. The error bars in this figure are huge and make their claims hardly supported. Their claim of a ”monotonic decay” of the average time between intercalations is also not fully supported given their statistics.

We appreciate the Reviewer’s comment regarding the statistical robustness of Fig. 3g. While we acknowledge that the error bars are substantial – reflecting the inherent variability in cell intercalation dynamics – the yellow curve does exhibit a consistent downward trend in the average time between T1 transitions as rotational diffusion increases. This monotonic decrease is visible across the entire range of variation of the rotational diffusion Dr, and is statistically supported when considering the trend over independent simulations. To address this concern, we have revised the main text to adjusted the wording: instead of stating that “the former is a monotonically decreasing function of Dr,” we now write that “the former displays a decreasing trend with Dr,” which better reflects the statistical variability while preserving the observed behavior.

Reviewer #3 (Recommendations for the Authors):

(1) Section 1 is difficult to follow due to multiple reasons: early but delayed definitions, unclear use of T1 intercalation vs. T1 cycles, disconnected figures and unclear simulation descriptions. We recommend including simulation setup details earlier and restructuring the flow of arguments.

We thank the referee for their comment. We have made an effort in rewording and clarifying things in our amended manuscript. We are slightly confused by what they mean by “early but delayed definitions”, if they could clarify, we would be happy to amend the position and phrasing of these definitions accordingly.

(2) It could be useful to have an additional figure early on defining schematically hexatic defects and an illustration showing an epithelium (or a simulation), similar to what the authors have produced in some of their other publications on this topic.

We thank the referee for their comment. Figures 3c and 3d show what a hexatic defect looks like in a simulation of the epithelium. Following the referee’s recommendation, we have added a note in the caption of figure 3, citing our work were we show the same defects in MDCK epithelial monolayers (Armengol et al., Nat. Phys. 2023).

(3) Minor points and typos:

Line 88: the bond between vertices shrinks, not the vertices.

Figure 1: the 1/6 is displayed as 1 6 (fraction bar missing).

Line 232: “and order” → “one/an order”.

Line 237: Fig. 3g) → Fig. 3g

Line 298: ”nu” and ”v” hard to distinguish in eLife font.

Methods: define all notation clearly (e.g., tensor product exponent, D/Dt in Eq. 3c).

Methods: ”cell orientation, coarse-graining and topological defects” section is difficult to follow, schematic would help.

Line 457 onward: unclear how panels (ii-iv) of Fig. 2ab are obtained.

Line 480 onward: not referenced in main text.

Figure 2: “avalancHe” typo.

Figure 2 caption: “cell intercalaTION” typo.

Movies are neither referenced nor explained.

Figure 5 and 6 are not referenced in the main text.

We thank the referee for their detailed read of the paper. We have corrected all typos.

eLife Assessment

This important work attempts to understand observed variability in oral shedding of SARS-CoV-2 and suggests that routine clinical factors are not determinative. The evidence supporting the conclusion is solid though the limited clinical heterogeneity of the included cohorts, the lack of COVID vaccination, and the absence of comprehensive viral load data for model training, makes the results difficult to generalize to contemporaneous COVID-19 conditions. This study may be of interest to virologists, public health officials and clinicians.

Reviewer #1 (Public Review):

Summary:

This study by Park and colleagues uses longitudinal saliva viral load data from two cohorts (one in the US and one in Japan from a clinical trial) in the pre-vaccine era to subset viral shedding kinetics and then use machine learning to attempt to identify clinical correlates of different shedding patterns. The stratification method identifies three separate shedding patterns discriminated by peak viral load, shedding duration, and clearance slope. The authors also assess micro-RNAs as potential biomarkers of severity but do not identify any clear relationships with viral kinetics.

Strengths:

The cohorts are well developed, the mathematical model appears to capture shedding kinetics fairly well, the clustering seems generally appropriate, and the machine learning analysis is a sensible, albeit exploratory approach. The micro-RNA analysis is interesting and novel.

Reviewer #2 (Public Review):

Summary:

This study argues it has found that it has stratified viral kinetics for saliva specimens into three groups by the duration of "viral shedding"; the authors could not identify clinical data or microRNAs that correlate with these three groups.

Strengths:

The question of whether there is a stratification of viral kinetics is interesting.

Reviewer #3 (Public Review):

The article presents a comprehensive study on the stratification of viral shedding patterns in saliva among COVID-19 patients. The authors analyze longitudinal viral load data from 144 mildly symptomatic patients using a mathematical model, identifying three distinct groups based on the duration of viral shedding. Despite analyzing a wide range of clinical data and micro-RNA expression levels, the study could not find significant predictors for the stratified shedding patterns, highlighting the complexity of SARS-CoV-2 dynamics in saliva. The research underscores the need for identifying biomarkers to improve public health interventions and acknowledges several limitations, including the lack of consideration of recent variants, the sparsity of information before symptom onset, and the focus on symptomatic infections.

The manuscript is well-written, with the potential for enhanced clarity in explaining statistical methodologies. This work could inform public health strategies and diagnostic testing approaches.

Comments on the revised version from the editor:

The authors comprehensively addressed the concerns of all 3 reviewers. We are thankful for their considerable efforts to do so. Certain limitations remain unavoidable such as the lack of immunologic diversity among included study participants and lack of contemporaneous variants of concern.

One remaining issue is the continued use of the target cell limited model which is sufficient in most cases, but misses key datapoints in certain participants. In particular, viral rebound is poorly described by this model. Even if viral rebound does not place these cases in a unique cluster, it is well understood that viral rebound is of clinical significance.

In addition, the use of microRNAs as a potential biomarker is still not fully justified. In other words, are there specific microRNAs that have a pre-existing mechanistic basis for relating to higher or lower viral loads? As written it still feels like microRNA was included in the analysis simply because the data existed.

Author response:

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

Reviewer #1 (Public review)

Summary:

This study by Park and colleagues uses longitudinal saliva viral load data from two cohorts (one in the US and one in Japan from a clinical trial) in the pre-vaccine era to subset viral shedding kinetics and then use machine learning to attempt to identify clinical correlates of different shedding patterns. The stratification method identifies three separate shedding patterns discriminated by peak viral load, shedding duration, and clearance slope. The authors also assess micro-RNAs as potential biomarkers of severity but do not identify any clear relationships with viral kinetics.

Strengths:

The cohorts are well developed, the mathematical model appears to capture shedding kinetics fairly well, the clustering seems generally appropriate, and the machine learning analysis is a sensible, albeit exploratory approach. The micro-RNA analysis is interesting and novel.

Weaknesses:

The conclusions of the paper are somewhat supported by the data but there are certain limitations that are notable and make the study's findings of only limited relevance to current COVID-19 epidemiology and clinical conditions.

We sincerely appreciate the reviewer’s thoughtful and constructive comments, which have been invaluable in improving the quality of our study. We have carefully revised the manuscript to address all points raised.

(1) The study only included previously uninfected, unvaccinated individuals without the omicron variant. It has been well documented that vaccination and prior infection both predict shorter duration shedding. Therefore, the study results are no longer relevant to current COVID-19 conditions. This is not at all the authors' fault but rather a difficult reality of much retrospective COVID research.

Thank you for your comment. We agree with the review’s comment that some of our results could not provide insight into the current COVID-19 conditions since most people have either already been infected with COVID-19 or have been vaccinated. We revised our manuscript to discuss this (page 22, lines 364-368). Nevertheless, we believe it is novel that we have extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and microRNA data, and that developing a method to do so remains important. This is important for providing insight into early responses to novel emerging viral diseases in the future. Therefore, we still believe that our findings are valuable.

(2) The target cell model, which appears to fit the data fairly well, has clear mechanistic limitations. Specifically, if such a high proportion of cells were to get infected, then the disease would be extremely severe in all cases. The authors could specify that this model was selected for ease of use and to allow clustering, rather than to provide mechanistic insight. It would be useful to list the AIC scores of this model when compared to the model by Ke.

Thank you for your feedback and suggestion regarding our mathematical model. As the reviewer pointed out, in this study, we adopted a simple model (target cell-limited model) to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this point (page 10, lines 139-144). Also, we revised our manuscript to provide more detailed description of the model comparison along with information about AIC (page 10, lines 130-135).

(3) Line 104: I don't follow why including both datasets would allow one model to work better than the other. This requires more explanation. I am also not convinced that non-linear mixed effects approaches can really be used to infer early model kinetics in individuals from one cohort by using late viral load kinetics in another (and vice versa). The approach seems better for making populationlevel estimates when there is such a high amount of missing data.

Thank you for your feedback. We recognized that our explanation was insufficient by your comment. We intended to describe that, rather than comparing performance of the two models, data fitting can be performed with same level for both models by including both datasets. We revised the manuscript to clarify this point (page 10, lines 135-139).

Additionally, we agree that nonlinear mixed effects models are a useful approach for performing population-level estimates of missing data. On the other hand, in addition, the nonlinear mixed effects model has the advantage of making the reasonable parameter estimation for each individual with not enough data points by considering the distribution of parameters of other individuals. Paying attention to these advantages, we adopted a nonlinear mixed effects model in our study. We also revised the manuscript to clarify this (page 27, lines 472-483).

(4) Along these lines, the three clusters appear to show uniform expansion slopes whereas the NBA cohort, a much larger cohort that captured early and late viral loads in most individuals, shows substantial variability in viral expansion slopes. In Figure 2D: the upslope seems extraordinarily rapid relative to other cohorts. I calculate a viral doubling time of roughly 1.5 hours. It would be helpful to understand how reliable of an estimate this is and also how much variability was observed among individuals.

We appreciate your detailed feedback on the estimated up-slope of viral dynamics. As the reviewer noted, the pattern differs from that observed in the NBA cohort, which may be due to their measurement of viral load from upper respiratory tract swabs. In our estimation, the mean and standard deviation of the doubling time (defined as ln2/(𝛽𝑇₀𝑝𝑐⁻¹ − 𝛿)) were 1.44 hours and 0.49 hours, respectively. Although direct validation of these values is challenging, several previous studies, including our own, have reported that viral loads in saliva increase more rapidly than in the upper respiratory tract swabs, reaching their peak sooner. Thus, we believe that our findings are consistent with those of previous studies. We revised our manuscript to discuss this point with additional references (page 20, lines 303-311).

(5) A key issue is that a lack of heterogeneity in the cohort may be driving a lack of differences between the groups. Table 1 shows that Sp02 values and lab values that all look normal. All infections were mild. This may make identifying biomarkers quite challenging.

Thank you for your comment regarding heterogeneity in the cohort. Although the NFV cohort was designed for COVID-19 patients who were either mild or asymptomatic, we have addressed this point and revised the manuscript to discuss it (page 21, lines 334-337).

(6) Figure 3A: many of the clinical variables such as basophil count, Cl, and protein have very low pre-test probability of correlating with virologic outcome.

Thank you for your comment regarding some clinical information we used in our study. We revised our manuscript to discuss this point (page 21, lines 337-338).

(7) A key omission appears to be micoRNA from pre and early-infection time points. It would be helpful to understand whether microRNA levels at least differed between the two collection timepoints and whether certain microRNAs are dynamic during infection.

Thank you for your comment regarding the collection of micro-RNA data. As suggested by the reviewer, we compared micro-RNA levels between two time points using pairwise t-tests and Mann-Whitney U tests with FDR correction. As a result, no micro-RNA showed a statistically significant difference. This suggests that micro-RNA levels remain relatively stable during the course of infection, at least for mild or asymptomatic infection, and may therefore serve as a biomarker independent of sampling time. We have revised the manuscript to include this information (page 17, lines 259-262).

(8) The discussion could use a more thorough description of how viral kinetics differ in saliva versus nasal swabs and how this work complements other modeling studies in the field.

We appreciate the reviewer’s thoughtful feedback. As suggested, we have added a discussion comparing our findings with studies that analyzed viral dynamics using nasal swabs, thereby highlighting the differences between viral dynamics in saliva and in the upper respiratory tract. To ensure a fair and rigorous comparison, we referred to studies that employed the same mathematical model (i.e., Eqs.(1-2)). Accordingly, we revised the manuscript and included additional references (page 20, lines 303-311).

Furthermore, we clarified the significance of our study in two key aspects. First, it provides a detailed analysis of viral dynamics in saliva, reinforcing our previous findings from a single cohort by extending them across multiple cohorts. Second, this study uniquely examines whether viral dynamics in saliva can be directly predicted by exploring diverse clinical data and micro-RNAs. Notably, cohorts that have simultaneously collected and reported both viral load and a broad spectrum of clinical data from the same individuals, as in our study, are exceedingly rare. We revised the manuscript to clarify this point (page 20, lines 302-311).

(9) The most predictive potential variables of shedding heterogeneity which pertain to the innate and adaptive immune responses (virus-specific antibody and T cell levels) are not measured or modeled.

Thank you for your comment. We agree that antibody and T cell related markers may serve as the most powerful predictors, as supported by our own study [S. Miyamoto et al., PNAS (2023), ref. 24] as well as previous reports. While this point was already discussed in the manuscript, we have revised the text to make it more explicit (page 21, lines 327-328).

(10) I am curious whether the models infer different peak viral loads, duration, expansion, and clearance slopes between the 2 cohorts based on fitting to different infection stage data.

Thank you for your comment. We compared features between 2 cohorts as reviewer suggested. As a result, a statistically significant difference between the two cohorts (i.e., p-value ≤ 0.05 from the t-test) was observed only at the peak viral load, with overall trends being largely similar. At the peak, the mean value was 7.5 log₁₀ (copies/mL) in the Japan cohort and 8.1 log₁₀ (copies/mL) in the Illinois cohort, with variances of 0.88 and 0.87, respectively, indicating comparable variability.

Reviewer #2 (Public review)

Summary:

This study argues it has found that it has stratified viral kinetics for saliva specimens into three groups by the duration of "viral shedding"; the authors could not identify clinical data or microRNAs that correlate with these three groups.

Strengths:

The question of whether there is a stratification of viral kinetics is interesting.

Weaknesses:

The data underlying this work are not treated rigorously. The work in this manuscript is based on PCR data from two studies, with most of the data coming from a trial of nelfinavir (NFV) that showed no effect on the duration of SARS-CoV-2 PCR positivity. This study had no PCR data before symptom onset, and thus exclusively evaluated viral kinetics at or after peak viral loads. The second study is from the University of Illinois; this data set had sampling prior to infection, so has some ability to report the rate of "upswing." Problems in the analysis here include:

We are grateful to the reviewer for the constructive feedback, which has greatly enhanced the quality of our study. In response, we have carefully revised the manuscript to address all comments.

The PCR Ct data from each study is treated as equivalent and referred to as viral load, without any reports of calibration of platforms or across platforms. Can the authors provide calibration data and justify the direct comparison as well as the use of "viral load" rather than "Ct value"? Can the authors also explain on what basis they treat Ct values in the two studies as identical?

Thank you for your comment regarding description of viral load data. We recognized the lack of explanation for the integration of viral load data by reviewer's comment. We calculated viral load from Ct value using linear regression equations between Ct and viral load for each study's measurement method, respectively. We revised the manuscript to clarify this point in the section of Saliva viral load data in Methods.

The limit of detection for the NFV PCR data was unclear, so the authors assumed it was the same as the University of Illinois study. This seems a big assumption, as PCR platforms can differ substantially. Could the authors do sensitivity analyses around this assumption?

Thank you for your comment regarding the detection limit for viral load data. As reviewer suggested, we conducted sensitivity analysis for assumption of detection limit for the NFV dataset. Specifically, we performed data fitting in the same manner for two scenarios: when the detection limit of NFV PCR was lower (0 log₁₀ copies/mL) or higher (2 log₁₀ copies/mL) than that of the Illinois data (1.08 log₁₀ copies/mL), and compared the results.

As a result, we obtained largely comparable viral dynamics in most cases (Supplementary Fig 6). When comparing the AIC values, we observed that the AIC for the same censoring threshold was 6836, whereas it increased to 7403 under the low censoring threshold and decreased to 6353 under the higher censoring threshold. However, this difference may be attributable to the varying number of data points treated as below the detection limit. Specifically, when the threshold is set higher, more data are treated as below the detection limit, which may result in a more favorable error calculation. To discuss this point, we have added a new figure (Supplementary Fig 6) and revised the manuscript accordingly (page 25, lines 415-418).

The authors refer to PCR positivity as viral shedding, but it is viral RNA detection (very different from shedding live/culturable virus, as shown in the Ke et al. paper). I suggest updating the language throughout the manuscript to be precise on this point.

We appreciate the reviewer’s feedback regarding the terminology used for viral shedding. In response, we have revised all instances of “viral shedding” to “viral RNA detection” throughout the manuscript as suggested.

Eyeballing extended data in Figure 1, a number of the putative long-duration infections appear to be likely cases of viral RNA rebound (for examples, see S01-16 and S01-27). What happens if all the samples that look like rebound are reanalyzed to exclude the late PCR detectable time points that appear after negative PCRs?

We sincerely thank the reviewer for the valuable suggestion. In response, we established a criterion to remove data that appeared to exhibit rebound and subsequently performed data fitting

(see Author response image 1 below). The criterion was defined as: “any data that increase again after reaching the detection limit in two measurements are considered rebound and removed.” As a result, 15 out of 144 cases were excluded due to insufficient usable data, leaving 129 cases for analysis. Using a single detection limit as the criterion would have excluded too many data points, while defining the criterion solely based on the magnitude of increase made it difficult to establish an appropriate “threshold for increase.”

The fitting result indicates that the removal of rebound data may influence the fitting results; however, direct comparison of subsequent analyses, such as clustering, is challenging due to the reduced sample size. Moreover, the results can vary substantially depending on the criterion used to define rebound, and establishing a consistent standard remains difficult. Accordingly, we retained the current analysis and have added a discussion of rebound phenomena in the Discussion section as a limitation (page 22, lines 355-359). We once again sincerely appreciate the reviewer’s insightful and constructive suggestion.

Author response image 1.

Comparison of model fits before and after removing data suspected of rebound. Black dots represent observed measurements, and the black and yellow curves show the fitted viral dynamics for the full dataset and the dataset with rebound data removed, respectively.

There's no report of uncertainty in the model fits. Given the paucity of data for the upslope, there must be large uncertainty in the up-slope and likely in the peak, too, for the NFV data. This uncertainty is ignored in the subsequent analyses. This calls into question the efforts to stratify by the components of the viral kinetics. Could the authors please include analyses of uncertainty in their model fits and propagate this uncertainty through their analyses?

We sincerely appreciate the reviewer’s detailed feedback on model uncertainty. To address this point, we revised Extended Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach. In addition, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information through Result and Methods sections (page 11, lines 159-162 and page 28, lines 512-519). Once again, we are deeply grateful for this insightful comment.

The clinical data are reported as a mean across the course of an infection; presumably vital signs and blood test results vary substantially, too, over this duration, so taking a mean without considering the timing of the tests or the dynamics of their results is perplexing. I'm not sure what to recommend here, as the timing and variation in the acquisition of these clinical data are not clear, and I do not have a strong understanding of the basis for the hypothesis the authors are testing.

We appreciate the reviewers' feedback on the clinical data. We recognized that the manuscript lacked description of the handling of clinical data by your comment. In this research, we focused on finding “early predictors” which could provide insight into viral shedding patterns. Thus, we used clinical data measured in the earliest time (date of admission) for each patient. Another reason is that the date of admission is the almost only time point at which complete clinical data without any missing values are available for all participants. We revised our manuscript to clarify this point (page 5, lines 90-95).

It's unclear why microRNAs matter. It would be helpful if the authors could provide more support for their claims that (1) microRNAs play such a substantial role in determining the kinetics of other viruses and (2) they play such an important role in modulating COVID-19 that it's worth exploring the impact of microRNAs on SARS-CoV-2 kinetics. A link to a single review paper seems insufficient justification. What strong experimental evidence is there to support this line of research?

We appreciate the reviewer’s comments regarding microRNA. Based on this feedback, we recognized the need to clarify our rationale for selecting microRNAs as the analyte. The primary reason was that our available specimens were saliva, and microRNAs are among the biomarkers that can be reliably measured in saliva. At the same time, previous studies have reported associations between microRNAs and various diseases, which led us to consider the potential relevance of microRNAs to viral dynamics, beyond their role as general health indicators. To better reflect this context, we have added supporting references (page 17, lines 240-243).

Reviewer #3 (Public review)

The article presents a comprehensive study on the stratification of viral shedding patterns in saliva among COVID-19 patients. The authors analyze longitudinal viral load data from 144 mildly symptomatic patients using a mathematical model, identifying three distinct groups based on the duration of viral shedding. Despite analyzing a wide range of clinical data and micro-RNA expression levels, the study could not find significant predictors for the stratified shedding patterns, highlighting the complexity of SARS-CoV-2 dynamics in saliva. The research underscores the need for identifying biomarkers to improve public health interventions and acknowledges several limitations, including the lack of consideration of recent variants, the sparsity of information before symptom onset, and the focus on symptomatic infections. 

The manuscript is well-written, with the potential for enhanced clarity in explaining statistical methodologies. This work could inform public health strategies and diagnostic testing approaches. However, there is a thorough development of new statistical analysis needed, with major revisions to address the following points:

We sincerely appreciate the thoughtful feedback provided by Reviewer #3, particularly regarding our methodology. In response, we conducted additional analyses and revised the manuscript accordingly. Below, we address the reviewer’s comments point by point.

(1) Patient characterization & selection: Patient immunological status at inclusion (and if it was accessible at the time of infection) may be the strongest predictor for viral shedding in saliva. The authors state that the patients were not previously infected by SARS-COV-2. Was Anti-N antibody testing performed? Were other humoral measurements performed or did everything rely on declaration? From Figure 1A, I do not understand the rationale for excluding asymptomatic patients. Moreover, the mechanistic model can handle patients with only three observations, why are they not included? Finally, the 54 patients without clinical data can be used for the viral dynamics fitting and then discarded for the descriptive analysis. Excluding them can create a bias. All the discarded patients can help the virus dynamics analysis as it is a population approach. Please clarify. In Table 1 the absence of sex covariate is surprising.

We appreciate the detailed feedback from the reviewer regarding patient selection. We relied on the patient's self-declaration to determine the patient's history of COVID-19 infection and revised the manuscript to specify this (page 6, lines 83-84).

In parameter estimation, we used the date of symptom onset for each patient so that we establish a baseline of the time axis as clearly as possible, as we did in our previous works. Accordingly, asymptomatic patients who do not have information on the date of symptom onset were excluded from the analysis. Additionally, in the cohort we analyzed, for patients excluded due to limited number of observations (i.e., less than 3 points), most patients already had a viral load close to the detection limit at the time of the first measurement. This is due to the design of clinical trial, as if a negative result was obtained twice in a row, no further follow-up sampling was performed. These patients were excluded from the analysis because it hard to get reasonable fitting results. Also, we used 54 patients for the viral dynamics fitting and then only used the NFV cohort for clinical data analysis. We acknowledge that our description may have confused readers. We revised our manuscript to clarify these points regarding patient selecting for data fitting (page 6, lines 96-102, page 24, lines 406-407, and page 7, lines 410-412). In addition, we realized, thanks to the reviewer’s comment, that gender information was missing in Table 1. We appreciate this observation and have revised the table to include gender (we used gender in our analysis). 

(2) Exact study timeline for explanatory covariates: I understand the idea of finding « early predictors » of long-lasting viral shedding. I believe it is key and a great question. However, some samples (Figure 4A) seem to be taken at the end of the viral shedding. I am not sure it is really easier to micro-RNA saliva samples than a PCR. So I need to be better convinced of the impact of the possible findings. Generally, the timeline of explanatory covariate is not described in a satisfactory manner in the actual manuscript. Also, the evaluation and inclusion of the daily symptoms in the analysis are unclear to me.

We appreciate the reviewer’s feedback regarding the collection of explanatory variables. As noted, of the two microRNA samples collected from each patient, one was obtained near the end of viral shedding. This was intended to examine potential differences in microRNA levels between the early and late phases of infection. No significant differences were observed between the two time points, and using microRNA from either phase alone or both together did not substantially affect predictive accuracy for stratified groups. Furthermore, microRNA collection was motivated primarily by the expectation that it would be more sensitive to immune responses, rather than by ease of sampling. We have revised the manuscript to clarify these points regarding microRNA (page 17, lines 243-245 and 259-262).

Furthermore, as suggested by the reviewer, we have also strengthened the explanation regarding the collection schedule of clinical information and the use of daily symptoms in the analysis (page 6, lines 90-95, page 14, lines 218-220,).

(3) Early Trajectory Differentiation: The model struggles to differentiate between patients' viral load trajectories in the early phase, with overlapping slopes and indistinguishable viral load peaks observed in Figures 2B, 2C, and 2D. The question arises whether this issue stems from the data, the nature of Covid-19, or the model itself. The authors discuss the scarcity of pre-symptom data, primarily relying on Illinois patients who underwent testing before symptom onset. This contrasts earlier statements on pages 5-6 & 23, where they claim the data captures the full infection dynamics, suggesting sufficient early data for pre-symptom kinetics estimation. The authors need to provide detailed information on the number or timing of patient sample collections during each period.

Thank you for the reviewer’s thoughtful comments. The model used in this study [Eqs.(1-2)] has been employed in numerous prior studies and has successfully identified viral dynamics at the individual level. In this context, we interpret the rapid viral increase observed across participants as attributable to characteristics of SARS-CoV-2 in saliva, an interpretation that has also been reported by multiple previous studies. We have added the relevant references and strengthened the corresponding discussion in the manuscript (page 20, lines 303-311).

We acknowledge that our explanation of how the complementary relationship between the two cohorts contributes to capturing infection dynamics was not sufficiently clear. As described in the manuscript, the Illinois cohort provides pre-symptomatic data, whereas the NFV cohort offers abundant end-phase data, thereby compensating for each other’s missing phases. By jointly analyzing the two cohorts with a nonlinear mixed-effects model, we estimated viral dynamics at the individual-level. This approach first estimates population-level parameters (fixed effects) using data from all participants and then incorporates random effects to account for individual variability, yielding the most plausible parameter values.

Thus, even when early-phase data are lacking in the NFV cohort, information from the Illinois cohort allows us to infer most reasonable dynamics, and the reverse holds true for the end phase. In this context, we argued that combining the two cohorts enables mathematical modeling to capture infection dynamics at the individual level. Recognizing that our earlier description could be misleading, we have carefully reinforced the relevant description (page 27, lines 472-483). In addition, as suggested by the reviewer, we have added information on the number of data samples available for each phase in both cohorts (page 7, lines 106-109).

(4) Conditioning on the future: Conditioning on the future in statistics refers to the problematic situation where an analysis inadvertently relies on information that would not have been available at the time decisions were made or data were collected. This seems to be the case when the authors create micro-RNA data (Figure 4A). First, when the sampling times are is something that needs to be clarified by the authors (for clinical outcomes as well). Second, proper causal inference relies on the assumption that the cause precedes the effect. This conditioning on the future may result in overestimating the model's accuracy. This happens because the model has been exposed to the outcome it's supposed to predict. This could question the - already weak - relation with mir-1846 level.

We appreciate the reviewer’s detailed feedback. As noted in Reply to Comments 2, we collected micro-RNA samples at two time points, near the peak of infection dynamics and at the end stage, and found no significant differences between them. This suggests that micro-RNA levels are not substantially affected by sampling time. Indeed, analyses conducted using samples from the peak, late stage, or both yielded nearly identical results in relation to infection dynamics. To clarify this point, we revised the manuscript by integrating this explanation with our response in Reply to Comments 2 (page 17, lines 259-262). In addition, now we also revised manuscript to clarify sampling times of clinical information and micro-RNA (page 6, lines 90-95).

(5) Mathematical Model Choice Justification and Performance: The paper lacks mention of the practical identifiability of the model (especially for tau regarding the lack of early data information). Moreover, it is expected that the immune effector model will be more useful at the beginning of the infection (for which data are the more parsimonious). Please provide AIC for comparison, saying that they have "equal performance" is not enough. Can you provide at least in a point-by-point response the VPC & convergence assessments?

We appreciate the reviewer’s detailed feedback regarding the mathematical model. We acknowledge the potential concern regarding the practical identifiability of tau (incubation period), particularly given the limited early-phase data. In our analysis, however, the nonlinear mixed-effects model yielded a population-level estimate of 4.13 days, which is similar with previously reported incubation periods for COVID-19. This concordance suggests that our estimate of tau is reasonable despite the scarcity of early data.

For model comparison, first, we have added information on the AIC of the two models to the manuscript as suggested by the reviewer (page 10, lines 130-135). One point we would like to emphasize is that we adopted a simple target cell-limited model in this study, aiming to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this (page 10, lines 135-144). 

Furthermore, as suggested, we have added the VPC and convergence assessment results for both models, together with explanatory text, to the manuscript (Supplementary Fig 2, Supplementary Fig 3, and page 10, lines 130-135). In the VPC, the observed 5th, 50th, and 95th percentiles were generally within the corresponding simulated prediction intervals across most time points. Although minor deviations were noted in certain intervals, the overall distribution of the observed data was well captured by the models, supporting their predictive performance (Supplementary Fig 2). In addition, the log-likelihood and SAEM parameter trajectories stabilized after the burn-in phase, confirming appropriate convergence (Supplementary Fig 3).

(6) Selected features of viral shedding: I wonder to what extent the viral shedding area under the curve (AUC) and normalized AUC should be added as selected features.

We sincerely appreciate the reviewer’s valuable suggestion regarding the inclusion of additional features. Following this recommendation, we considered AUC (or normalized AUC) as an additional feature when constructing the distance matrix used for stratification. We then evaluated the similarity between the resulting distance matrix and the original one using the Mantel test, which showed a very high correlation (r = 0.92, p < 0.001). This indicates that incorporating AUC as an additional feature does not substantially alter the distance matrix. Accordingly, we have decided to retain the current stratification analysis, and we sincerely thank the reviewer once again for this interesting suggestion.

(7) Two-step nature of the analysis: First you fit a mechanistic model, then you use the predictions of this model to perform clustering and prediction of groups (unsupervised then supervised). Thus you do not propagate the uncertainty intrinsic to your first estimation through the second step, ie. all the viral load selected features actually have a confidence bound which is ignored. Did you consider a one-step analysis in which your covariates of interest play a direct role in the parameters of the mechanistic model as covariates? To pursue this type of analysis SCM (Johnson et al. Pharm. Res. 1998), COSSAC (Ayral et al. 2021 CPT PsP), or SAMBA ( Prague et al. CPT PsP 2021) methods can be used. Did you consider sampling on the posterior distribution rather than using EBE to avoid shrinkage?

Thank you for the reviewer’s detailed suggestions regarding our analysis. We agree that the current approach does not adequately account for the impact of uncertainty in viral dynamics on the stratified analyses. As a first step, we have revised Extended Data Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach, to present the model-fitting uncertainty more explicitly. Then, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information (page 11, lines 159-162 and page 28, 512-519).

Furthermore, we carefully considered the reviewer’s proposed one-step analysis. However, implementation was constrained by data-fitting limitations. Concretely, clinical information is available only in the NFV cohort. Thus, if these variables are to be entered directly as covariates on the parameters, the Illinois cohort cannot be included in the data-fitting process. Yet the NFV cohort lacks any pre-symptomatic observations, so fitting the model to that cohort alone does not permit a reasonable (well-identified/robust) fitting result. While we were unable to implement the suggestion under the current data constraints, we sincerely appreciate the reviewer’s thoughtful and stimulating proposal.

(8) Need for advanced statistical methods: The analysis is characterized by a lack of power. This can indeed come from the sample size that is characterized by the number of data available in the study. However, I believe the power could be increased using more advanced statistical methods. At least it is worth a try. First considering the unsupervised clustering, summarizing the viral shedding trajectories with features collapses longitudinal information. I wonder if the R package « LongituRF » (and associated method) could help, see Capitaine et al. 2020 SMMR. Another interesting tool to investigate could be latent class models R package « lcmm » (and associated method), see ProustLima et al. 2017 J. Stat. Softwares. But the latter may be more far-reached.

Thank you for the reviewer’s thoughtful suggestions regarding our unsupervised clustering approach. The R package “LongitiRF” is designed for supervised analysis, requiring a target outcome to guide the calculation of distances between individuals (i.e., between viral dynamics). In our study, however, the goal was purely unsupervised clustering, without any outcome variable, making direct application of “LongitiRF” challenging.

Our current approach (summarizing each dynamic into several interpretable features and then using Random Forest proximities) allows us to construct a distance matrix in an unsupervised manner. Here, the Random Forest is applied in “proximity mode,” focusing on how often dynamics are grouped together in the trees, independent of any target variable. This provides a practical and principled way to capture overall patterns of dynamics while keeping the analysis fully unsupervised.

Regarding the suggestion to use latent class mixed models (R package “lcmm”), we also considered this approach. In our dataset, each subject has dense longitudinal measurements, and at many time points, trajectories are very similar across subjects, resulting in minimal inter-individual differences. Consequently, fitting multi-class latent class mixed models (ng ≥ 2) with random effects or mixture terms is numerically unstable, often producing errors such as non-positive definite covariance matrices or failure to generate valid initial values. Although one could consider using only the time points with the largest differences, this effectively reduces the analysis to a feature-based summary of dynamics. Such an approach closely resembles our current method and contradicts the goal of clustering based on full longitudinal information.

Taken together, although we acknowledge that incorporating more longitudinal information is important, we believe that our current approach provides a practical, stable, and informative solution for capturing heterogeneity in viral dynamics. We would like to once again express our sincere gratitude to the reviewer for this insightful suggestion.

(9) Study intrinsic limitation: All the results cannot be extended to asymptomatic patients and patients infected with recent VOCs. It definitively limits the impact of results and their applicability to public health. However, for me, the novelty of the data analysis techniques used should also be taken into consideration.

We appreciate your positive evaluation of our research approach and acknowledge that, as noted in the Discussion section as our first limitation, our analysis may not provide valid insights into recent VOCs or all populations, including asymptomatic individuals. Nonetheless, we believe it is novel that we extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and micro-RNA data. Our findings contribute to a deeper and more quantitative understanding of heterogeneity in viral dynamics, particularly in saliva samples. To discuss this point, we revised our manuscript (page 22, lines 364-368).

Strengths are:

Unique data and comprehensive analysis.

Novel results on viral shedding.

Weaknesses are:

Limitation of study design.

The need for advanced statistical methodology.

Reviewer #1 (Recommendations For The Authors):

Line 8: In the abstract, it would be helpful to state how stratification occurred.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 2, lines 8-11).

Line 31 and discussion: It is important to mention the challenges of using saliva as a specimen type for lab personnel.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 36-41).

Line 35: change to "upper respiratory tract".

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, line 35).

Line 37: "Saliva" is not a tissue. Please hazard a guess as to which tissue is responsible for saliva shedding and if it overlaps with oral and nasal swabs.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 42-45).

Line 42, 68: Please explain how understanding saliva shedding dynamics would impact isolation & screening, diagnostics, and treatments. This is not immediately intuitive to me.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 48-50).

Line 50: It would be helpful to explain why shedding duration is the best stratification variable.

We thank the reviewer for the feedback. We acknowledge that our wording was ambiguous. The clear differences in the viral dynamics patterns pertain to findings observed following the stratification, and we have revised the manuscript to make this explicit (page 4, lines 59-61).

Line 71: Dates should be listed for these studies.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 6, lines 85-86).

Reviewer #2 (Recommendations For The Authors):

Please make all code and data available for replication of the analyses.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

Reviewer #3 (Recommendations For The Authors):

Here are minor comments / technical details:

(1) Figure 1B is difficult to understand.

Thank you for the comment. We updated Fig 1B to incorporate more information to aid interpretation.

(2) Did you analyse viral load or the log10 of viral load? The latter is more common. You should consider it. SI Figure 1 please plot in log10 and use a different point shape for censored data. The file quality of this figure should be improved. State in the material and methods if SE with moonlit are computed with linearization or importance sampling.

Thank you for the comment. We conducted our analyses using log10-transformed viral load. Also, we revised Supplementary Fig 1 (now renumbered as Supplementary Fig 4) as suggested. We also added Supplementary Fig 3 and clarified in the Methods that standard errors (SE) were obtained in Monolix from the Fisher information matrix using the linearization method (page 28, lines 498-499).

(3) Table 1 and Figure 3A could be collapsed.

Thank you for the comment, and we carefully considered this suggestion. Table 1 summarizes clinical variables by category, whereas Fig 3A visualizes them ordered by p-value of statistical analysis. Collapsing these into a single table would make it difficult to apprehend both the categorical summaries and the statistical ranking at a glance, thereby reducing readability. We therefore decided to retain the current layout. We appreciate the constructive feedback again. 

(4) Figure 3 legend could be clarified to understand what is 3B and 3C.

We thank the reviewer for the feedback and have reinforced the description accordingly.

(5) Why use AIC instead of BICc?

Thank you for your comment. We also think BICc is a reasonable alternative. However, because our objective is predictive adequacy (reconstruction of viral dynamics), we judged AIC more appropriate. In NLMEM settings, the effective sample size required by BICc is ambiguous, making the penalty somewhat arbitrary. Moreover, since the two models reconstruct very similar dynamics, our conclusions are not sensitive to the choice of criterion.

(6) Bibliography. Most articles are with et al. (which is not standard) and some are with an extended list of names. Provide DOI for all.

We thank the reviewer for the feedback, and have revised the manuscript accordingly.

(7) Extended Table 1&2 - maybe provide a color code to better highlight some lower p-values (if you find any interesting).

We thank the reviewer for the feedback. Since no clinical information and micro-RNAs other than mir-1846 showed low p-values, we highlighted only mir-1846 with color to make it easier to locate.

(8) Please make the replication code available.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

eLife Assessment

The findings of this study are valuable as it demonstrates that when treatment is initiated during acute infection, HIV specific CD8 T cell responses are maintained long term and continued proliferative capacity of these cells may play a role in reducing HIV DNA levels. The evidence supporting the conclusions are solid with rigorous and advanced methodology used with the major limitations being that the findings are association level and do not meet strict criteria for causality. The work is of interest to the HIV cure field and suggests that enhancing early HIV specific CD8 T cell responses should be considered in the design of interventional cure strategies.

Reviewer #2 (Public review):

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies.

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper.

The study's limitations are minor and well acknowledged. While the cohort included only male participants-potentially limiting generalizability-the authors have clarified this limitation in the discussion. Although a chronic infection control group was not yet available, the authors explained that their protocol includes plans to add this comparison in future studies. These limitations are appropriately addressed and do not undermine the strength or validity of the study's conclusions.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this work, van Paassen et al. have studied how CD8 T cell functionality and levels predict HIV DNA decline. The article touches on interesting facets of HIV DNA decay, but ultimately comes across as somewhat hastily done and not convincing due to the major issues. 

(1) The use of only 2 time points to make many claims about longitudinal dynamics is not convincing. For instance, the fact that raw data do not show decay in intact, but do for defective/total, suggests that the present data is underpowered. The authors speculate that rising intact levels could be due to patients who have reservoirs with many proviruses with survival advantages, but this is not the parsimonious explanation vs the data simply being noisy without sufficient longitudinal follow-up. n=12 is fine, or even reasonably good for HIV reservoir studies, but to mitigate these issues would likely require more time points measured per person. 

(1b) Relatedly, the timing of the first time point (6 months) could be causing a number of issues because this is in the ballpark for when the HIV DNA decay decelerates, as shown by many papers. This unfortunate study design means some of these participants may already have stabilized HIV DNA levels, so earlier measurements would help to observe early kinetics, but also later measurements would be critical to be confident about stability. 

The main goal of the present study was to understand the relationship of the HIV-specific CD8 T-cell responses early on ART with the reservoir changes across the subsequent 2.5-year period on suppressive therapy. We have revised the manuscript in order to clarify this.  We chose these time points because the 24 week time point is past the initial steep decline of HIV DNA, which takes place in the first weeks after ART initiation. It is known that HIV DNA continues to decay for years after (Besson, Lalama et al. 2014, Gandhi, McMahon et al. 2017). 

(2) Statistical analysis is frequently not sufficient for the claims being made, such that overinterpretation of the data is problematic in many places. 

(2a) First, though plausible that cd8s influence reservoir decay, much more rigorous statistical analysis would be needed to assert this directionality; this is an association, which could just as well be inverted (reservoir disappearance drives CD8 T cell disappearance). 

To correlate different reservoir measures between themselves and with CD8+ T-cell responses at 24 and 156 weeks, we now performed non-parametric (Spearman) correlation analyses, as they do not require any assumptions about the normal distribution of the independent and dependent variables. Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results. 

Following this comment we would like to note that the association between the T-cell response at 24 weeks and the subsequent decrease in the reservoir cannot be bi-directional (that can only be the case when both variables are measured at the same time point). Therefore, to model the predictive value of T-cell responses measured at 24 weeks for the decrease in the reservoir between 24 and 156 weeks, we fitted generalized linear models (GLM), in which we included age and ART regimen, in addition to three different measures of HIV-specific CD8+ T-cell responses, as explanatory variables, and changes in total, intact, and total defective HIV DNA between 24 and 156 weeks ART as dependent variables.

(2b) Words like "strong" for correlations must be justified by correlation coefficients, and these heat maps indicate many comparisons were made, such that p-values must be corrected appropriately. 

We have now used Spearman correlation analysis, provided correlation coefficients to justify the wording, and adjusted the p-values for multiple comparisons (Fig. 1, Fig 3., Table 2). Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results.  

(3) There is not enough introduction and references to put this work in the context of a large/mature field. The impacts of CD8s in HIV acute infection and HIV reservoirs are both deep fields with a lot of complexity. 

Following this comment we have revised and expanded the introduction to put our work more in the context of the field (CD8s in acute HIV and HIV reservoirs). 

Reviewer #2 (Public review): 

Summary: 

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow-up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies. 

Strengths: 

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper. 

Weaknesses: 

All participants were male (acknowledged by the authors), potentially reducing the generalizability of the findings to broader populations. A control group receiving ART during chronic infection would have been an interesting comparison. 

We thank the reviewer for their appreciation of our study. Although we had indeed acknowledged the fact that all participants were male, we have clarified why this is a limitation of the study (Discussion, lines 296-298). The reviewer raises the point that it would be useful to compare our data to a control group. Unfortunately, these samples are not yet available, but our study protocol allows for a control group (chronic infection) to ensure we can include a control group in the future.

Reviewer #1 (Recommendations for the authors): 

Minor: 

On the introduction: 

(1) One large topic that is mostly missing completely is the emerging evidence of selection on HIV proviruses during ART from the groups of Xu Yu and Matthias Lichterfeld, and Ya Chi Ho, among others. 

Previously, it was only touched upon in the Discussion. Now we have also included this in the Introduction (lines 77-80).

(2) References 4 and 5 don't quite match with the statement here about reservoir seeding; we don't completely understand this process, and certainly, the tissue seeding aspect is not known. 

Line 61-62: references were changed and this paragraph was rewritten to clarify.

(3) Shelton et al. showed a strong relationship with HIV DNA size and timing of ART initiation across many studies. I believe Ananwaronich also has several key papers on this topic. 

References by Ananwaronich are included (lines 91-94).

(4) "the viral levels decline within weeks of AHI", this is imprecise, there is a peak and a decline, and an equilibrium. 

We agree and have rewritten the paragraph accordingly.

(5) The impact of CD8 cells on viral evolution during primary infection is complex and likely not relevant for this paper. 

We have left viral evolution out of the introduction in order to keep a focus on the current subject.

(6) The term "reservoir" is somewhat polarizing, so it might be worth mentioning somewhere exactly what you think the reservoir is, I think, as written, your definition is any HIV DNA in a person on ART? 

Indeed, we refer to the reservoir when we talk about the several aspects of the reservoir that we have quantified with our assays (total HIV DNA, unspliced RNA, intact and defective proviral DNA, and replication-competent virus). In most instances we try to specify which measurement we are referring to. We have added additional reservoir explanation to clarify our definition to the introduction (lines 55-58).

(7) I think US might be used before it is defined. 

We thank the reviewer for this notification, we have now also defined it in the Results section (line 131).

(8) In Figure 1 it's also not clear how statistics were done to deal with undetectable values, which can be tricky but important. 

We have now clarified this in the legend to Figure 2 (former Figure 1). Paired Wilcoxon tests were performed to test the significance of the differences between the time points. Pairs where both values were undetectable were always excluded from the analysis. Pairs where one value was undetectable and its detection limit was higher than the value of the detectable partner, were also excluded from the analysis. Pairs where one value was undetectable and its detection limit was lower than the value of the detectable partner, were retained in the analysis.

In the discussion: 

(1) "This confirms that the existence of a replication-competent viral reservoir is linked to the presence of intact HIV DNA." I think this statement is indicative of many of the overinterpretations without statistical justification. There are 4 of 12 individuals with QVOA+ detectable proviruses, which means there are 8 without. What are their intact HIV DNA levels? 

We thank the reviewer for the question that is raised here. We have now compared the intact DNA levels (measured by IPDA) between participants with positive vs. negative QVOA output, and observed a significant difference. We rephrased the wording as follows: “We compared the intact HIV DNA levels at the 24-week timepoint between the six participants, from whom we were able to isolate replicating virus, and the fourteen participants, from whom we could not. Participants with positive QVOA had significantly higher intact HIV DNA levels than those with negative QVOA (p=0.029, Mann-Whitney test; Suppl. Fig. 3). Five of six participants with positive QVOA had intact DNA levels above 100 copies/106 PBMC, while thirteen of fourteen participants with negative QVOA had intact HIV DNA below 100 copies/106 PBMC (p=0.0022, Fisher’s exact test). These findings indicate that recovery of replication-competent virus by QVOA is more likely in individuals with higher levels of intact HIV DNA in IPDA, reaffirming a link between the two measurements.”

(2) "To determine whether early HIV-specific CD8+ T-cell responses at 24 weeks were predictive for the change in reservoir size". This is a fundamental miss on correlation vs causation... it could be the inverse. 

We thank the reviewer for the remark. We have calculated the change in reservoir size (the difference between the reservoir size at 24 weeks and 156 weeks ART) and analyzed if the HIVspecific CD8+ T-cell response at 24 weeks ART are predictive for this change. We do not think it can be inverse, as we have a chronological relationship (CD8+ responses at week 24 predict the subsequent change in the reservoir).

(3) "This may suggest that active viral replication drives the CD8+ T-cell response." I think to be precise, you mean viral transcription drives CD8s, we don't know about the full replication cycle from these data. 

We agree with the reviewer and have changed “replication” to “transcription” (line 280).

(4) "Remarkably, we observed that the defective HIV DNA levels declined significantly between 24 weeks and 3 years on ART. This is in contrast to previous observations in chronic HIV infection (30)". I don't find this remarkable or in contrast: many studies have analyzed and/or modeled defective HIV DNA decay, most of which have shown some negative slope to defective HIV DNA, especially within the first year of ART. See White et al., Blankson et al., Golob et al., Besson et al., etc In addition, do you mean in long-term suppressed? 

The point we would like to make is that,  compared to other studies, we found a significant, prominent decrease in defective DNA (and not intact DNA) over the course of 3 years, which is in contrast to other studies (where usually the decrease in intact is significant and the decrease in defective less prominent). We have rephrased the wording (lines 227-230) as follows:

“We observed that the defective HIV DNA levels decreased significantly between 24 and 156 weeks of ART. This is different from studies in CHI, where no significant decrease during the first 7 years of ART (Peluso, Bacchetti et al. 2020, Gandhi, Cyktor et al. 2021), or only a significant decrease during the first 8 weeks on ART, but not in the 8 years thereafter, was observed (Nühn, Bosman et al. 2025).”

Reviewer #2 (Recommendations for the authors): 

(1) Page 4, paragraph 2 - will be informative to report the statistics here. 

(2) Page 4, paragraph 4 - "General phenotyping of CD4+ (Suppl. Fig. 3A) and CD8+ (Supplementary Figure 3B) T-cells showed no difference in frequencies of naïve, memory or effector CD8+ T-cells between 24 and 156 weeks." - What did the CD4+ phenotyping show? 

We thank the reviewer for the remark. Indeed, there were also no differences in frequencies of naïve, memory or effector CD4+ T-cells between 24 and 156 weeks. We have added this to the paragraph (now Suppl. Fig 4), lines 166-168.

(3) Page 5, paragraph 3 - "Similarly, a broad HIV-specific CD8+ T-cell proliferative response to at least three different viral proteins was observed in the majority of individuals at both time points" - should specify n=? for the majority of individuals. 

At time point 24 weeks, 6/11 individuals had a response to env, 10/11 to gag, 5/11 to nef, and 4/11 to pol. At 156 weeks, 8/11 to env, 10/11 to gag, 8/11 to nef and 9/11 to pol. We have added this to the text (lines 188-191).

(4) Seven of 22 participants had non-subtype B infection. Can the authors explain the use of the IPDA designed by Bruner et. al. for subtype B HIV, and how this may have affected the quantification in these participants? 

Intact HIV DNA was detectable in all 22 participants. We cannot completely exclude influence of primer/probe-template mismatches on the quantification results, however such mismatches could also have occurred in subtype B participants, and droplet digital PCR that IPDA is based on is generally much less sensitive to these mismatches than qPCR.

(5) Page 7, paragraph 2 - the authors report a difference in findings from a previous study ("a decline in CD8 T cell responses over 2 years" - reference 21), but only provide an explanation for this on page 9. The authors should consider moving the explanation to this paragraph for easier understanding. 

We agree with the reviewer that this causes confusion. Therefore, we have revised and changed the order in the Discussion.

(6) Page 7, paragraph 2 - Following from above, the previous study (21) reported this contradicting finding "a decline in CD8 T cell responses over 2 years" in a CHI (chronic HIV) treated cohort. The current study was in an acute HIV treated cohort. The authors should explain whether this may also have resulted in the different findings, in addition to the use of different readouts in each study.

We thank the reviewer for this attentiveness. Indeed, the study by Takata et al. investigates the reservoir and HIV-specific CD8+ T-cell responses in both the RV254/ SEARCH010 study who initiated ART during AHI and the RV304/ SEARCH013 who initiated ART during CHI. We had not realized that the findings of the decline in CD8 T cell responses were solely found in the RV304/ SEARCH013 (CHI cohort). It appears functional HIV specific immune responses were only measured in AHI at 96 weeks, so we have clarified this in the Discussion. 

Besson, G. J., C. M. Lalama, R. J. Bosch, R. T. Gandhi, M. A. Bedison, E. Aga, S. A. Riddler, D. K. McMahon, F. Hong and J. W. Mellors (2014). "HIV-1 DNA decay dynamics in blood during more than a decade of suppressive antiretroviral therapy." Clin Infect Dis 59(9): 1312-1321.

Gandhi, R. T., J. C. Cyktor, R. J. Bosch, H. Mar, G. M. Laird, A. Martin, A. C. Collier, S. A. Riddler, B. J. Macatangay, C. R. Rinaldo, J. J. Eron, J. D. Siliciano, D. K. McMahon and J. W. Mellors (2021). "Selective Decay of Intact HIV-1 Proviral DNA on Antiretroviral Therapy." J Infect Dis 223(2): 225-233.

Gandhi, R. T., D. K. McMahon, R. J. Bosch, C. M. Lalama, J. C. Cyktor, B. J. Macatangay, C. R. Rinaldo, S. A. Riddler, E. Hogg, C. Godfrey, A. C. Collier, J. J. Eron and J. W. Mellors (2017). "Levels of HIV-1 persistence on antiretroviral therapy are not associated with markers of inflammation or activation." PLoS Pathog 13(4): e1006285.

Nühn, M. M., K. Bosman, T. Huisman, W. H. A. Staring, L. Gharu, D. De Jong, T. M. De Kort, N. Buchholtz, K. Tesselaar, A. Pandit, J. Arends, S. A. Otto, E. Lucio De Esesarte, A. I. M. Hoepelman, R. J. De Boer, J. Symons, J. A. M. Borghans, A. M. J. Wensing and M. Nijhuis (2025). "Selective decline of intact HIV reservoirs during the first decade of ART followed by stabilization in memory T cell subsets." Aids 39(7): 798-811.

Peluso, M. J., P. Bacchetti, K. D. Ritter, S. Beg, J. Lai, J. N. Martin, P. W. Hunt, T. J. Henrich, J. D. Siliciano, R. F. Siliciano, G. M. Laird and S. G. Deeks (2020). "Differential decay of intact and defective proviral DNA in HIV-1-infected individuals on suppressive antiretroviral therapy." JCI Insight 5(4).

eLife Assessment

This manuscript provides evidence that mouse germline cysts develop an asymmetric Golgi, ER, and microtubule-associated structure, referred to as Visham, which in many ways resembles the fusome of Drosophila germline cysts. This is an important study that provides new evidence that fusome-like structures exist in germ cell cysts across species. While most of the data are solid, several instances remain in which conclusions regarding the dynamics and function of Visham should be restated, or additional experimental evidence should be provided to more fully support the authors' interpretations.

Reviewer #1 (Public review):

Summary:

The authors attempt to study how oocyte incomplete cytokinesis occurs in the mouse ovary.

Strengths:

The finding that UPR components are highly expressed during zygotene is an interesting result that has broad implications for how germ cells navigate meiosis. The findings that proteasome activity increases in germ cells compared to somatic cells suggest that the germline might have a quantitatively different response for protein clearance.

Weaknesses:

(1) The microscopy images look saturated, for example, Figure 1a, b, etc? Is this a normal way to present fluorescent microscopy?

(2) The authors should ensure that all claims regarding enrichment/lower vs lower values have indicated statistical tests.

(a) In Figure 2f, the authors should indicate which comparison is made for this test. Is it comparing 2 vs 6 cyst numbers?

(b) Figures 4d and 4e do not have a statistical test indicated.

(3) Because the system is developmentally dynamic, the major conclusions of the work are somewhat unclear. Could the authors be more explicit about these and enumerate them more clearly in the abstract?

(4) The references for specific prior literature are mostly missing (lines 184-195, for example).

(5) The authors should define all acronyms when they are first used in the text (UPR, EGAD, etc).

(6) The jumping between topics (EMA, into microtubule fragmentation, polarization proteins, UPR/ERAD/EGAD, GCNA, ER, balbiani body, etc) makes the narrative of the paper very difficult to follow.

(7) The heading title "Visham participates in organelle rejuvenation during meiosis" in line 241 is speculative and/or not supported. Drawing upon the extensive, highly rigorous Drosophila literature, it is safe to extrapolate, but the claim about regeneration is not adequately supported.

Reviewer #2 (Public review):

This study identifies Visham, an asymmetric structure in developing mouse cysts resembling the Drosophila fusome, an organelle crucial for oocyte determination. Using immunofluorescence, electron microscopy, 3D reconstruction, and lineage labeling, the authors show that primordial germ cells (PGCs) and cysts, but not somatic cells, contain an EMA-rich, branching structure that they named Visham, which remains unbranched in male cysts. Visham accumulates in regions enriched in intercellular bridges, forming clusters reminiscent of fusome "rosettes." It is enriched in Golgi and endosomal vesicles and partially overlaps with the ER. During cell division, Visham localizes near centrosomes in interphase and early metaphase, disperses during metaphase, and reassembles at spindle poles during telophase before becoming asymmetric. Microtubule depolymerization disrupts its formation.

Cyst fragmentation is shown to be non-random, correlating with microtubule gaps. The authors propose that 8-cell (or larger) cysts fragment into 6-cell and 2-cell cysts. Analysis of Pard3 (the mouse ortholog of Par3/Baz) reveals its colocalization with Visham during cyst asymmetry, suggesting that mammalian oocyte polarization depends on a conserved system involving Par genes, cyst formation, and a fusome-like structure.

Transcriptomic profiling identifies genes linked to pluripotency and the unfolded protein response (UPR) during cyst formation and meiosis, supported by protein-level reporters monitoring Xbp1 splicing and 20S proteasome activity. Visham persists in meiotic germ cells at stage E17.5 and is later transferred to the oocyte at E18.5 along with mitochondria and Golgi vesicles, implicating it in organelle rejuvenation. In Dazl mutants, cysts form, but Visham dynamics, polarity, rejuvenation, and oocyte production are disrupted, highlighting its potential role in germ cell development.

Overall, this is an interesting and comprehensive study of a conserved structure in the germline cells of both invertebrate and vertebrate species. Investigating these early stages of germ cell development in mice is particularly challenging. Although primarily descriptive, the study represents a remarkable technical achievement. The images are generally convincing, with only a few exceptions.

Major comments:

(1) Some titles contain strong terms that do not fully match the conclusions of the corresponding sections.

(1a) Article title "Mouse germline cysts contain a fusome-like structure that mediates oocyte development":

The term "mediates" could be misleading, as the functional data on Visham (based on comparing its absence to wild-type) actually reflects either a microtubule defect or a Dazl mutant context. There is no specific loss-of-function of visham only.

(1b) Result title, "Visham overlaps centrosomes and moves on microtubules":

The term "moves" implies dynamic behavior, which would require live imaging data that are not described in the article.

(1c) Result title, "Visham associates with Golgi genes involved in UPR beginning at the onset of cyst formation":

The presented data show that the presence of Visham in the cyst coincides temporally with the expression and activity of the UPR response; the term "associates" is unclear in this context.

(1d) Result title, "Visham participates in organelle rejuvenation during meiosis":

The term "participates" suggests that Visham is required for this process, whereas the conclusion is actually drawn from the Dazl mutant context, not a specific loss-of-function of visham only.

(2) The authors aim to demonstrate that Visham is a fusome-like structure. I would suggest simply referring to it as a "fusome-like structure" rather than introducing a new term, which may confuse readers and does not necessarily help the authors' goal of showing the conservation of this structure in Drosophila and Xenopus germ cells. Interestingly, in a preprint from the same laboratory describing a similar structure in Xenopus germ cells, the authors refer to it as a "fusome-like structure (FLS)" (Davidian and Spradling, BioRxiv, 2025).

Reviewer #3 (Public review):

This manuscript provides evidence that mice have a fusome, a conserved structure most well studied in Drosophila that is important for oocyte specification. Overall, a myriad of evidence is presented demonstrating the existence of a mouse fusome that the authors term visham. This work is important as it addresses a long-standing question in the field of whether mice have fusomes and sheds light on how oocytes are specified in mammals. Concerns that need to be addressed revolve around several conclusions that are overstated or unclear and are listed below.

(1) Line 86 - the heading for this section is "PGCs contain a Golgi-rich structure known as the EMA granule" but there is nothing in this section that shows it is Golgi-rich. It does show that the structure is asymmetric and has branches.

(2) Line 105-106, how do we know if what's seen by EM corresponds to the EMA1 granule?

(3) Line 106-107-states "Visham co-stained with the Golgi protein Gm130 and the recycling endosomal protein Rab11a1". This is not convincing as there is only one example of each image, and both appear to be distorted.

(4) Line 132-133---while visham formation is disrupted when microtubules are disrupted, I am not convinced that visham moves on microtubules as stated in the heading of this section.

(5) Line 156 - the heading for this section states that Visham associates with polarity and microtubule genes, including pard3, but only evidence for pard3 is presented.

(6) Lines 196-210 - it's strange to say that UPR genes depend on DAZ, as they are upregulated in the mutants. I think there are important observations here, but it's unclear what is being concluded.

(7) Line 257-259---wave 1 and 2 follicles need to be explained in the introduction, and how this fits with the observations here clarified.

Author response:

Reviewer #1 (Public Review):

Summary

We thank the reviewer for the constructive and thoughtful evaluation of our work. We appreciate the recognition of the novelty and potential implications of our findings regarding UPR activation and proteasome activity in germ cells.

(1) The microscopy images look saturated, for example, Figure 1a, b, etc. Is this a normal way to present fluorescent microscopy?

The apparent saturation was not present in the original images, but likely arose from image compression during PDF generation. While the EMA granule was still apparent, in the revised submission, we will provide high-resolution TIFF files to ensure accurate representation of fluorescence intensity and will carefully optimize image display settings to avoid any saturation artifacts.

(2) The authors should ensure that all claims regarding enrichment/lower vs. lower values have indicated statistical tests.

We fully agree. In the revised version, we will correct any quantitative comparisons where statistical tests were not already indicated, with a clear statement of the statistical tests used, including p-values in figure legends and text.

(a) In Figure 2f, the authors should indicate which comparison is made for this test. Is it comparing 2 vs. 6 cyst numbers?

We acknowledge that the description was not sufficiently detailed. Indeed, the test was not between 2 vs 6 cyst numbers, but between all possible ways 8-cell cysts or the larger cysts studied could fragment randomly into two pieces, and produce by chance 6-cell cysts in 13 of 15 observed examples. We will expand the legend and main text to clarify that a binomial test was used to determine that the proportion of cysts producing 6-cell fragments differed very significantly from chance.

Revised text:

“A binomial test was used to assess whether the observed frequency of 6-cell cyst products differed from random cyst breakage. Production of 6-cell cysts was strongly preferred (13/15 cysts; ****p < 0.0001).”

(b) Figures 4d and 4e do not have a statistical test indicated.

We will include the specific statistical test used and report the corresponding p-values directly in the figure legends.

(3) Because the system is developmentally dynamic, the major conclusions of the work are somewhat unclear. Could the authors be more explicit about these and enumerate them more clearly in the abstract?

We will revise the abstract to better clarify the findings of this study. We will also replace the term Visham with mouse fusome to reflect its functional and structural analogy to the Drosophila and Xenopus fusomes, making the narrative more coherent and conclusive.

(4) The references for specific prior literature are mostly missing (lines 184-195, for example).

We appreciate this observation of a problem that occurred inadvertently when shortening an earlier version.  We will add 3–4 relevant references to appropriately support this section.

(5) The authors should define all acronyms when they are first used in the text (UPR, EGAD, etc).

We will ensure that all acronyms are spelled out at first mention (e.g., Unfolded Protein Response (UPR), Endosome and Golgi-Associated Degradation (EGAD)).

(6)  The jumping between topics (EMA, into microtubule fragmentation, polarization proteins, UPR/ERAD/EGAD, GCNA, ER, balbiani body, etc) makes the narrative of the paper very difficult to follow.

We are not jumping between topics, but following a narrative relevant to the central question of whether female mouse germ cells develop using a fusome.  EMA, microtubule fragmentation, polarization proteins, ER, and balbiani body are all topics with a known connection to fusomes. This is explained in the general introduction and in relevant subsections. We appreciate this feedback that further explanations of these connections would be helpful. In the revised manuscript, use of the unified term mouse fusome will also help connect the narrative across sections.  UPR/ERAD/EGAD are processes that have been studied in repair and maintenance of somatic cells and in yeast meiosis.  We show that the major regulator XbpI is found in the fusome, and that the fusome and these rejuvenation pathway genes are expressed and maintained throughout oogenesis, rather than only during limited late stages as suggested in previous literature.

(7) The heading title "Visham participates in organelle rejuvenation during meiosis" in line 241 is speculative and/or not supported. Drawing upon the extensive, highly rigorous Drosophila literature, it is safe to extrapolate, but the claim about regeneration is not adequately supported.

We believe this statement is accurate given the broad scope of the term "participates." It is supported by localization of the UPR regulator XbpI to the fusome. XbpI is the ortholog of HacI a key gene mediating UPR-mediated rejuvenation during yeast meiosis.  We also showed that rejuvenation pathway genes are expressed throughout most of meiosis (not previously known) and expanded cytological evidence of stage-specific organelle rejuvenation later in meiosis, such as mitochondrial-ER docking, in regions enriched in fusome antigens. However, we recognize the current limitations of this evidence in the mouse, and want to appropriately convey this, without going to what we believe would be an unjustified extreme of saying there is no evidence. 

Reviewer #2 (Public Review):

We thank the reviewer for the comprehensive summary and for highlighting both the technical achievement and biological relevance of our study. We greatly appreciate the thoughtful suggestions that have helped us refine our presentation and terminology.

(1) Some titles contain strong terms that do not fully match the conclusions of the corresponding sections.

(1a) Article title “Mouse germline cysts contain a fusome-like structure that mediates oocyte development”

We will change the statement to: “Mouse germline cysts contain a fusome that supports germline cyst polarity and rejuvenation.”

(1b) Result title “Visham overlaps centrosomes and moves on microtubules” We acknowledge that “moves” implies dynamics. We will include additional supplementary images showing small vesicular components of the mouse fusome on spindle-derived microtubule tracks.

(1c) Result title “Visham associates with Golgi genes involved in UPR beginning at the onset of cyst formation”

We will revise this title to: “The mouse fusome associates with the UPR regulatory protein Xbp1 beginning at the onset of cyst formation” to reflect the specific UPR protein that was immunolocalized. 

(1d) Result title “Visham participates in organelle rejuvenation during meiosis”

We will revise this to: “The mouse fusome persists during organelle rejuvenation in meiosis.”

(2) The authors aim to demonstrate that Visham is a fusome-like structure. I would suggest simply referring to it as a "fusome-like structure" rather than introducing a new term, which may confuse readers and does not necessarily help the authors' goal of showing the conservation of this structure in Drosophila and Xenopus germ cells. Interestingly, in a preprint from the same laboratory describing a similar structure in Xenopus germ cells, the authors refer to it as a "fusome-like structure (FLS)" (Davidian and Spradling, BioRxiv, 2025).

We appreciate the reviewer’s insightful comment. To maintain conceptual clarity and align with existing literature, we will refer to the structure as the mouse fusome throughout the manuscript, avoiding introduction of a new term.

Reviewer #3 (Public Review):

We thank the reviewer for emphasizing the importance of our study and for providing constructive feedback that will help us clarify and strengthen our conclusions.

(1) Line 86 - the heading for this section is "PGCs contain a Golgi-rich structure known as the EMA granule" 

We agree that the enrichment of Golgi within the EMA PGCs was not shown until the next section. We will revise this heading to:

“PGCs contain an asymmetric EMA granule.”

(2)  Line 105-106, how do we know if what's seen by EM corresponds to the EMA1 granule?

We will clarify that this identification is based on co-localization with Golgi markers (GM130 and GS28) and response to Brefeldin A treatment, which will be included as supplementary data. These findings support that the mouse fusome is Golgi-derived and can therefore be visualized by EM. The Golgi regions in E13.5 cyst cells move close together and associate with ring canals as visualized by EM (Figure 1E), the same as the mouse fusomes identified by EMA.

(3) Line 106-107-states "Visham co-stained with the Golgi protein Gm130 and the recycling endosomal protein Rab11a1". This is not convincing as there is only one example of each image, and both appear to be distorted.

Space is at a premium in these figures, but we have no limitation on data documenting this absolutely clear co-localization. We will replace the existing images with high-resolution, non-compressed versions for the final figures to clearly illustrate the co-staining patterns for GM130 and Rab11a1.

(4) Line 132-133---while visham formation is disrupted when microtubules are disrupted, I am not convinced that visham moves on microtubules as stated in the heading of this section.

We will include additional supplementary data showing small mouse fusome vesicles aligned along microtubules.

(5) Line 156 - the heading for this section states that Visham associates with polarity and microtubule genes, including pard3, but only evidence for pard3 is presented.

We agree and will revise the heading to: “Mouse fusome associates with the polarity protein Pard3.” We are adding data showing association of small fusome vesicles on microtubules.  

(6)  Lines 196-210 - it's strange to say that UPR genes depend on DAZ, as they are upregulated in the mutants. I think there are important observations here, but it's unclear what is being concluded.

UPR genes are not upregulated in DAZ in the sense we have never documented them increasing. We show that UPR genes during this time behave like pleuripotency genes and normally decline, but in DAZ mutants their decline is slowed.  We will rephrase the paragraph to clarify that Dazl mutation partially decouples developmental processes that are normally linked, which alters UPR gene expression relative to cyst development.

(7) Line 257-259-wave 1 and 2 follicles need to be explained in the introduction, and how these fits with the observations here clarified.

Follicle waves are too small a focus of the current study to explain in the introduction, but we will request readers to refer to the cited relevant literature (Yin and Spradling, 2025) for further details.

We sincerely thank all reviewers for their insightful and constructive feedback. We believe that the planned revisions—particularly the refined terminology, improved image quality, clarified statistics, and restructured abstract—will substantially strengthen the manuscript and enhance clarity for readers.

eLife Assessment

The authors combine experiments and mathematical modeling to determine how the infectivity of human cytomegalovirus scales with the viral concentration in the inoculum, i.e., considering the multiplicity of infection (MOI). They propose and test different model assumptions to explain a mechanism termed "apparent cooperativity" of virions based on an observed super-linear increase in the number of infected cells with increasing inocula. The authors present a solid study showing valuable findings for virologists and quantitative scientists working on the analysis and interpretation of viral infection dynamics. Some of the presented aspects would benefit from additional clarification.

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of the virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to doubling the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration), infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and constructed mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but they can't be conclusive as to what the correct explanation is. In any case, this advances our knowledge of the system, and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

There are minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have a substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

Suggestions to clarify the study:

(1) Mathematically, it is clear what "increase linearly" or "increase faster than linearly" (e.g., line 94) means. However, it may be confusing for some readers to then look at plots such as in Figure 2, which appear linear (but on the log-log scale) and about which the authors also say (line 326) "data best matching the linear relationship on a log-log scale".

(2) One of the main issues that is unclear to me is whether the authors assume that cell infection is independent of other cells. This could be a very important issue affecting their results, both when analyzing the experimental data and running the simulations. One possible outcome of infection could be the generation of innate mediators that could protect (alter the resistance) of nearby cells. I can imagine two opposite results of this: i) one possibility is that resistance would lead to lower infection frequencies and this would result in apparent sub-linear infection (contrary to the observations); or ii) inoculums with more virus lead to faster infection, which doesn't allow enough time for the "resistance" (innate effect) to spread (potentially leading to results similar to the observations, supra-linear infection).

(3) Another unclear aspect of cell infection is whether each cell only has one chance to be infected or multiple chances, i.e., do the authors run the simulation once over all the cells or more times?

(4) On the other hand, the authors address the complementary issue of the virus acting independently or not, with their clumping model (which includes nice experimental measurements). However, it was unclear to me what the assumption of the simulation is in this case. In the case of infection by a clump of virus or "viral compensation", when infection is successful (the cell becomes infected), how many viruses "disappear" and what happens to the rest? For example, one of the viruses of the clump is removed by infection, but the others are free to participate in another clump, or they also disappear. The only thing I found about this is the caption of Figure S10, and it seems to indicate that only the infected virus is removed. However, a typical assumption, I think, is that viruses aggregate to improve infection, but then the whole aggregate participates in infection of a single cell, and those viruses in the clump can't participate in other infections. Viral cooperativity with higher inocula in this case would be, perhaps, the result of larger numbers of clumps for higher inocula. This seems in agreement with Figure S8, but was a little unclear in the interpretation provided.

(5) In algorithm 1, how does P_i, as defined, relate to equation 1?

(6) In line 228, and several other places (e.g., caption of Table S2), the authors refer to the probability of a single genome infecting a cell p(1)=exp(-lambda), but shouldn't it be p(1)=1-exp(-lambda) according to equation 1?

(7) In line 304, the accrued damage hypothesis is defined, but it is stated as a triggering of an antiviral response; one would assume that exposure to a virion should increase the resistance to infection. Otherwise, the authors are saying that evolution has come up with intracellular viral resistance mechanisms that are detrimental to the cell. As I mentioned above, this could also be a mechanism for non-independent cell infection. For example, infected cells signal to neighboring cells to "become resistance" to infection. This would also provide a mechanism for saturation at high levels.

(8) In Figure 3, and likely other places, t-tests are used for comparisons, but with only an n=5 (experiments). Many would prefer a non-parametric test.

Reviewer #2 (Public review):

In their article, Peterson et al. wanted to show to what extent the classical "single hit" model of virion infection, where one virion is required to infect a cell, does not match empirical observations based on human cytomegalovirus in vitro infection model, and how this would have practical impacts in experimental protocols.

They first used a very simple experimental assay, where they infected cells with serially diluted virions and measured the proportion of infected cells with flow cytometry. From this, they could elegantly show how the proportion of infected cells differed from a "single hit" model, which they simulated using a simple mathematical model ("powerlaw model"), and better fit a model where virions need to cooperate to infect cells. They then explore which mechanism could explain this apparent cooperation:

(1) Stochasticity alone cannot explain the results, although I am unsure how generalizable the results are, because the mathematical model chosen cannot, by design, explain such observations only by stochasticity.

(2) Virion clumping seemed not to be enough either to generally explain such a pattern. For that, they first use a mathematical model showing that the apparent cooperation would be small. However, I am unsure how extreme the scenario of simulated virion clumping is. They then used dynamic light scattering to measure the distribution of the sizes of clumps. From these estimates, they show that virion clumps cannot reproduce the observed virion cooperation in serial dilution assays. However, the authors remain unprecise on how the uncertainty of these clumps' size distribution would impact the results, as most clumps have a size smaller than a single virion, leaving therefore a limited number of clumps truly containing virions.

The two models remain unidentifiable from each other but could explain the apparent virion cooperativity: either due to an increase in susceptibility of the cell each time a virion tries to infect it, or due to viral compensation, where lesser fit viruses are able to infect cells in co-infection with a better fit virion. Unfortunately, the authors here do not attempt to fit their mathematical model to the experimental data but only show that theoretical models and experimental data generate similar patterns regarding virion apparent cooperation.

Finally, the authors show that this virions cooperation could make the relationship between the estimated multiplicity of infection and viruses/cell deviate from the 1:1 relationship. Consequently, the dilution of a virion stock would lead to an even stronger decrease in infectivity, as more diluted virions can cooperate less for infection.

Overall, this work is very valuable as it raises the general question of how the estimate of infectivity can be biased if extrapolated from a single virus titer assay. The observation that HCMV virions often cooperate and that this cooperation varies between contexts seems robust. The putative biological explanations would require further exploration.

This topic is very well known in the case of segmented viruses and the semi-infectious particles, leading to the idea of studying "sociovirology", but to my knowledge, this is the first time that it was explored for a nonsegmented virus, and in the context of MOI estimation.

Reviewer #3 (Public review):

Summary:

The authors dilute fluorescent HCMV stocks in small steps (df ≈ 1.3-1.5) across 23 points, quantify infections by flow cytometry at 3 dpi, and fit a power-law model to estimate a cooperativity parameter n (n > 1 indicates apparent cooperativity). They compare fibroblasts vs epithelial cells and multiple strains/reporters, and explore alternative mechanisms (clumping, accrued damage, viral compensation) via analytical modeling and stochastic simulations. They discuss implications for titer/MOI estimation and suggest a method for detecting "apparent cooperativity," noting that for viruses showing this behavior, MOI estimation may be biased.

Strengths:

(1) High-resolution titration & rigor: The small-step dilution design (23 serial dilutions; tailored df) improves dose-response resolution beyond conventional 10× series.

(2) Clear quantitative signal: Multiple strain-cell pairs show n > 1, with appropriate model fitting and visualization of the linear regime on log-log axes.

(3) Mechanistic exploration: Side-by-side modeling of clumping vs accrued damage vs compensation frames testable hypotheses for cooperativity.

Weaknesses:

(1) Secondary infection control: The authors argue that 3 dpi largely avoids progeny-mediated secondary infection; this claim should be strengthened (e.g., entry inhibitors/control infections) or add sensitivity checks showing results are robust to a small secondary-infection contribution.

(2) Discriminating mechanisms: At present, simulations cannot distinguish between accrued damage and viral compensation. The authors should propose or add a decisive experiment (e.g., dual-color coinfection to quantify true coinfection rates versus "priming" without coinfection; timed sequential inocula) and outline expected signatures for each mechanism.

(3) Decline at high genomes/cell: Several datasets show a downturn at high input. Hypotheses should be provided (cytotoxicity, receptor depletion, and measurement ceiling) and any supportive controls.

(4) Include experimental data: In Figure 6, please include the experimentally measured titers (IU/mL), if available.

(5) MOI guidance: The practical guidance is important; please add a short "best-practice box" (how to determine titer at multiple genomes/cell and cell densities; when single-hit assumptions fail) for end-users.

Author response:

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of the virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to doubling the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration), infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and constructed mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but they can't be conclusive as to what the correct explanation is. In any case, this advances our knowledge of the system, and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

There are minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have a substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

Suggestions to clarify the study:

(1) Mathematically, it is clear what "increase linearly" or "increase faster than linearly" (e.g., line 94) means. However, it may be confusing for some readers to then look at plots such as in Figure 2, which appear linear (but on the log-log scale) and about which the authors also say (line 326) "data best matching the linear relationship on a log-log scale". 

This is a good point. In our revision, we will include a clarification to indicate that linear on the log-log scale relationship does not imply linear relationship on the linear-linear scale.

(2) One of the main issues that is unclear to me is whether the authors assume that cell infection is independent of other cells. This could be a very important issue affecting their results, both when analyzing the experimental data and running the simulations. One possible outcome of infection could be the generation of innate mediators that could protect (alter the resistance) of nearby cells. I can imagine two opposite results of this: i) one possibility is that resistance would lead to lower infection frequencies and this would result in apparent sub-linear infection (contrary to the observations); or ii) inoculums with more virus lead to faster infection, which doesn't allow enough time for the "resistance" (innate effect) to spread (potentially leading to results similar to the observations, supra-linear infection). 

In our models we assumed cells to be independent of each other (see also responses to other similar points). Because we measure infection in individual cells, assuming cells are independent is a reasonable first approximation. However, the reviewer makes an excellent point that there may be some between-cell signaling happening in the culture that “alerts” or “conditions” cells to change their “resistance”. It is also possible that at higher genome/cell numbers, exposure of cells to virions or virion debris may change the state of cells in the culture, and more cells become “susceptible” to infection. This is a good point that we will list in Limitations subsection of Discussion; it is a good hypothesis to test in our future experiments.

(3) Another unclear aspect of cell infection is whether each cell only has one chance to be infected or multiple chances, i.e., do the authors run the simulation once over all the cells or more times? 

Each cell has only one chance to be infected. Algorithm 1 clearly states that; we will add an extra sentence in “Agent-based simulations” to indicate this point.

(4) On the other hand, the authors address the complementary issue of the virus acting independently or not, with their clumping model (which includes nice experimental measurements). However, it was unclear to me what the assumption of the simulation is in this case. In the case of infection by a clump of virus or "viral compensation", when infection is successful (the cell becomes infected), how many viruses "disappear" and what happens to the rest? For example, one of the viruses of the clump is removed by infection, but the others are free to participate in another clump, or they also disappear. The only thing I found about this is the caption of Figure S10, and it seems to indicate that only the infected virus is removed. However, a typical assumption, I think, is that viruses aggregate to improve infection, but then the whole aggregate participates in infection of a single cell, and those viruses in the clump can't participate in other infections. Viral cooperativity with higher inocula in this case would be, perhaps, the result of larger numbers of clumps for higher inocula. This seems in agreement with Figure S8, but was a little unclear in the interpretation provided. 

This is a good point. We did not remove the clump if one of the virions in the clump manages to infect a cell, and indeed, this could be the reason why in some simulations we observe apparent cooperativity when modeling viral clumping. This is something we will explore in our revision.

(5) In algorithm 1, how does P_i, as defined, relate to equation 1? 

These are unrelated because eqn.(1) is a phenomenological model that links infection per cell to genomes per cell. P_i in algorithm 1 is “physics-inspired” potential barrier.

(6) In line 228, and several other places (e.g., caption of Table S2), the authors refer to the probability of a single genome infecting a cell p(1)=exp(-lambda), but shouldn't it be p(1)=1-exp(-lambda) according to equation 1?

Indeed, it was a typo, p(1)=1-exp(-lambda) per eqn 1. Thank you, it will be corrected in the revised paper.

(7) In line 304, the accrued damage hypothesis is defined, but it is stated as a triggering of an antiviral response; one would assume that exposure to a virion should increase the resistance to infection. Otherwise, the authors are saying that evolution has come up with intracellular viral resistance mechanisms that are detrimental to the cell. As I mentioned above, this could also be a mechanism for non-independent cell infection. For example, infected cells signal to neighboring cells to "become resistance" to infection. This would also provide a mechanism for saturation at high levels. 

We do not know how exposure of a cell to one virion would change its “antiviral state”, i.e., to become more or less resistant to the next infection. If a cell becomes more resistant, there is no possibility to observe apparent cooperativity in infection of cells, so this hypothesis cannot explain our observations with n>1. Whether this mechanism plays a role in saturation of cell infection rate at lower than 1 value when genome/cell is large is unclear but is a possibility. We will add this point to Discussion in revision.

(8) In Figure 3, and likely other places, t-tests are used for comparisons, but with only an n=5 (experiments). Many would prefer a non-parametric test. 

We repeated the analyses in Fig 3 with Mann-Whitney test, results were the same, so we would like to keep results from the t-test in the paper.

Reviewer #2 (Public review):

In their article, Peterson et al. wanted to show to what extent the classical "single hit" model of virion infection, where one virion is required to infect a cell, does not match empirical observations based on human cytomegalovirus in vitro infection model, and how this would have practical impacts in experimental protocols.

They first used a very simple experimental assay, where they infected cells with serially diluted virions and measured the proportion of infected cells with flow cytometry. From this, they could elegantly show how the proportion of infected cells differed from a "single hit" model, which they simulated using a simple mathematical model ("powerlaw model"), and better fit a model where virions need to cooperate to infect cells. They then explore which mechanism could explain this apparent cooperation:

(1) Stochasticity alone cannot explain the results, although I am unsure how generalizable the results are, because the mathematical model chosen cannot, by design, explain such observations only by stochasticity. 

Our null model simulations are not just about stochasticity; they also include variability in virion infectivity and cell resistance to infection. We agree that simulations cannot truly prove that such variability cannot result in apparent cooperativity; however, we also provide a mathematical proof that increase in frequency of infected cells should be linear with virion concentration at small genome/cell numbers.

(2) Virion clumping seemed not to be enough either to generally explain such a pattern. For that, they first use a mathematical model showing that the apparent cooperation would be small. However, I am unsure how extreme the scenario of simulated virion clumping is. They then used dynamic light scattering to measure the distribution of the sizes of clumps. From these estimates, they show that virion clumps cannot reproduce the observed virion cooperation in serial dilution assays. However, the authors remain unprecise on how the uncertainty of these clumps' size distribution would impact the results, as most clumps have a size smaller than a single virion, leaving therefore a limited number of clumps truly containing virions. 

As we stated in the paper, clumping may explain apparent cooperativity in simulations depending on how stock dilution impacts distribution of virions/clump. This could be explored further, however, better experimental measurements of virions/clump would be highly informative (but we do not have resources to do these experiments at present). Our point is that the degree of apparent cooperativity is dependent on the target cell used (n is smaller on epithelial cells than on fibroblasts) that is difficult to explain by clumping which is a virion property. Per comment by reviewer 1, we will do some more analyses of the clumping model to investigate importance of clump removal per successful infection on the detected degree of apparent cooperativity.

The two models remain unidentifiable from each other but could explain the apparent virion cooperativity: either due to an increase in susceptibility of the cell each time a virion tries to infect it, or due to viral compensation, where lesser fit viruses are able to infect cells in co-infection with a better fit virion. Unfortunately, the authors here do not attempt to fit their mathematical model to the experimental data but only show that theoretical models and experimental data generate similar patterns regarding virion apparent cooperation. 

In the revision we will provide examples of simulations that “match” experimental data with a relatively high degree of apparent cooperativity; we have done those before but excluded them from the current version since they are a bit messy. Fitting simulations to data may be an overkill.

Finally, the authors show that this virions cooperation could make the relationship between the estimated multiplicity of infection and viruses/cell deviate from the 1:1 relationship. Consequently, the dilution of a virion stock would lead to an even stronger decrease in infectivity, as more diluted virions can cooperate less for infection.

Overall, this work is very valuable as it raises the general question of how the estimate of infectivity can be biased if extrapolated from a single virus titer assay. The observation that HCMV virions often cooperate and that this cooperation varies between contexts seems robust. The putative biological explanations would require further exploration.

This topic is very well known in the case of segmented viruses and the semi-infectious particles, leading to the idea of studying "sociovirology", but to my knowledge, this is the first time that it was explored for a nonsegmented virus, and in the context of MOI estimation. 

Thank you.

Reviewer #3 (Public review): 

Summary:

The authors dilute fluorescent HCMV stocks in small steps (df ≈ 1.3-1.5) across 23 points, quantify infections by flow cytometry at 3 dpi, and fit a power-law model to estimate a cooperativity parameter n (n > 1 indicates apparent cooperativity). They compare fibroblasts vs epithelial cells and multiple strains/reporters, and explore alternative mechanisms (clumping, accrued damage, viral compensation) via analytical modeling and stochastic simulations. They discuss implications for titer/MOI estimation and suggest a method for detecting "apparent cooperativity," noting that for viruses showing this behavior, MOI estimation may be biased.

Strengths:

(1) High-resolution titration & rigor: The small-step dilution design (23 serial dilutions; tailored df) improves dose-response resolution beyond conventional 10× series.

(2) Clear quantitative signal: Multiple strain-cell pairs show n > 1, with appropriate model fitting and visualization of the linear regime on log-log axes.

(3) Mechanistic exploration: Side-by-side modeling of clumping vs accrued damage vs compensation frames testable hypotheses for cooperativity. 

Thank you.

Weaknesses:

(1) Secondary infection control: The authors argue that 3 dpi largely avoids progeny-mediated secondary infection; this claim should be strengthened (e.g., entry inhibitors/control infections) or add sensitivity checks showing results are robust to a small secondary-infection contribution. 

This is an important point. We do believe that the current knowledge about HCMV virion production time – it takes 3-4 days to make virions per multiple papers (see Fig 7 in Vonka and Benyesh-Melnick JB 1966; Fig 3B in Stanton et al JCI 2010; and Fig 1A in Li et al. PNAS 2015) – is sufficient to justify our experimental design but we do agree that an additional control to block novel infections with would be useful. We had previously performed experiments with a HCMV TB-gL-KO that cannot make infectious virions (but the stock virions can be made from complemented target cells). We will investigate if our titration experiments with this virus strain have sufficient resolution to detect apparent cooperativity. However, at present we do not have the resources to perform novel experiments.  

(2) Discriminating mechanisms: At present, simulations cannot distinguish between accrued damage and viral compensation. The authors should propose or add a decisive experiment (e.g., dual-color coinfection to quantify true coinfection rates versus "priming" without coinfection; timed sequential inocula) and outline expected signatures for each mechanism. 

Excellent suggestion. Because infection of a cell is a result of the joint viral infectivity and cell resistance, it may be hard to discriminate between these alternatives unless we specify them as particular molecular mechanisms. But we will try our best and list potential future experiments in the revised version of the paper.

(3) Decline at high genomes/cell: Several datasets show a downturn at high input. Hypotheses should be provided (cytotoxicity, receptor depletion, and measurement ceiling) and any supportive controls. 

Another good point. We do not have a good explanation, but we do not believe this is because of saturation of available target cells.  It seemed to only happen (or was most pronounced) with the ME stocks, which are typically lower in titer and so the higher MOI were nearly undiluted stock. It may be the effect of the conditioned medium.  Or perhaps there are non-infectious particles like dense bodies (enveloped particles that lack a capsid and genome) and non-infectious, enveloped particles (NIEPs) that compete for receptors or otherwise damage cells and these don’t get diluted out at the higher doses.  We plan to include these points in Discussion of the revised version of the paper.

(4) Include experimental data: In Figure 6, please include the experimentally measured titers (IU/mL), if available. 

This is a model-simulated scenario, and as such, there is no measured titers.

(5) MOI guidance: The practical guidance is important; please add a short "best-practice box" (how to determine titer at multiple genomes/cell and cell densities; when single-hit assumptions fail) for end-users. 

Good suggestion. We will include best-practice box using guidelines developed in Ryckman lab over the years in the revised version of the paper.

Overall note to all reviews: We have deposited our codes and the data on github; yet, none of the reviewers commented on it.

eLife Assessment

This manuscript reports on the application of ribosome profiling (EZRA-seq and eRF1-seq) combined with massively parallel reporter assays to identify and characterize a GA-rich element associated with ribosome pausing during translation termination. While the development of eRF1-seq is useful and the identification of GA-rich elements upstream of stop codons is convincing, the level of support for other claims is inadequate. Specifically, the evidence that GA-rich sequences upstream of stop codons can base-pair with the 3′ end of 18S rRNA to prolong ribosome dwell time, and the evidence that Rps26 interferes with this interaction to regulate translation termination, are not adequate.

Reviewer #1 (Public review):

Summary:

The authors use high-resolution ribosome profiling (Ezra-seq) and eRF1 pulldown-based ribosome profiling (eRF1-seq) developed in their lab to identify a GA rich sequence motif located upstream of the stop codon responsible for translation termination pausing. They then perform a massively parallel assay with randomly generated sequences to further characterize this motif. Using mouse tissues, they show that termination pausing signatures can be tissue-specific. They use a series of published ribosome structures and 18S rRNA mutants, and eS26 knockdown experiments to propose that the GA rich sequence interacts with the 3′-end of the 18S rRNA.

Strengths:

(1) Robust ribosome profiling data and clear analyses clarify the subtle behavior of terminating ribosomes near the stop codon.

(2) Novel termination or "false termination" sites revealed by eRF1-seq in the 5′-UTR, 3′-UTR, and CDS highlight a previously underappreciated facet of translation dynamics.

Weakness:

(1) Modest effects seen in ABCE1 knockdown do not seem to add up to the level of regulation. The authors state "ABCE1 regulates terminating ribosomes independent of the sequence context" on pg 9, and "ABCE1 modulates termination pausing independent of the mRNA sequence context" in the figure caption for Figure S4. Given the modest effect of the knockdown, such phrasing is most likely not supported. Further clarification of "ABCE1 plays a generic role in translation termination" is necessary.

(2) The authors propose that the GA rich sequence element upstream of the stop codon on the mRNA could potentially base pair with the 3′-end of the 18S rRNA. In the PDBs the authors reference in their paper and also in 3JAG, 3JAH, 3JAI (structures of terminating ribosomes with the stop codon in the A-site and eRF1), the mRNA exiting the ribosome and the 3′-end of the 18S rRNA are about 25-30 A apart. In addition, a segment of eS26 is wedged in between these two RNA segments. This reviewer noted this arrangement in a random sampling of 5 other PDBs of mammalian and human ribosome 80S structures. How do the authors anticipate the base pairing they have proposed to occur in light of these steric hindrances? RpsS26 is known to be released by Tsr2 in yeast during very specific stresses. Is it their expectation that termination pausing in human/mammalian cells happens during stressful conditions only?

(3) The authors say, "It is thus likely that mRNA undergoes post-decoding scanning by 18S rRNA." (pg. 10). It is unclear what the authors mean by "scanning." Do they mean that the mRNA gets scanned in a manner similar to scanning during initiation? There is no evidence presented to support that particular conclusion.

(4) Role of termination pausing in the testis is highly speculative. The authors state: "It is thus conceivable that the wide range of ribosome density at stop codons in testis facilitates functional division of ribosome occupancy beyond the coding region." It is unclear what type of functional division they are referring to.

Reviewer #2 (Public review):

Summary:

This paper presents results interpreted to indicate that sequences upstream of stop codons capable of base-pairing with the 3' end of 18S rRNA prolong the dwell time of 80S ribosomes at stop codons in a manner impeded by Rps26 in the 40S subunit exit channel, which leads to the proper completion of termination and ribosome recycling and prevents spurious translation of 3'UTR sequences by one or more unconventional mechanisms.

Strengths:

The standard 80S and selective eRF1 80S ribosome profiling data obtained using EZRA-Seq are of high quality, allowing the authors to detect an enrichment for purine-rich sequences upstream of stop codons at sites where termination is relatively slow and ribosomal complexes are paused with eRF1 still engaged in the A site.

Weaknesses:

There are many weaknesses in the experimental design, interpretation of results, and description of assay design and assumptions, the data obtained, and the interpretation of results, all of which detract from the scientific quality and significance of this work. In fact, a large proportion of paragraphs in the text and figure panels present some difficulty either in understanding how the experiment or data analysis was conducted or what the authors wish to conclude from the results, or that stem from an overinterpretation of findings or failure to consider other equally likely explanations.

Reviewer #3 (Public review):

Summary:

This study from Jia et al carried out a variety of analyses of terminating ribosomes, including the development of eRF1-seq to map termination sites, identification of a GA-rich motif that promotes ribosome pausing, characterization of tissue-specific termination dynamics, and elucidation of the regulatory roles of 18S rRNA and RPS26. Overall, the study is thoughtfully designed, and its biological conclusions are well supported by complementary experiments. The tools and datasets generated provide valuable resources for researchers investigating the mechanisms of RNA translation.

Strengths:

(1) The study introduces eRF1-seq, a novel approach for mapping translation termination sites, providing a methodological advance for studying ribosome termination.

(2) Through integrative bioinformatic analyses and complementary MPRA experiments, the authors demonstrate that GA-rich motifs promote ribosome pausing at termination sites and reveal possible regulatory roles of 18S rRNA in this process.

(3) The study characterizes tissue-specific ribosome termination dynamics, showing that the testis exhibits stronger ribosome pausing at stop codons compared to other tissues. Follow-up experiments suggest that RPS26 may contribute to this tissue specificity.

Weaknesses:

The biological significance of ribosome pausing regulation at translation termination sites or of translational readthrough, for example, across different tissue types, remains unclear. Nevertheless, this question lies beyond the primary scope of the current study.

Reviewer #4 (Public review):

Summary:

This manuscript by Qian and colleagues utilizes ribosome profiling, and reporter assays to dissect translation termination. Unfortunately, the data do not support the conclusions of the paper, controls are missing and several assays are not well validated and do not reproduce previous findings from others.

Specific comments:

• Translation termination has been studied in several organisms including mammalian cells and yeast. In those cases what is analyzed is not the peak height at the stop codon, but rather the difference in the ribosome density before and after the stop. Thus, analyzing peak height is not validated. I understand that this is relevant only for the ribosome profiling experiments (and Ezra-seq) not the RF1 profiling. But much of the data was acquired that way.

• Moreover, the data do not reproduce previous findings and no effort is made to connect them to previous data. Previous data has shown that stop codon efficacy varies. This is not reproduced (S1C). Similarly, an effect from the +1 residue is not reproduced. The data isn't even stratified by different stop codons as previous work has shown that different surrounding residues have different effects in the context of different stop codons. Thus, none of the sequencing data is validated or trusted and does not reproduce previous findings.

• The GA-rich sequence identified by Ezra-Seq and RF1 seq is not the same and it differs from previous sequences (Wangen &Green).

• The authors claim that the majority of Rf1 peaks is at stop codons, but that is not true. It is only about 30% of the peaks. Also, not all mRNAs have peaks at the stop codons. That is at best problematic. Finally, there are mRNAs that are known to "suffer" from NMD, what do these look like in the Ezra-Seq and RF1-Seq? How about mRNAs that have programmed frameshifts? This raises questions on the validity of the eRF1 data.

• Figure 4: First, instead of M/P ratio, one should analyze M/M+P, to normalize out differences in the loading and effects from collisions, which are guaranteed to occur here, but not considered or analyzed. Second, the data are analyzed as if what matters are codons in the P and E site (and beyond, where there are definitely NOT recognized codons). While there is evidence for some interactions, one would think that an additional analysis based on sequence would be helpful. Also, the supplemental data indicates that very rarely are there reciprocal changes (as should be the case), and as seen for stop codons.

• Regarding the HiBit reporter assay: The two sequecnes clearly have effects on translation without considering stop codon context (Figure 4C), which need to be taken into account. Also, the effect from the sequences varies in the context of the assay in 4C and 4D (2-fold vs .5 fold), further questioning the assay. Moreover, the authors claim that re-initiation cannot account for Hibit levels, but that is clearly incorrect. The western in Figure 4E does not reproduce the data in 4D. While Hibit goes up (as in 4D, the putative GFP-fusion goes down. Finally, while the second reading frame should be more efficient is not explained and further argues for an artifact. Previous work (and work herein) suggests that read-through occurs equally in each reading frame. No controls for these assays are presented: e.g. stimulation by antibiotics, ABCE1 depletion, etc.

• Figure 5 has similar problems. I don't understand how the Figure in 5A is made, but when you overlay the cited structures on Rps26, the molecules are identical. I guess the authors used some fantasy to build non-existing sequences differently into the structure. There is no basis for that. In panel C and the same in Figure 7, the number of analyzed mRNAs varies. This could influence the outcome and the EXACT same set of mRNAs should be analyzed. But the main problem here is that the authors need to analyze readthrough and not peak height as detailed above. Essential controls are missing that show what fraction of the 18S rRNA is mutated. Previous work has shown that 2 nt truncated 18S rRNA is actively degraded. It is hard to believe how 15% of altered ribosomes can abolish 100% of the effect from the C-rich sequences. Important validation is missing: the authors should analyze rRNA sequences in their ribo-seq dataset to demonstrate that they have the mutated rRNAs, and that these enrich and de-enrich as predicted.

• In Figure 5-7 the authors develop a model that the sequence selectivity arises from base pairing between 18S rRNA and the mRNA. If so, then they should really stratify the data by number of WC pairs that can be formed. And only WC pairs, as GU pairs have a totally different geometry that will likely be discriminated against in this context. Also, the mutation is in a part of the helix that has no effect (Figure S3G). Thus, the data within the manuscript are inconsistent.

• Figure 6 does not agree with published data (Li et al., Nature 2022). Previous work did not show testis-depletion of Rps26 in purified ribosomes. This is the critical difference as the authors here did not purify ribosomes. Also, another Rps is an essential control, even if purified ribosomes are used. The validity of this dataset is thus questionable . Depletion from polysomes is hard to believe, as overall there is less signal in the polysomes.

• Figure 7 has similar problems as figure 5. Different pools of mRNAs are analyzed; peak height is not validated. Overexpression of Rps26 is not shown, as only Myc is shown, not Rps26. Beyond that, increased occupancy in ribosomes needs to be shown for the effect to come from ribosomes. Given how sick the cells are it is most likely that all effects are secondary and arise from whatever else is going on in the overexpression or depletion of Rps26. No controls are presented to show specific effects from Rps26.

• The authors need to check Rli1/ABCE levels in their cells. Their data have features that are indicative of low ABCE1 levels. These include a very small effect from ABCE1 depletion. These could be responsible for some of the effects they observe.

Author response:

We thank the editor and reviewers for their thoughtful feedback. We agree with eLife’s overall assessment that, while profiling terminating ribosomes is informative in revealing termination dynamics, the underlying mechanisms require more evidence. Our revision will focus on three conceptual points.

(1) We will tone down the statement that putative mRNA:rRNA interaction contributes to sequence-specific termination pausing.

(2) We will clarify the potential role of Rps26 in regulating translation termination.

(3) We will expand the discussion of tissue-specific termination pausing.

Reviewer #1 (Public Review):

(1) We admit that the modest effects of ABCE1 were partly due to the incomplete ABCE1 knockdown in HEK293 cells. Since the elevated ribosome density occurred at all stop codons, we argue that the action of ABCE1 is likely independent of the sequence context. We will rephrase relevant statements in the revised manuscript.

(2) In terms of Rps26 structures, we agree the structural rearrangement in the absence of Rps26 is highly speculative. However, we do not believe the Rps26 stoichiometry is solely dependent on stress. We will clarify this important point in the revised manuscript.

(3) We apologize for the confusion about 18S rRNA “scanning” and will revise the sentence in the main text.

(4) We agree that functional significance of testis-specific termination dynamics is unclear. Since other reviewers raised similar concern, we will expand the discussion of tissue-specific termination pausing in the revised manuscript.

Reviewer #2 (Public Review):

We appreciate the Reviewer’s time and efforts in reviewing our manuscript. We are grateful for the insightful comments and many recommendations made by the reviewer to improve our manuscript. We feel that the reviewer may have some misunderstanding in terms of the sequence motif associated with the termination pausing, partly because of the lack of clarity in our original description of the results from MPRA and reporter assays. We will ensure that the reviewer’s points are fully addressed in the revised manuscript.

Reviewer #3 (Public Review):

We thank the reviewer’s positive comment on our manuscript. We agree that the tissue-specific termination differences were poorly described in the main text. Notably, other reviewers raised similar concerns. We will expand the relevant discussion in the revised manuscript, outlining this as a limitation and a future direction.

Reviewer #4 (Public Review):

We believe the reviewer mixed xthe public view with recommendation comments. The reviewer appears to be preoccupied by previous studies and questioned some inconsistency in our results. With the development of new technology such as eRF1-seq, we are encouraged to present “new” and “different” findings. All other reviewers appreciate the development of eRF1-seq to profile terminating ribosomes. In fact, we do not believe our data is fundamentally different from the established principles. Rather, our data provides new perspectives to further our understanding of ribosome dynamics at stop codons. We thank the reviewer for understanding.

The reviewer is quite confused by our sequencing analysis based on peak height, or read density, which is commonly used to infer ribosome dynamics such as pausing. Regarding the sequencing analysis and reporter assays in cells expressing 18S mutant (Figure 5) and Rps26 (Figure 7), we feel that the reviewer has some misunderstanding. In the revised manuscript, we will do our best to clarify those relevant issues. Finally, the reviewer’s comment on base pairing is well-received and we will thoroughly revise the main text and discussion in the revised manuscript.

eLife Assessment

The authors investigated the epigenetic mechanisms regulating the differentiation of circulating monocytes that infiltrate the CNS and adopt microglia-like characteristics. The work is useful to the field, as the contribution of circulating myeloid cell-derived microglia remains controversial. However, the evidence presented is inadequate as the analyses are based on a very limited set of genes, which does not sufficiently support the authors' central claims.

Reviewer #1 (Public review):

Microglia are mononuclear phagocytes in the CNS and play essential roles in physiology and pathology. In some conditions, circulating monocytes may infiltrate in the CNS and differentiated into microglia or microglia-like cells. However, the specific mechanism is large unknown. In this study, the authors explored the epigenetic regulation of this process. The quality of this study will be significantly improved if a few questions are addressed.

(1) The capacity of circulating myeloid cell-derived microglia are controversial. In this study, the authors utilized CX3CR1-GFP/CCR2-DsRed (hetero) mice as a lineage tracing line. However, this animal line is not an appropriate approach for this purpose. For example, when the CX3CR1-GFP/CCR2-DsRed as the undifferentiated donor cell, they are GFP+ and DsRed+. When the cell fate has been changed to microglia, they will change into GFP+ and DsRed- cells. However, this process is mediated with busulfan and artificially introduced bone marrow cells in the circulating cell, which is not existed in physiological and pathological conditions. These artifacts will potentially bring in artifacts and confound the conclusion, as the classical wrong text book knowledge of the bone marrow derived microglia theory and subsequently corrected by Fabio Rossi lab1,2. This is the most risk for drawing this conclusion. The top evidence is from the parabiosis animal model. Therefore, A parabiosis study before making this conclusion, combining a CX3CR1-GFP (hetero) mouse with a WT mouse without busulfan conditioning and looking at whether there are GFP+ microglia in the GFP- WT mouse brain. If there are no GFP+ microglia, the author should clarify this is not a physiological or pathological condition, but a defined artificial host condition, as previously study did3.

(2) In some conditions, peripheral myeloid cells can infiltrate and replace the brain microglia4,5. Discuss it would be helpful to better understand the mechanism of microglia replacement.

References:

(1) Ajami, B., Bennett, J.L., Krieger, C., Tetzlaff, W., and Rossi, F.M. (2007). Local self-renewal can sustain CNS microglia maintenance and function throughout adult life. Nature neuroscience 10, 1538-1543. 10.1038/nn2014.

(2) Ajami, B., Bennett, J.L., Krieger, C., McNagny, K.M., and Rossi, F.M.V. (2011). Infiltrating monocytes trigger EAE progression, but do not contribute to the resident microglia pool. Nature neuroscience 14, 1142-1149. http://www.nature.com/neuro/journal/v14/n9/abs/nn.2887.html#supplementary-information.

(3) Mildner, A., Schmidt, H., Nitsche, M., Merkler, D., Hanisch, U.K., Mack, M., Heikenwalder, M., Bruck, W., Priller, J., and Prinz, M. (2007). Microglia in the adult brain arise from Ly-6ChiCCR2+ monocytes only under defined host conditions. Nature neuroscience 10, 1544-1553. 10.1038/nn2015.

(4) Wu, J., Wang, Y., Li, X., Ouyang, P., Cai, Y., He, Y., Zhang, M., Luan, X., Jin, Y., Wang, J., et al. (2025). Microglia replacement halts the progression of microgliopathy in mice and humans. Science 389, eadr1015. 10.1126/science.adr1015.

(5) Xu, Z., Rao, Y., Huang, Y., Zhou, T., Feng, R., Xiong, S., Yuan, T.F., Qin, S., Lu, Y., Zhou, X., et al. (2020). Efficient strategies for microglia replacement in the central nervous system. Cell reports 32, 108041. 10.1016/j.celrep.2020.108041.

Reviewer #2 (Public review):

Mouse fate mapping studies have established that the bulk of microglia derives from cells that seed the brain early during development. However, monocytes were also shown to give rise to parenchymal CNS macrophages and thus are potential candidates for microglia replacement therapy. Whether monocyte-derived cells adopt bona fide microglia identities has remained under debate. The study of Liu et al addresses this important outstanding question, focusing on the retina.

Specifically, the authors investigate monocyte-derived macrophages that arise upon challenges in the murine retina using scRNAseq and ATACseq analyses, combined with flow cytometry and histology. They complement this approach with an analysis of BM chimeras and analyses of the latter. The authors conclude that monocyte-derived cells acquire markers that have originally been proposed to be microglia-specific, including P2ry12, Tmem119, and Fcrls.

In 2018, four comprehensive independent studies reported the analyses of monocyte-derived CNS macrophages (PMID 30451869, 30523248, 29643186, 29861285). Following transcriptome and epigenome analyses, these teams came to the collective conclusion that HSC-derived cells remain distinct from microglia. Using advanced fate mapping and better isolation and profiling tools, a more recent study, however, concluded that, if given sufficient time of CNS residence, most monocyte-derived macrophages can, at the transcriptome level, become essentially identical to microglia (PMID 40279248, https://www.biorxiv.org/content/10.1101/2023.11.16.567402v1).

Given this controversy, the study of Paschalis and colleagues, which focuses largely on retinal monocyte-derived cells, could have been a valuable resource and complement for clarification. Indeed, interestingly, their data suggest that microglia adaptation of monocyte-derived macrophages might be faster in the retina than in the CNS. However, for the reasons outlined below, the study falls in its present form short of providing significant new insight and is a missed opportunity.

Comments:

The major shortcoming of the study is that the authors decided to focus on a very limited number of genes to make their case, rather than performing a more informative, unbiased, and detailed global analysis. In contrast to what the authors state, much of the microglia community is, I believe, aware of experimental limitations and the problem with markers. Showing gain of microglia marker expression on monocyte-derived cells, or loss of monocyte markers, such as Ly6C, is not novel.

This is highlighted Fig. 3F. No one argues today that monocyte-derived tissue macrophages differ from blood monocytes (although the authors repeatedly emphasize this as novelty). However, the heatmap shows that the engrafted cells clearly differ from naïve and injured microglia. What are these genes, their associated pathways ?

Also, how about expression of the Sall1 gene that encodes a repressor that is considered important to maintain microglia identity (PMID37322178, 27776109). Somewhat surprisingly, Sall1 was recently also shown to be expressed by monocyte-derived CNS macrophages (PMID 40279248). It would be valuable information if the authors can corroborate this finding.

The authors state in their discussion that monocyte-derived macrophages seem 'hardwired for inflammatory responses'. While this is an interesting suggestion, the NFkB motif enrichment is insufficient and should be complemented with a target list. Again, it would be important to be aware of heterogeneity.

A critical factor when analyzing CNS macrophages is the exclusion of perivascular CNS border-associated cells, which also holds for the retina (see PMID 38596358). This should be addressed. Can the authors discriminate BAM from microglia in their scRNAseq data set, for instance, by their CD206 expression or other markers ? BAM have been shown to display distinct transcriptomes and even as a contamination could introduce significant bias.

Even for the genes the authors focus on, it is hard to understand from the way the authors present the data what fraction of cells are positive. This would be critical information since there could be some heterogeneity. Flowcytometry analysis, including double staining for P2ry12, Tmem119, and Fcrls to see correlations, would here be valuable.

The authors state in their title that 'epigenetic adaptation drives monocyte differentiation'. However, since all gene expression is governed by the epigenome, this is trivial. I would argue that to gain meaningful insight and justify such a statement, it would require an in-depth global comparative analysis of the chromatin status of yolk sac microglia and monocyte-derived CNS macrophages, including CUT&RUN analysis for specific histone marks and methylation patterns.

Please cite and discuss PMID 30451869, 30523248, 29643186, 29861285, and in particular the more recent highly relevant study PMID 40279248.

eLife Assessment

This study presents a role for heparin sulfate in SARS-CoV-2 entry that runs counter to prevailing data in the field. If the conclusions were firmly supported by the data, the work would be a significant contribution to the field. While the use of diverse cellular models, virological tools, and robust microscopy approaches constitutes a useful data set, the proposed model remains incomplete and requires clarification of entry mechanisms, host factors, and viral variant-specific fusion pathways to substantiate it against established entry models.

Reviewer #1 (Public review):

This paper investigates how heparan sulfate (HS) engagement functions in the cellular entry of SARS-CoV-2. A prevailing model that has been developed over the last five years by work from many laboratories using a variety of biochemical, structural, and microscopic approaches is that HS acts a co-receptor for SARS-CoV-2; its binding to SARS-CoV-2 both concentrates virus on the surface of target cells and allosterically alters the spike protein to promote an "up/open" RBD conformation that enables engagement of the proteinaceous receptor human ACE2 on the cell surface (PMID: 32970989, 35926454, 38055954, 39401361, 40548749). These two events enable plasma membrane fusion (after a cleavage event promoted by plasma membrane TMPSS2) or endocytosis and subsequent pH-dependent fusion (which requires a cathepsin L-mediated cleavage of the spike).

The authors in this study used a series of microscopy techniques, labeled pseudoviruses and authentic SARS-CoV-2 strains, and cells lacking or expressing HS and/or hACE2 to re-examine the specific stage(s) HS and hACE2 function in the entry process. They suggest that HS mediates SARS-CoV-2 cell-surface attachment and endocytosis, and that hACE2 functions "downstream" of this to facilitate productive infection. Their results also suggest that SARS-CoV-2 binds clusters of HS molecules projecting 60-410 nm, which act as docking sites for viral attachment. Blocking HS binding with pixantrone, a drug under clinical evaluation for cancer (due to its anti-topoisomerase II activity), inhibited SARS-CoV-2 Omicron JN.1 variant from attaching to and infecting human airway cells. The authors conclude that their work establishes a revised entry paradigm in which HS clusters mediate SARS-CoV-2 attachment and endocytosis, with ACE2 acting at some stage downstream. They speculate this idea might apply broadly to other viruses known to engage HS and has translational implications for developing antiviral agents that target HS interactions.

The strengths of the interesting and technically well-executed study include the use of multiple high-resolution microscopy modalities, the tracking of labelled viruses, the use of both pseudoviruses and authentic SARS-CoV-2, and the use of primary airway cells. Nonetheless, there are issues that need to be addressed to buttress the proposed model compared to earlier ones. These include: (a) the distinction between macropinocytosis and receptor-mediated endocytosis and what this might mean for productive SARS-CoV-2 infection; (b) the need to account for TMPRSS2 expression and plasma membrane fusion; (c) addition of genetic studies in which hACE2 is expressed in cells lacking HS; (d) an unclear picture of exactly where downstream hACE2 functions; and (e) and a need for comparative/additional study of earlier SARS-CoV-2 variants, which preferentially fuse at the plasma membrane.

Reviewer #2 (Public review):

In this manuscript by Han et al, the authors assess the binding of SARS-CoV-2 to heparan sulfate clusters via advanced light microscopy of viral particles. The authors claim that the SARS-CoV-2 spike (in the context of pseudovirus and in authentic virus) engages heparan sulfate clusters on the cell surface, which then promotes endocytosis and subsequent infection. The finding that HSPGs are important for SARS-CoV-2 entry in some cell types is well-described, but the authors attempt to make the claim here that HS represents an alternative "receptor" and that HS engagement is far more important than the field appreciates. The data itself appears to be of appropriate quality and would be of interest to the field, but the overly generalized conclusions lack adequate experimental support. This significantly diminishes enthusiasm for this manuscript as written. The manuscript is imprecise and far overstates the actual findings shown by the data. Additional controls would be of great benefit.

Further, it is this reviewer's opinion that the findings do not represent a novel paradigm as claimed. HS has been well described for SARS-CoV-2 and other viruses to serve as attachment factors to promote initial virus attachment. While the manuscript provides new insight into the details of this process, the manuscript attempts to oversell this finding by applying new words rather than new molecular details. The authors would be better served by presenting a more balanced and nuanced view of their interesting data. In this reviewer's opinion, the salesmanship significantly detracts from the data and manuscript.

Major Comments:

The authors need to rigorously define a "receptor" vs an "attachment factor." They also should avoid ambiguous terms such as "receptor underlying ...attachment" and "attachment receptor" (or at least clearly define them). Much of their argument hinges on the specific definition of these terms. This reviewer would argue that a receptor is a host factor that is necessary and sufficient for active promotion of viral entry (genome release into the cytoplasm), while an attachment factor is a host factor that enhances initial viral attachment/endocytosis but is neither necessary nor sufficient. The evidence does NOT implicate HS as a receptor under this fairly textbook definition. This is proven in Figure 1 (and elsewhere) in which ACE2 is absolutely required for viral entry.

The authors should genetically perturb HS biosynthesis in their key assays to demonstrate necessity. HS biosynthesis genes have been shown to be important for SARS-CoV-2 entry into some cells but not others (Huh7.5 cells PMID 33306959, but not in Vero cells PMID 33147444, Calu3 cells 35879413, A549 cells 33574281, and others 36597481. The authors need to discuss this important information and reconcile it with their data and model if they want to claim that HS is broadly important.

Is targeting HS really a compelling anti-viral strategy? The data show a ~5-fold reduction, which likely won't excite a drug company. The strengths and limitations of HS targeting should be presented in a more balanced discussion. Animal data showing anti-viral activity of PIX is warranted. This would enhance this claim and also provide key evidence of a relevant role for HS in a more physiologic model.

The authors provide little discussion of the fact that these studies rely exclusively on cell lines (which also happen to be TMPRSS2-deficient). The role of proteases in the role of HS should be tested in the cell lines and primary cells used, as protease expression is a key determinant of the site of fusion.

The claim that "SARS-CoV2 JN.1 variant binds to heparan sulfate, not hACE2, in primary human airway cells" is extraordinary and thus requires extraordinary evidence.

First, PIX reduces attachment by 5-fold, which is not the same as "nearly abolished." Also, anti-ACE2 "nearly abolished" entry in 7D, while PIX did not. If the authors want to make these claims, an alternative method to disrupt HS (other than PIX) is needed in primary airway cells. A genetic approach would be much more convincing. The authors should also demonstrate whether entry in their primary cell assays is TMPRSS2 vs Cathepsin L dependent (using E64d and camostat, for instance) as mentioned above.

Each figure should clearly state how many independent experiments and replicates per experiment were performed. What does "3 experiments" mean? Are these three independent experiments or three wells on one day?

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors define a new paradigm for the attachment and endocytosis of SARS-CoV-2 in which cell surface heparan sulfate (HS) is the primary receptor, with ACE2 having a downstream role within endocytic vesicles. This has implications for the importance of targeting virion-HS interactions as a therapeutic strategy.

Strengths:

The authors show that viruses are internalized via dynamin-dependent endocytosis and that endocytic internalization is the major pathway for pseudotyped SARS-CoV-2 genome expression. They show that HS-mediated viral attachment is a critical step preceding viral endocytosis and also subsequent genome expression. Further, they show that hACE2 acts downstream of endocytosis to promote viral infection, and may be co-internalised with virions after HS attachment. Pseudotyped virus and authentic SARS-CoV-2 provide similar results. In addition, the authors demonstrate that remarkable clusters of multiple HS chains exist on the cell surface, visualised by a number of elegant microscopy methods, and that these represent the docking sites for virions. These visualisations are an important general contribution in themselves to understanding the nanoscale interactions of HS at the cell surface.

The use of a complementary range of methods, virus constructs, and cell models is a strength, and the results clearly support the conclusions.

Overall, the results convincingly demonstrate a different model to the currently accepted mechanism in which the ACE2 protein is regarded as the cell surface receptor for SARS-CoV-2. Here, the authors provide compelling evidence that cell surface clusters of HS are the primary docking site, with ACE2 interactions occurring later, after endocytosis (whilst still being essential for viral genome expression). This is an exciting and important landmark evidence which supports the view that HS-virion interactions should be viewed as a key site for anti-viral drug targeting, likely in strategies that also target the downstream ACE2-based mechanism of viral entry within endosomes.

Weaknesses:

This reviewer identified only minor points regarding citing and discussing other studies and typos, which can be corrected.

eLife Assessment

This work details the finding that in at least one of the subunits of the heterohexameric chaperone complex Pfdn5 has additional functions beyond its contribution to cytoskeletal protein folding in Drosophila. The authors provide convincing evidence that it is a hitherto unknown microtubule associated protein in addition to regulating microtubule organization and levels of tubulin monomers. The important findings show that Pfdn5 loss exaggerates pathological manifestations of mutant human Tau bearing FTDP-17 linked mutations in Drosophila, while its overexpression suppresses them, suggesting that the latter may constitute a future therapeutic approach.

Reviewer #1 (Public review):

Summary:

In this manuscript, Bisht et al address the hypothesis that protein folding chaperones may be implicated in aggregopathies and in particular Tau aggregation, as a means to identify novel therapeutic routes for these largely neurodegenerative conditions.

The authors conducted a genetic screen in the Drosophila eye, which facilitates identification of mutations that either enhance or suppress a visible disturbance in the nearly crystalline organization of the compound eye. They screened by RNA-interference all 64 known Drosophila chaperones and revealed that mutations in 20 of them exaggerate the Tau-dependent phenotype, while 15 ameliorated it. The enhancer of degeneration group included 2 subunits of the typically heterohexameric prefoldin complex and other co-translational chaperones.

The authors characterized in depth one of the prefoldin subunits, Pfdn5 and convincingly demonstrated that this protein functions in regulation of microtubule organization, likely due to its regulation of proper folding of tubulin monomers. They demonstrate convincingly using both immunohistochemistry in larval motor neurons and microtubule binding assays that Pfdn5 is a bona fide microtubule associated protein contributing to the stability of the axonal microtubule cytoskeleton, which is significantly disrupted in the mutants.

Similar phenotypes were observed in larvae expressing the Frontotemporal dementia with Parkinsonism on chromosome 17-associated mutations of the human Tau gene V377M and R406W. On the strength of the phenotypic evidence and the enhancement of the TauV377M-induced eye degeneration they demonstrate that loss of Pfdn5 exaggerates the synaptic deficits upon expression of the Tau mutants. Conversely, overexpression of Pfdn5 or Pfdn6 ameliorates the synaptic phenotypes in the larvae, the vacuolization phenotypes in the adult, even memory defects upon TauV377M expression.

Strengths:

The phenotypic analyses of the mutant and its interactions with TauV377M at the cell biological, histological, and behavioral levels are precise, extensive, and convincing and achieve the aims of characterization of a novel function of Pfdn5.

Regarding this memory defect upon V377M tau expression. Kosmidis et al (2010) pmid: 20071510, demonstrated that pan-neuronal expression of TauV377M disrupts the organization of the mushroom bodies, the seat of long-term memory in odor/shock and odor/reward conditioning. If the novel memory assay the authors use depends on the adult brain structures, then the memory deficit can be explained in this manner.

If the mushroom bodies are defective upon TauV377M expression does overexpression of Pfdn5 or 6 reverse this deficit? This would argue strongly in favor of the microtubule stabilization explanation.

The discovery that Pfdn5 (and 6 most likely) affect tauV377M toxicity is indeed a novel and important discovery for the Tauopathies field. It is important to determine whether this interaction affects only the FTDP-17-linked mutations, or also WT Tau isoforms, which are linked to the rest of the Tauopathies. Also, insights on the mode(s) that Pfdn5/6 affect Tau toxicity, such as some of the suggestions above are aiming at, will likely be helpful towards therapeutic interventions.

Weaknesses:

What is unclear however is how Pfdn5 loss or even overexpression affects the pathological Tau phenotypes.

Does Pfdn5 (or 6) interact directly with TauV377M? Colocalization within tissues is a start, but immunoprecipitations would provide additional independent evidence that this is so.

Does Pfdn5 loss exacerbate TauV377M phenotypes because it destabilizes microtubules, which are already at least partially destabilized by Tau expression?<br /> Rescue of the phenotypes by overexpression of Pfdn5 agrees with this notion.

However, Cowan et al (2010) pmid: 20617325 demonstrated that wild-type Tau accumulation in larval motor neurons indeed destabilizes microtubules in a Tau phosphorylation-dependent manner.

So, is TauV377M hyperphosphorylated in the larvae?? What happens to TauV377M phosphorylation when Pfdn5 is missing and presumably more Tau is soluble and subject to hyperphosphorylation as predicted by the above?

Expression of WT human Tau (which is associated with most common Tauopathies other than FTDP-17) as Cowan et al suggest has significant effects on microtubule stability, but such Tau-expressing larvae are largely viable. Will one mutant copy of the Pfdn5 knockout enhance the phenotype of these larvae?? Will it result in lethality? Such data will serve to generalize the effects of Pfdn5 beyond the two FDTP-17 mutations utilized.

Does the loss of Pfdn5 affect TauV377M (and WTTau) levels?? Could the loss of Pfdn5 simply result in increased Tau levels? And conversely, does overexpression of Pfdn5 or 6 reduce Tau levels?? This would explain the enhancement and suppression of TauV377M (and possibly WT Tau) phenotypes. It is an easily addressed, trivial explanation at the observational level, which if true begs for a distinct mechanistic approach.

Finally, the authors argue that TauV377M forms aggregates in the larval brain based on large puncta observed especially upon loss of Pfdn5. This may be so, but protocols are available to validate this molecularly the presence of insoluble Tau aggregates (for example, pmid: 36868851) or soluble Tau oligomers as these apparently differentially affect Tau toxicity. Does Pfdn5 loss exaggerate the toxic oligomers and overexpression promotes the more benign large aggregates??

Comments on revisions:

In the revised manuscript Βisht et al have provided extensive new experimental evidence in support of previously more tenuous claims. These fully satisfy my comments and suggestions, and in my view, have significantly strengthened the manuscript with compelling new evidence.

Reviewer #2 (Public review):

Bisht et al detail a novel interaction between the chaperone, Prefoldin 5, microtubules, and tau-mediated neurodegeneration, with potential relevance for Alzheimer's disease and other tauopathies. Using Drosophila, the study shows that Pfdn5 is a microtubule-associated protein, which regulates tubulin monomer levels and can stabilize microtubule filaments in the axons of peripheral nerves. The work further suggests that Pfdn5/6 may antagonize Tau aggregation and neurotoxicity. While the overall findings may be of interest to those investigating the axonal and synaptic cytoskeleton, the detailed mechanisms for the observed phenotypes remain unresolved and the translational relevance for tauopathy pathogenesis is yet to be established. Further, a number of key controls and important experiments are missing that are needed to fully interpret the findings.

The strength of this study is the data showing that Pfdn5 localizes to axonal microtubules and the loss-of-function phenotypic analysis revealing disrupted synaptic bouton morphology. The major weakness relates to the experiments and claims of interactions with Tau-mediated neurodegeneration. In particular, it is unclear whether knockdown of Pfdn5 may cause eye phenotypes independent of Tau. Further, the GMR>tau phenotype appears to have been incorrectly utilized to examine age-dependent, neurodegeneration.

This manuscript argues that its findings may be relevant to thinking about mechanisms and therapies applicable to tauopathies; however, this is premature given that many questions remain about the interactions from Drosophila, the detailed mechanisms remain unresolved, and absent evidence that tau and Pfdn may similarly interact in the mammalian neuronal context. Therefore, this work would be strongly enhanced by experiments in human or murine neuronal culture or supportive evidence from analyses of human data.

Comments on revisions:

The revision adequately addresses most of the previously raised concerns, resulting in a significantly improved manuscript.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this manuscript, Bisht et al address the hypothesis that protein folding chaperones may be implicated in aggregopathies and in particular Tau aggregation, as a means to identify novel therapeutic routes for these largely neurodegenerative conditions.

The authors conducted a genetic screen in the Drosophila eye, which facilitates the identification of mutations that either enhance or suppress a visible disturbance in the nearly crystalline organization of the compound eye. They screened by RNA interference all 64 known Drosophila chaperones and revealed that mutations in 20 of them exaggerate the Tau-dependent phenotype, while 15 ameliorated it. The enhancer of the degeneration group included 2 subunits of the typically heterohexameric prefoldin complex and other co-translational chaperones.

The authors characterized in depth one of the prefoldin subunits, Pfdn5, and convincingly demonstrated that this protein functions in the regulation of microtubule organization, likely due to its regulation of proper folding of tubulin monomers. They demonstrate convincingly using both immunohistochemistry in larval motor neurons and microtubule binding assays that Pfdn5 is a bona fide microtubule-associated protein contributing to the stability of the axonal microtubule cytoskeleton, which is significantly disrupted in the mutants.

Similar phenotypes were observed in larvae expressing Frontotemporal dementia with Parkinsonism on chromosome 17-associated mutations of the human Tau gene V377M and R406W. On the strength of the phenotypic evidence and the enhancement of the TauV377Minduced eye degeneration, they demonstrate that loss of Pfdn5 exaggerates the synaptic deficits upon expression of the Tau mutants. Conversely, the overexpression of Pfdn5 or Pfdn6 ameliorates the synaptic phenotypes in the larvae, the vacuolization phenotypes in the adult, and even memory defects upon TauV377M expression.

Strengths

The phenotypic analyses of the mutant and its interactions with TauV377M at the cell biological, histological, and behavioral levels are precise, extensive, and convincing and achieve the aims of characterization of a novel function of Pfdn5. 

Regarding this memory defect upon V377M tau expression. Kosmidis et al (2010), PMID: 20071510, demonstrated that pan-neuronal expression of Tau^V377M disrupts the organization of the mushroom bodies, the seat of long-term memory in odor/shock and odor/reward conditioning. If the novel memory assay the authors use depends on the adult brain structures, then the memory deficit can be explained in this manner. 

(1) If the mushroom bodies are defective upon Tau^V377M. expression, does overexpression of Pfdn5 or 6 reverse this deficit? This would argue strongly in favor of the microtubule stabilization explanation.

We thank the reviewer for this insightful comment. Consistent with Kosmidis et al. (2010), we confirm that expression of hTau^V377M disrupts the architecture of mushroom bodies.   In addition, we find, as suggested by the reviewer, that coexpression of either Pfdn5 or Pfdn6 with hTau^V377M significantly restores the organization of the mushroom bodies. These new findings strongly support the hypothesis that Pfdn5 or Pfdn6 mitigate hTau^V377M -induced memory deficits by preserving the structure of the mushroom body, likely through stabilizing the microtubule network. This data has now been included in the revised manuscript (Figure 7H-O).

(2) The discovery that Pfdn5 (and 6 most likely) affects tauV377M toxicity is indeed a novel and important discovery for the Tauopathies field. It is important to determine whether this interaction affects only the FTDP-17-linked mutations or also WT Tau isoforms, which are linked to the rest of the Tauopathies. Also, insights on the mode(s) that Pfdn5/6 affect Tau toxicity, such as some of the suggestions above, are aiming at will likely be helpful towards therapeutic interventions.

We agree that determining whether prefoldin modulates the toxicity of both mutant and wildtype Tau is critical for understanding its broader relevance to Tauopathies. We have now performed additional experiments required to address this issue. These new data show that loss of Pfdn5 also exacerbates toxicity associated with wildype Tau (hTau^WT), in a manner similar to that observed with hTau^V337M or hTau^R406W. Specifically, overexpression of hTau^WT in a Pfdn5 mutant background leads to Tau aggregate formation (Figure S7G-I), and coexpression of Pfdn5 with hTau^WT reduces the associated synaptic defects (Figure S11F-L). These findings underscore a general role for Pfdn5 in modulating diverse Tauopathy-associated phenotypes and suggest that it could be a broadly relevant therapeutic target. 

Weakness

(3) What is unclear, however, is how Pfdn5 loss or even overexpression affects the pathological Tau phenotypes. Does Pfdn5 (or 6) interact directly with TauV377M? Colocalization within tissues is a start, but immunoprecipitations would provide additional independent evidence that this is so.

We appreciate this important suggestion. To investigate a potential direct interaction between Pfdn5 and Tau^V377M, we performed co-immunoprecipitation experiments using lysates from adult fly brain expressing hTau^V337M. Under the conditions tested, we did not detect a direct physical interaction. While this does not support a direct interaction, it does not strongly refute it either. We note that Pfdn5 and Tau are colocalized within axons (Figure S13J-K). At this stage, we are unable to resolve the issue of direct vs indirect association. If indirect, then Tau and Pfdn5 act within the same subcellular compartments (axon); if direct, then either only a small fraction of the total cellular proteins is in the Tau-Pfdn5 complex and therefore difficult to detect in bulk protein westerns, or the interactions are dynamic or occur in conditions that we have not been able to mimic in vitro. 

(4) Does Pfdn5 loss exacerbate Tau^V377M phenotypes because it destabilizes microtubules, which are already at least partially destabilized by Tau expression? Rescue of the phenotypes by overexpression of Pfdn5 agrees with this notion. 

However, Cowan et al (2010) pmid: 20617325 demonstrated that wildtype Tau accumulation in larval motor neurons indeed destabilizes microtubules in a Tau phosphorylation-dependent manner. So, is Tau^V377M hyperphosphorylated in the larvae?? What happens to Tau^V377M phosphorylation when Pfdn5 is missing and presumably more Tau is soluble and subject to hyperphosphorylation as predicted by the above?

We completely agree that it is important to link Tau-induced phenotypes with the microtubule destabilization and phosphorylation state of Tau.   We performed immunostaining using futsch antibody to check the microtubule organization at the NMJ and observed a severe reduction in futsch intensity when Tau^V337M was expressed in the Pfdn5 mutant (ElavGal4>Tau^V337M; DPfdn5^15/40), suggesting that Pfdn5 absence exacerbates the hTau^V337M defects due to more microtubule destabilization (Figure S6F-J). 

We have performed additional experiments to examine the phosphorylation state of hTau in Drosophila larval axons. Immunocytochemistry indicated that only a subset of hTau aggregates in Pfdn5 mutants (Elav-Gal4>Tau^V337M; DPfdn5^15/40) are recognized by phospho-hTau antibodies.   For instance, the AT8 antibody (targeting pSer202/pThr205) (Goedert et al., 1995) labelled only a subset of aggregates identified by the total hTau antibody (D5D8N) (Figure S9AE). Moreover, feeding these larvae (Elav-Gal4>Tau<sup>V337M</sup; DPfdn5^15/40) with LiCl, which blocks GSK3b, still showed robust Tau aggregation (Figure S9F-J). 

These results imply that: a) soluble phospho-hTau levels in Pfdn5 mutants are low and not reliably detected with a single phospholylation-specific antibody; b) Loss of Pfdn5 results in Tau aggregation in a hyperphosphorylation-independent manner similar to what has been reported earlier (LI et al. 2022); and c) the destabilization of microtubules in Elav-Gal4>Tau^V337M; DPfdn5^15/40 results in Tau dissociation and aggregate formation. These data and conclusions have been incorporated into the revised manuscript.

(5) Expression of WT human Tau (which is associated with most common Tauopathies other than FTDP-17) as Cowan et al suggest has significant effects on microtubule stability, but such Tauexpressing larvae are largely viable. Will one mutant copy of the Pfdn5 knockout enhance the phenotype of these larvae?? Will it result in lethality? Such data will serve to generalize the effects of Pfdn5 beyond the two FDTP-17 mutations utilized.

We have now examined whether heterozygous loss of Pfdn5 (∆Pfdn5/+) enhances the effect of Tau expression. While each genotype (hTau^V337M, hTau^WT or ∆Pfdn5/+) alone is viable, Elav-Gal4 driven expression of hTau^V337M or hTau^WT in Pfdn5 heterozygous background does not cause lethality. 

(6) Does the loss of Pfdn5 affect TauV377M (and WTTau) levels?? Could the loss of Pfdn5 simply result in increased Tau levels? And conversely, does overexpression of Pfdn5 or 6 reduce Tau levels?? This would explain the enhancement and suppression of Tau^V377M (and possibly WT Tau) phenotypes. It is an easily addressed, trivial explanation at the observational level, which, if true, begs for a distinct mechanistic approach.

To test whether Pfdn5 modulates Tau phenotypes by altering Tau protein levels, we performed western blot analysis under Pfdn5 or Pfdn6 overexpression conditions and observed no change in hTau^V337M levels (Figure 6O). However, in the absence of Pfdn5, both hTau^V337M and hTau^WT form large, insoluble aggregates that are not detected in soluble lysates by standard western blotting but are visualized by immunocytochemistry (Figure S7G-I). Thus, the apparent reduction in Tau levels on western blots reflects a solubility shift, not an actual decrease in Tau expression. These findings argue against a simple model in which Pfdn5 regulates Tau abundance and instead support a mechanism in which Pfdn5 loss leads to change in Tau conformation, leading to its sequesteration away for already destabilized microtubules.  

(7) Finally, the authors argue that Tau^V377M forms aggregates in the larval brain based on large puncta observed especially upon loss of Pfdn5. This may be so, but protocols are available to validate this molecularly the presence of insoluble Tau aggregates (for example, pmid: 36868851) or soluble Tau oligomers, as these apparently differentially affect Tau toxicity. Does Pfdn5 loss exaggerate the toxic oligomers, and overexpression promote the more benign large aggregates??

We have performed additional experiments to analyze the nature of these aggregates using 1,6-HD. The 1,6-hexanediol can dissolve the Tau aggregate seeds formed by Tau droplets, but cannot dissolve the stable Tau aggregates (WEGMANN et al. 2018). We observed that 5% 1,6hexanediol failed to dissolve these Tau aggregates (Figure S8), demonstrating the formation of stable filamentous flame-shaped NFT-like aggregates in the absence of Pfdn5 (Figure 5D and Figure S9).

Reviewer #2 (Public review):

Bisht et al detail a novel interaction between the chaperone, Prefoldin 5, microtubules, and taumediated neurodegeneration, with potential relevance for Alzheimer's disease and other tauopathies. Using Drosophila, the study shows that Pfdn5 is a microtubule-associated protein, which regulates tubulin monomer levels and can stabilize microtubule filaments in the axons of peripheral nerves. The work further suggests that Pfdn5/6 may antagonize Tau aggregation and neurotoxicity. While the overall findings may be of interest to those investigating the axonal and synaptic cytoskeleton, the detailed mechanisms for the observed phenotypes remain unresolved and the translational relevance for tauopathy pathogenesis is yet to be established. Further, a number of key controls and important experiments are missing that are needed to fully interpret the findings.

The strength of this study is the data showing that Pfdn5 localizes to axonal microtubules and the loss-of-function phenotypic analysis revealing disrupted synaptic bouton morphology. The major weakness relates to the experiments and claims of interactions with Tau-mediated neurodegeneration. 

In particular, it is unclear whether knockdown of Pfdn5 may cause eye phenotypes independent of Tau. 

Our new experiments confirm that knockdown of Pfdn5 alone does not cause eye phenotypes.

Further, the GMR>tau phenotype appears to have been incorrectly utilized to examine agedependent, neurodegeneration.

In response, we have modulated and explained our conclusions in this regard as described later in our “rebuttal.”

This manuscript argues that its findings may be relevant to thinking about mechanisms and therapies applicable to tauopathies; however, this is premature given that many questions remain about the interactions from Drosophila, the detailed mechanisms remain unresolved, and absent evidence that Tau and Pfdn may similarly interact in the mammalian neuronal context. Therefore, this work would be strongly enhanced by experiments in human or murine neuronal culture or supportive evidence from analyses of human data.

The reviewer is correct that the impact would be greater if Pfdn5-Tau interactions were also examined in human tissue.   While we have not attempted these experiments ourselves, we hope that our observations will stimulate others to test the conservation of phenomena we describe. There are, however, several lines of circumstantial evidence from human Alzheimer’s disease datasets that implicate PFDN5 in disease pathology. For example, recent compilations and analyses of proteomic data show reductions of CCT components, TBCE, as well as Prefoldin subunits, including PFDN5, in AD tissue (HSIEH et al. 2019; TAO et al. 2020; JI et al. 2022; ASKENAZI et al. 2023; LEITNER et al. 2024; SUN et al. 2024). Furthermore, whole blood mRNA expression data from Alzheimer's patients revealed downregulation of PFDN5 transcript (JI et al. 2022). Together, these findings from human data are consistent with the roles of PFDN5 in suppressing diverse neurodegenerative processes. We have incorporated these points into the discussion section of the revised manuscript.

Reviewer #1 (Recommendations for the authors):

See public review for experimental recommendations focusing on the Tau Pfdn interactions.  I would refrain from using the word aggregates, I would call them puncta, unless there is molecular or visual (ie AFM) evidence that they are indeed insoluble aggregates.  Finally, although including the full genotypes written out below the axis in the bar graphs is appreciated, it nevertheless makes them difficult to read due to crowding in most cases and somewhat distracting from the figure. 

In my opinion, a more reader-friendly manner of reporting the phenotypes will be highly helpful. For example, listing each component of the genotype on the left of each bar graph and adding a cross or a filled circle under the bar to inform of the full genotype of the animals used.

As described in the response to the previous comment, we now have strong direct evidences to support our view that the observed puncta are stable Tau aggregates. Thus, we feel justified to use the term Tau-aggregates in preference to Tau puncta. 

We have tried to write the genotypes to make them more reader-friendly.

Reviewer #2 (Recommendations for the authors):

(1) Lines 119-121: 35 modifiers from 64 seem like an unusually high hit rate. Are these individual genes or lines? Were all modifiers supported by at least 2 independent RNAi strains targeting non-overlapping sequences? A supplemental table should be included detailing all genes and specific strains tested, with corresponding results.

We agree with the reviewer that 35 modifiers from 64 genes may be too high. However, since the genes knocked down in the study are chaperones, crucial for maintaining proteostasis, we may have got unusually high hits. The information related to individual genes and lines is provided in Supplemental Table 1. We have now included an additional Supplemental Table 3, which lists the genes and the RNAi lines used in Figure 1, detailing the sequence target information. The table also specifies the number of independent RNAi strains used and the corresponding results. 

(2) Figure 1: The authors quantify the areas of ommatidial fusion and necrosis as degeneration, but it is difficult to appreciate the aberrations in the photos provided. Was any consideration given to also quantifying eye size?

We have processed the images to enhance their contrast and make the aberrations clearer. The percentage of degenerated eye area (Figure 1M) was normalized with total eye area. The method for quantifying degenerated area has been explained in the materials and methods section.

(3) Figure 1: a) Only enhancers of rough eyes are shown but no controls are included to evaluate whether knockdown of these genes causes eye toxicity in the absence of Tau. These are important missing controls. All putative Tau enhancers, including Pdn5/6, need to be tested with GMR-GAL4 independently of Tau to determine whether they cause a rough eye. In a previous publication from some of the same investigators (Raut et al 2017), knockdown of Pfdn using eyGAL4 was shown to induce severe eye morphology defects - this raises questions about the results shown here. 

We agree that assessing the effects of HSP knockdown independent of Tau is essential to confirm modifier specificity. We have now performed these knockdowns, and the data are reported in Supplemental Table 1. For RNAi lines represented in Figure 1, which enhanced Tau-induced degeneration/eye developmental defect, except for one of the RNAi lines against Pfdn6 (GD34204), no detectable eye defects were observed when knocked down with GMR-Gal4 at 25°C, suggesting that enhancement is specific to the Tau background. 

Use of a more eye-specific GMR-Gal4 driver at 25°C versus broader expressing ey-Gal4 at 29°C in prior work (Raut et al. 2017) likely reflects the differences in the eye morphological defects.

(b) Besides RNAi, do the classical Pdn5 deletion alleles included in this work also enhance the tau rough eye when heterozygous? Please also consider moving the Pfdn5/6 overexpression studies to evaluate possible suppression of the Tau rough eye to Figure 1, as it would enhance the interpretation of these data (but see also below).

GMR-Gal4 driven expression of hTau^V337M or hTau^WT in Pfdn5 heterozygous background does not enhance rough eye phenotype. 

(4) For genes of special interest, such as Pdn5, and other genes mentioned in the results, the main figure, or discussion, it is also important to perform quantitative PCR to confirm that the RNAi lines used actually knock down mRNA expression and by how much. These studies will establish specificity.

We agree that confirming RNAi efficiency via quantitative PCR (qPCR) is essential for validating the knockdown efficiency. We have now included qPCR data, especially for key modifiers, confirming effective knockdown (Figure S2).

(5) Lines 235-238: how do you conclude whether the tau phenotype is "enhanced" when Pfdn5 causes a similar phenotype on its own? Could the combination simply be additive? Did overexpression of Pdn5 suppress the UAS-hTau NMJ bouton phenotype (see below)? 

Although Pfdn5 mutants and hTau expression individually increase satellite boutons, their combination leads to a significantly more severe and additional phenotype, such as significantly decreased bouton size and increased bouton number, indicating an enhancing rather than purely additive interaction (Figure 4 and Figure S6C). Moreover, we now show that overexpression of Pfdn5 significantly suppressed the hTau^V337M-induced NMJ phenotypes. This new data has been incorporated as Figure S11F-L in the revised manuscript. 

Alternatively, did the authors consider reducing fly tau in the Pdn5 mutant background?

In new additional experiments, we observe that double mutants for Drosophila Tau (dTau) and Pfdn5 also exhibit severe NMJ defects, suggesting genetic interactions between dTau and Pfdn5. This data is shown below for the reviewer.

Author response image 1.

A double mutant combination of dTau and Pfdn5 aggravates the synaptic defects at the Drosophila NMJ. (A-D') Confocal images of NMJ synapses at muscle 4 of A2 hemisegment showing synaptic morphology in (A-A') control, (B-B') ΔPfdn5<SUP>15/40</SUP>, (C-C') dTauKO/dTauKO (Drosophila Tau mutant), (D-D') dTauKO/dTauKO; ∆Pfdn5<SUP>15/40</SUP> double immunolabeled for HRP (green), and CSP (magenta). The scale bar in D for (A-D') represents 10 µm. 

(6) It may be important to further extend the investigation to the actin cytoskeleton. It is noted that Pfdn5 also stabilizes actin. Importantly, tau-mediated neurodegeneration in Drosophila also disrupts the actin cytoskeleton, and many other regulators of actin modify tau phenotypes.

We appreciate the suggestion to examine the actin cytoskeleton. While prior studies indicate that Pfdn5 might regulate the actin cytoskeleton and that Tau^V377M hyperstabilizes the actin cytoskeleton, we did not observe altered actin levels in Pfdn5 mutants (Figure 2G). However, actin dynamics may represent an additional mechanism through which Pfdn5 might temporally influence Tauopathy. Future work will address potential actin-related mechanisms in Tauopathy.

(7) Figure 2: in the provided images, it is difficult to appreciate the futsch loops. Please include an image with increased magnification. It appears that fly strains harboring a genomic rescue BAC construct are available for Pfdn-this would be a complementary reagent to test besides Pfdn overexpression.

We have updated Figure 2 to include high magnification NMJ images as insets, clearly showing the Futsch loops. While we have not yet tested a genomic rescue BAC construct for Pfdn5, we plan to use the fly line harboring this construct in future work.

(8) Figure 3: Some of the data is not adequately explained. The use of Ran as a loading control seems rather unusual. What is the justification? Pfdn appears to only partially co-localize with a-tubulin in the axon; can the authors discuss or explain this? Further, in Pfdn5 mutants, there appears to be a loss of a-tubulin staining (3b'); this should also be discussed.

We appreciate the reviewer's concern regarding the choice of loading control for our Western blot analysis. Importantly, since Tubulin levels and related pathways were the focus of our analysis, traditional loading controls such as α- or β-tubulin or actin were deemed unsuitable due to potential co-regulation. Ran, a nuclear GTPase involved in nucleocytoplasmic transport, is not known to be transcriptionally or post-translationally regulated by Tubulin-associated signaling pathways. To ensure its reliability as a loading control, we confirmed by densitometric analysis that Ran expression showed minimal variability across all samples. Hence, we used Ran for accurate normalization in the Western blot data represented in this manuscript. We have also used GAPDH as a loading control and found no difference with respect to Ran as a loading control across samples.

We appreciate the reviewer's comment regarding the interpretation of our Pearson's correlation coefficient (PCC) results. While the mean colocalization value of 0.6 represents a moderate positive correlation (MUKAKA 2012), which may not reach the conventional threshold for "high positive" colocalization (usually considered 0.7-0.9), it nonetheless indicates substantial spatial overlap between the proteins of interest. Importantly, colocalization analysis provides supportive but indirect evidence for molecular proximity.  To further validate the interaction, we performed a microtubule binding assay, which directly demonstrates the binding of Pfdn5 to stabilized microtubules.

In accordance with the western blot analysis shown in Figure 2G-I, the levels of Tubulin are reduced in the Pfdn5 mutants (Figure 3B''). We have incorporated and discussed this in the revised manuscript.

(9) Figure 4: Overexpression of Pfdn appears to rescue the supernumerary satellite bouton numbers induced by human Tau; however, interpretation of this experiment is somewhat complicated as it is performed in Pfdn mutant genetic background. Can overexpression of Pfdn on its own rescue the Tau bouton defect in an otherwise wildtype background?

We have now coexpressed Pfdn5 and hTau<SUP>V337M</SUP> in an otherwise wild-type background. As shown in Figure S11F-L, Pfdn5 overexpression suppresses Tau-induced bouton defects. We have incorporated the data in the Results section to support the role of Pfdn5 as a modifier of Tau toxicity.

(10) Lines 256-263 / Figure 5: (a) What exactly are these tau-positive structures (punctae) being stained in larval brains in Fig 5C-E? Most prior work on tau aggregation using Drosophila models has been done in the adult brain, and human wildtype or mutant Tau is not known to form significant numbers of aggregates in neurons (although aggregates have been described following glia tau expression). 

Therefore, the results need to be further clarified. Besides the provided schematic, a zoomed-out image showing the whole larval brain is needed here for orientation. Have these aggregates been previously characterized in the literature? 

We agree with the reviewer that the expression of the wildtype or mutant form of human Tau in Drosophila is not known to form aggregates in the larval brain, in contrast to the adult brain (JACKSON et al. 2002; OKENVE-RAMOS et al. 2024). Consistent with previous reports, we also observed that Tau expression on its own does not form aggregates in the Drosophila larval brain.

However, in the absence of Pfdn5, microtubule disruption is severe, leading to reduced Taumicrotubule binding and formation of globular/round or flame-shaped tangles like aggregates in the larval brain. Previous studies have reported that 1,6-hexanediol can dissolve the Tau aggregate seeds formed by Tau droplets, but cannot dissolve the stable Tau aggregates (WEGMANN et al. 2018). We observed that 5% 1,6-Hexanediol failed to dissolve these Tau puncta, demonstrating the formation of stable aggregates in the absence of Pfdn5. Additionally, we now performed a Tau solubility assay and show that in the absence of Pfdn5, a significant amount of Tau goes in the pellet fraction, which could not be detected by phospho-specific AT8 Tau antibody (targeting pSer202/pThr205) but was detected by total hTau antibody (D5D8N) on the western blots (Figure S8). These data further reinforce our conclusion that  Pfdn5 prevents the transition of hTau from soluble and/or microtubule-associated state to an aggregated, insoluble, and pathogenic state. These new data have been incorporated into the revised manuscript.

(b) Can additional markers (nuclei, cell membrane, etc.) be used to highlight whether the taupositive structures are present in the cell body or at synapses?

We performed the co-staining of Tau and Elav to assess the aggregated Tau localization. We found that in the presence of Pfdn5, Tau is predominantly cytoplasmic and localised to the cell body and axons. In the absence of Pfdn5, Tau forms aggregates but is still localized to the cell body or axons. However, some of the aggregates are very large, and the subcellular localization could not be determined (Figure S8M-N'). These might represent brain regions of possible nuclear breakdown and cell death (JACKSON et al. 2002).

(c) It would also be helpful to perform western blots from larval (and adult) brains examining tau protein levels, phospho-tau species, possible higher-molecular weight oligomeric forms, and insoluble vs. soluble species. These studies would be especially important to help interpret the potential mechanisms of observed interactions.

Western blot analysis revealed that overexpression of Pfdn5 does not alter total Tau levels (Figure 6O). In Pfdn5 mutants, however, hTau^V337M levels were reduced in the supernatant fraction and increased in the pellet fraction, indicating a shift from soluble monomeric Tau to aggregated Tau.

(d) Does overexpression of Pdn5 (UAS-Pdn5) suppress the formation of tau aggregates? I would therefore recommend that additional experiments be performed looking at adult flies (perhaps in Pfdn5 heterozygotes or using RNAi due to the larval lethality of Pdn5 null animals).

Overexpression of Pfdn5 significantly reduced Tau-aggregates (Elav-Gal4/UASTau^V337M; UAS-Pfdn5; DPfdn5^15/40) observed in Pfdn5 mutants (Figure 5E). Coexpression of Pfdn5 and hTau^V337M suppresses the Tau aggregates/puncta in 30-day adult brain. Since heterozygous DPfdn¹⁵/+ did not show a reduction in Pfdn5 levels, we did not test the suppression of Tau aggregates in  DPfdn¹⁵/+; Elav>UAS-Pfdn5, UAS-Tau^V337M.

(11) Figure 6, panels A-N: The GMR>Tau rough eye is not a "neurodegenerative" but rather a predominantly developmental phenotype. It results from aberrant retinal developmental patterning and the subsequent secretion/formation of the overlying eye cuticle (lenslets). I am confused by the data shown suggesting a "shrinking eye size" and increasing roughened surface over time (a GMR>tau eye similar to that shown in panel B cannot change to appear like the one in panel H with aging). The rough eye can be quite variable among a population of animals, but it is usually fixed at the time the adult fly ecloses from the pupal case, and quite stable over time in an individual animal. Therefore, any suppression of the Tau rough eye seen at 30 days should be appreciable as soon as the animals eclose. These results need to be clarified. If indeed there is robust suppression of Tau rough eye, it may be more intuitive and clearer to include these data with Figure 1, when first showing the loss-of-function enhancement of the Tau rough eye. Also, why is Pfdn6 included in these experiments but not in the studies shown in Figures 2-5?

We thank the reviewer for their careful and knowledgeable assessment of the GMR>Tau rough eye model. We appreciate the clarification that the rough eye phenotype could be “developmental” rather than neurodegenerative.”  Our initial observations regarding "shrinking eye size" and "increased surface roughness" clearly show age-related progression of structural change.   Such progression has been observed and reported by others (IIJIMA-ANDO et al. 2012; PASSARELLA AND GOEDERT 2018).   We observed an age-dependent increase in the number of fused ommatidia in GMR-Gal4 >Tau, which were rescued by Pfdn5 or Pfdn6 expression. We noted that adult-specific induction of hTau^V337M adult flies using the Gal80^ts and GMR-GeneSwitch (GMR-GS) systems was not sufficient to induce a significant eye phenotype; thus, early expression of Tau in the developing eye imaginal disc appears to be required for the adult progressive phenotype that we observe. We feel that it is inadequate to refer to this adult progressive phenotype as “developmental,” and while admittedly arguable whether this can be termed “degenerative.”   

To address neurodegeneration more directly, we focused on 30-day-old adult fly brains and demonstrated that Pfdn5 overexpression suppresses age-dependent Tau-induced neurodegeneration in the central nervous system (Figure 6H-N and Figure S12). This supports our central conclusion regarding the neuroprotective role of Pfdn5 in age-associated Tau pathology. Since we found an enhancement in the Tau-induced synaptic and eye phenotypes by Pfdn6 knockdown, we also generated CRISPR/Cas9-mediated loss-of-function mutants for Pfdn6. However, loss of Pfdn6 resulted in embryonic/early first instar lethality, which precluded its detailed analysis at the larval stages.

(12) Figure 6, panels O-T: the elav>tau image appears to show a different frontal section plane compared to the other panels. It is advisable to show images at a similar level in all panels since vacuolar pathology can vary by region. It is also useful to be able to see the entire brain at a lower power, but the higher power inset view is obscuring these images. I would recommend creating separate panels rather than showing them as insets.

In the revised figure, we now display the low- and high-magnification images as separate, clearly labeled panels instead of using insets. This improves visibility of the brain morphology while providing detailed views of the vacuolar pathology (Figure 6H-L).

(13) Figure 6/7: For the experiments in which Pfdn5/6 is overexpressed and possibly suppresses tau phenotypes (brain vacuoles and memory), it is important to use controls that normalize the number of UAS binding sites, since increased UAS sites may dilute GAL4 and reduced Tau expression levels/toxicity. Therefore, it would be advisable to compare with Elav>Tau flies that also include a chromosome with an empty UAS site or other transgenes, such as UAS-GFP or UAS-lacZ.

We thank the reviewer for the suggestion. Now we have incorporated proper controls in the brain vacuolization, the mushroom body, and ommatidial fusion rescue experiments. Also, we have independently verified whether Gal4 dilution has any effect on the Tau phenotypes (Figure 6H-L, Figure 7, and Figure S11A-B).

(14) Lines 311-312: the authors say vacuolization occurs in human neurodegenerative disease, which is not really true to my knowledge and definitely not stated in the citation they use. Please re-phrase.

Now we have made the appropriate changes in the revised manuscript.

(15) Figure 7: The authors claim that Pfdn5/6 expression does not impact memory behavior, but there in fact appears to be a decrease in preference index (panel D vs panel B). Does this result complicate the interpretation of the potential interaction with Tau (panel F). Are data from wildtype control flies available?

In our memory assay, a decrease in performance index (PI) of the trained flies compared to the naïve flies indicates memory formation (normal memory in control flies, Figure 7B). In contrast, a lack of significant difference in PI indicates a memory defect (Figure 7C: hTau^V337M overexpressed flies). "Decrease in preference index (panel D vs panel B)" is not a sign of memory defect; it may be interpreted as a better memory instead. Hence, neuronal overexpression of Pfdn5 (Figure 7D) or Pfdn6 (Figure 7E) in wildtype neurons does not cause memory deficits. In addition, coexpression of Pfdn5/6 and hTau^V337M successfully rescues the Tau-induced memory defect (significant drop in PI compared to the PI of naïve flies in Figure 7F-G). Moreover, almost complete rescue of the Tau-induced mushroom body defect on Pfdn5 or Pfdn6 expression further establishes potential interaction between Pfdn5/6 and Tau. This data has been incorporated into the revised manuscript.

The memory assay itself with extensive data on wildtype flies and various other genotype will shortly be submitted for publication in another manuscript (Majumder et al, manuscript under preparation); However, we can confirm for the reviewer that wildtype flies, trained and assayed by the protocol described, show a significant decrease in performance index compared to the naïve flies, indicative of strong learning and memory performance, very similar to the control genotype data shown in Figure 7B. 

Additional minor considerations

(16) Lines 50-52: there are many therapeutic interventions for treating tauopathies, but not curative or particularly effective ones.

Now we have made the appropriate changes in the revised manuscript.

(17) Lines 87-106 seem like a duplication of the abstract. Consider deleting or condensing.

We have made the appropriate changes in the revised manuscript.

(18) Where is pfdn5 expressed? Development v. adult? Neuron v. glia? Conservation?

Prefoldin5 is expressed throughout development but strongly localized to the larval trachea and neuronal axons. Drosophila Pfdn5 shows 35% overall identity with human PFDN5. 

(19) Liine 187: is pfdn5 truly "novel"?

The role of Pfdn5 as microtubule-binding and stabilizing is a new finding and has not been predicted or described before. Hence, it is a novel neuronal microtubule-associated protein.  

(20) Figure 5, panel F, genotype labels on the x-axis are confusing; consider simplifying to Control, DPfdn, and Rescue.

We have made appropriate changes in the figure for better readability.

(21) Figures 5/8: it might be preferable to use consistent colors for Tau/HRP--Tau is labeled green in Figure 5 and then purple in Figure 8.

We have made these changes where possible. 

(22) Lines 311-312: Vacuolar neuropathology is NOT typically observed in human Tauopathy.

We thank the reviewer for pointing this out. We have made the appropriate changes in the revised manuscript.

(23) Lines 328-349: The explanation could be made more clear. Naïve flies should not necessarily be called controls. Also, a more detailed explanation of how the preference index is computed would be helpful. Why are some datapoints negative values?

(a) We have rewritten this paragraph to make the description and explanation clearer. The detailed method and formula to calculate the Preference index have been incorporated in the Materials and Methods section.

(b) We have replaced the term Control with Naïve. 

(c) Datapoints with negative values appeared in some of the 'Trained' group flies. It indicates that post-CuSO₄ training, some groups showed repulsion towards the otherwise attractive odor 2,3B. As 2,3B is an attractive odorant, naïve or control flies show attraction towards it compared to air, which is evident from a higher number of flies in the Odor arm (O) compared to that of the Air arm (A) of the Y-maze; thus, the PI [(O-A/O+A)*100] is positive in case of naïve fly groups. Training of the flies led to an association of the attractive odorant with bitter food, leading to a decrease of attraction, and even repulsion towards the odorant in a few instances, resulting in less fly count in the odor arm compared to the air arm. Hence, the PI becomes negative as (O-A) is negative in such instances. Thus, it is not an anomaly but indicates strong learning. 

(24) Line 403: misspelling "Pdfn"

We have corrected this.

(25) Lines 423-425: recommend re-phrasing, since tauopathies are human diseases. Mice and other animal models may be susceptible to tau-mediated neuronal dysfunction but not Tauopathy, per see.

We have made the appropriate changes in the revised manuscript.

(26) Lines 468-469: "tau neuropathology" rather than "tau associated neuropathies".

We have made the appropriate changes in the revised manuscript. 

References

Askenazi, M., T. Kavanagh, G. Pires, B. Ueberheide, T. Wisniewski et al., 2023 Compilation of reported protein changes in the brain in Alzheimer's disease. Nat Commun 14: 4466.

Hsieh, Y. C., C. Guo, H. K. Yalamanchili, M. Abreha, R. Al-Ouran et al., 2019 Tau-Mediated Disruption of the Spliceosome Triggers Cryptic RNA Splicing and Neurodegeneration in Alzheimer's Disease. Cell Rep 29: 301-316 e310.

Iijima-Ando, K., M. Sekiya, A. Maruko-Otake, Y. Ohtake, E. Suzuki et al., 2012 Loss of axonal mitochondria promotes tau-mediated neurodegeneration and Alzheimer's disease-related tau phosphorylation via PAR-1. PLoS Genet 8: e1002918.

Jackson, G. R., M. Wiedau-Pazos, T. K. Sang, N. Wagle, C. A. Brown et al., 2002 Human wildtype tau interacts with wingless pathway components and produces neurofibrillary pathology in Drosophila. Neuron 34: 509-519.

Ji, W., K. An, C. Wang and S. Wang, 2022 Bioinformatics analysis of diagnostic biomarkers for Alzheimer's disease in peripheral blood based on sex differences and support vector machine algorithm. Hereditas 159: 38.

Leitner, D., G. Pires, T. Kavanagh, E. Kanshin, M. Askenazi et al., 2024 Similar brain proteomic signatures in Alzheimer's disease and epilepsy. Acta Neuropathol 147: 27.

Li, L., Y. Jiang, G. Wu, Y. A. R. Mahaman, D. Ke et al., 2022 Phosphorylation of Truncated Tau Promotes Abnormal Native Tau Pathology and Neurodegeneration. Mol Neurobiol 59: 6183-6199.

Mershin, A., E. Pavlopoulos, O. Fitch, B. C. Braden, D. V. Nanopoulos et al., 2004 Learning and memory deficits upon TAU accumulation in Drosophila mushroom body neurons. Learn Mem 11: 277-287.

Mukaka, M. M., 2012 Statistics corner: A guide to appropriate use of correlation coefficient in medical research. Malawi Med J 24: 69-71.

Okenve-Ramos, P., R. Gosling, M. Chojnowska-Monga, K. Gupta, S. Shields et al., 2024 Neuronal ageing is promoted by the decay of the microtubule cytoskeleton. PLoS Biol 22: e3002504.

Passarella, D., and M. Goedert, 2018 Beta-sheet assembly of Tau and neurodegeneration in Drosophila melanogaster. Neurobiol Aging 72: 98-105.

Sun, Z., J. S. Kwon, Y. Ren, S. Chen, C. K. Walker et al., 2024 Modeling late-onset Alzheimer's disease neuropathology via direct neuronal reprogramming. Science 385: adl2992.

Tao, Y., Y. Han, L. Yu, Q. Wang, S. X. Leng et al., 2020 The Predicted Key Molecules, Functions, and Pathways That Bridge Mild Cognitive Impairment (MCI) and Alzheimer's Disease (AD). Front Neurol 11: 233.

Wegmann, S., B. Eftekharzadeh, K. Tepper, K. M. Zoltowska, R. E. Bennett et al., 2018 Tau protein liquid-liquid phase separation can initiate tau aggregation. EMBO J 37.

eLife Assessment

In this valuable study, the authors used an elegant genetic approach to delete EED at the post-neural crest induction stage. The usage of the single-cell RNA-seq analysis method is extremely suitable to determine changes in the cell type-specific gene expression during development. Results backed by solid evidence demonstrate that Eed is required for craniofacial osteoblast differentiation and mesenchymal proliferation after the induction of the neural crest.

Reviewer #2 (Public review):

Summary:

The role of PRC2 in post neural crest induction was not well understood. This work developed an elegant mouse genetic system to conditionally deplete EED upon SOX10 activation. Substantial developmental defects were identified for craniofacial and bone development. The authors also performed extensive single-cell RNA sequencing to analyze differentiation gene expression changes upon conditional EED disruption.

Strengths:

(1) Elegant genetic system to ablate EED post neural crest induction.

(2) Single-cell RNA-seq analysis is extremely suitable for studying the cell type specific gene expression changes in developmental systems.

Original Weaknesses:

(1) Although this study is well designed and contains state-of-art single cell RNA-seq analysis, it lacks the mechanistic depth in the EED/PRC2-mediated epigenetic repression. This is largely because no epigenomic data was shown.

(2) The mouse model of conditional loss of EZH2 in neural crest has been previously reported, as the authors pointed out in the discussion. What is novelty in this study to disrupt EED? Perhaps a more detailed comparison of the two mouse models would be beneficial.

(3) The presentation of the single-cell RNA-seq data may need improvement. The complexity of the many cell types blurs the importance of which cell types are affected the most by EED disruption.

(4) While it's easy to identify PRC2/EED target genes using published epigenomic data, it would be nice to tease out the direct versus indirect effects in the gene expression changes (e.g Fig. 4e)

Comments on latest version:

The authors have addressed weaknesses 2 and 3 of my previous comment very well. For weaknesses 1 and 4, the authors have added a main Fig 5 and its associated supplemental materials, which definitely strengthen the mechanistic depth of the story. However, I think the audience would appreciate if the following questions/points could be further addressed regarding the Cut&Tag data (mostly related to main Figure 5):

(1) The authors described that Sox10-Cre would be expressed at E8.75, and in theory, EED-FL would be ablated soon after that. Why would E16.5 exhibit a much smaller loss in H3K27me3 compared to E12.5? Shouldn't a prolong loss of EED lead to even worse consequence?

(2) The gene expression change at E12.5 upon loss of EED (shown in Fig. 4h) seems to be massive, including many PRC2-target genes. However, the H3K27me3 alteration seems to be mild even at E12.5. Does this infer a PRC2 or H3K27 methylation - independent role of EED? To address this, I suggest the authors re-consider addressing my previously commented weakness #4 regarding the RNA-seq versus Cut&Tag change correlation. For example, a gene scatter plot with X-axis of RNA-seq changes versus Y-axis of H3K27me3 level changes.

(3) The CUT&Tag experiments seem to contain replicates according to the figure legend, but no statistical analysis was presented including the new supplemental tables. Also, for Fig. 5c-d, instead of showing the MRR in individual conditions, I think the audience would really want to know the differential MRR between Fl/WT and Fl/Fl. In other words, how many genes/ MRR have statistically lower H3K27me3 level upon EED loss.

Author response:

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

Reviewer #1 (Public review):

Epigenetic regulation complex (PRC2) is essential for neural crest specification, and its misregulation has been shown to cause severe craniofacial defects. This study shows that Eed, a core PRC2 component, is critical for craniofacial osteoblast differentiation and mesenchymal proliferation after neural crest induction. Using mouse genetics and single-cell RNA sequencing, the researcher found that conditional knockout of Eed leads to significant craniofacial hypoplasia, impaired osteogenesis, and reduced proliferation of mesenchymal cells in post-migratory neural crest populations.

Overall, the study is superficial and descriptive. No in-depth mechanism was analyzed and the phenotype analysis is not comprehensive.

We thank the reviewer for sharing their expertise and for taking the time to provide helpful suggestions to improve our study. We are gratified that the striking phenotypes we report from Eed loss in post-migratory neural crest craniofacial tissues were appreciated. The breadth and depth of our phenotyping techniques, including skeletal staining, micro-CT, echocardiogram, immunofluorescence, histology, and primary craniofacial cell culture provide comprehensive data in support our hypothesis that PRC2 is required for epigenetic control of craniofacial osteoblast differentiation. To provide mechanistic data in support of this hypothesis, we have now performed CUT&Tag H3K27me3 chromatin profiling on nuclei harvested from E12.5 or E16.5 Sox10-Cre Eed^Fl/WT and Sox10-Cre Eed^Fl/Fl craniofacial tissue. These new data, which are presented in Fig. 5, Supplementary Fig. 9, and Supplementary Tables 7-10 of our revised manuscript, validate our hypothesis that epigenetic regulation of chromatin architecture downstream of PRC2 activity underlies craniofacial osteoblast differentiation. In particular, we now show that Eed-dependent H3K27me3 methylation is associated with correct temporal expression of transcription factors that are necessary for craniofacial differentiation and patterning, such as including Msx1, Pitx1, Pax7, which were initially nominated by single-cell RNA sequencing of E12.5 Sox10-Cre Eed^Fl/WT and Sox10-Cre Eed^Fl/Fl craniofacial tissues in Fig. 4, Supplementary Fig. 5-7, and Supplementary Tables 1-6.

Reviewer #2 (Public review):

Summary:

The role of PRC2 in post-neural crest induction was not well understood. This work developed an elegant mouse genetic system to conditionally deplete EED upon SOX10 activation. Substantial developmental defects were identified for craniofacial and bone development. The authors also performed extensive single-cell RNA sequencing to analyze differentiation gene expression changes upon conditional EED disruption.

Strengths:

(1) Elegant genetic system to ablate EED post neural crest induction.

(2) Single-cell RNA-seq analysis is extremely suitable for studying the cell type-specific gene expression changes in developmental systems.

We thank the reviewer for their generous and helpful comments on our study. We are happy that our mouse genetic and single-cell RNA sequencing approaches were appropriate in pairing the craniofacial phenotypes we report with distinct gene expression changes in post-migratory neural crest tissues upon Eed deletion.

Weaknesses:

(1) Although this study is well designed and contains state-of-the-art single-cell RNA-seq analysis, it lacks the mechanistic depth in the EED/PRC2-mediated epigenetic repression. This is largely because no epigenomic data was shown.

Thank you for this suggestion. As described in response to Reviewer #1, we have now performed CUT&Tag H3K27me3 chromatin profiling on nuclei harvested from E12.5 or E16.5 Sox10-Cre Eed^Fl/WT and Sox10-Cre Eed^Fl/Fl craniofacial tissues to provide mechanistic epigenomic data in support of our hypothesis that hat PRC2 is required for craniofacial osteoblast differentiation. These new data, which are presented in Fig. 5, Supplementary Fig. 9, and Supplementary Tables 7-10 of our revised manuscript, integrate genome-wide and targeted metaplot visualizations across genotypes with in-depth analyses of methylation rich regions and genes associated with methylation rich loci. Broadly, these new data reveal that changes in H3K27me3 occupancy correlate with gene expression changes from single-cell RNA sequencing of E12.5 Sox10-Cre Eed^Fl/WT and Sox10-Cre Eed^Fl/Fl craniofacial tissues in Fig. 4, Supplementary Fig. 5-7, and Supplementary Tables 1-6.

(2) The mouse model of conditional loss of EZH2 in neural crest has been previously reported, as the authors pointed out in the discussion. What is novel in this study to disrupt EED? Perhaps a more detailed comparison of the two mouse models would be beneficial.

We acknowledge and cite the study the reviewer has indicated (Schwarz et al. Development 2014) in our initial and revised manuscripts. This elegant investigation uses Wnt1-Cre to delete Ezh2 and reports a phenotype similar to the one we observed with Sox10-Cre deletion of Eed, but our study adds depth to the understanding of PRC2’s vital role in neural crest development by ablating Eed, which has a unique function in the PRC2 complex by binding to H3K27me3 and allosterically activating Ezh2. In this sense, our study sheds light on whether phenotypes arising from deletion of Eed, the PRC2 “reader”, differ from phenotypes arising from deletion of Ezh2, the PRC2 “writer”, in neural crest derived tissues. Moreover, we provide the first single-cell RNA sequencing and epigenomic investigations of craniofacial phenotypes arising from PRC2 activity in the developing neural crest. Due to limitations associated with the Wnt1-Cre transgene (Lewis et al. Developmental Biology 2013), which targets pre-migratory neural crest cells, our investigations used Sox10Cre, which targets the migratory neural crest and is completely recombined by E10.5. We have included a detailed comparison of these mouse models in the Discussion section of our revised manuscript, and we thank the reviewer for this thoughtful suggestion. 

(3) The presentation of the single-cell RNA-seq data may need improvement. The complexity of the many cell types blurs the importance of which cell types are affected the most by EED disruption.

We thank the reviewer for the opportunity to improve the presentation of our single-cell RNA sequencing data. In response, we have added Supplementary Fig. 8 to our revised manuscript, which shows the cell clusters most affected by EED disruption in UMAP space across genotypes. Because we wanted to capture the fill diversity of cell types underlying the phenotypes we report, we did not sort Sox10+ cells (via FACS, for example) from craniofacial tissues before single-cell RNA sequencing. Our resulting single-cell RNA sequencing data are therefore inclusive of a diversity of cell types in UMAP space, and the prevalence of many of these cell types was unaffected by epigenetic disruption of neural crest derived tissues. The prevalence of the cell clusters that are most affected across genotypes and which are most relevant to our analyses of the developing neural crest are shown in Fig. 4c (and now also in Supplementary Fig. 8), including C0 (differentiating osteoblasts), C4 (mesenchymal stem cells), C5 (mesenchymal stem cells), and C7 (proliferating mesenchymal stem cells). Marker genes and pseudobulked differential expression analyses across these clusters are shown in Fig. 4d and Fig. 4e-h, respectively. 

(4) While it's easy to identify PRC2/EED target genes using published epigenomic data, it would be nice to tease out the direct versus indirect effects in the gene expression changes (e.g Figure 4e).

We agree with the reviewer that the single-cell RNA sequencing data in our initial submission do not provide insight into direct versus indirect changes in gene expression downstream of PRC2. In contrast, the CUT&Tag chromatin profiling data that we have generated for this revision provides mechanistic insight into H3K27me3 occupancy and direct effects on gene expression resulting from PRC2 inactivation in our mouse models.

REVIEWING EDITOR COMMENTS

The following are recommended as essential revisions

(1) The study is overall superficial and primarily descriptive, lacking in-depth mechanistic analysis and comprehensive phenotype evaluation.

Please see responses to Reviewer #1 and Reviewer #2 (weaknesses 1 and 4) above. 

(2) The authors did not investigate the temporal and spatial expression of Eed during cranial neural crest development, which is crucial for explaining the observed phenotypes.

The temporal and spatial expression of Eed during embryogenesis is well studied. Eed is ubiquitously expressed starting at E5.5, peaks at E9.5, and is downregulated but maintained at a high basal expression level through E18.5 (Schumacher et al. Nature 1996). Although comprehensive analysis of Eed expression in neural crest tissues has not been reported (to our knowledge), Eed physically and functionally interacts with Ezh2 (Sewalt et al. Mol Cell Biol 1998), which is enriched at a diversity of timepoints throughout all developing craniofacial tissues (Schwarz et al. Development 2014). In our study, we confirmed enrichment of Eed expression in craniofacial tissues throughout development using QPCR, and have provided a more detailed description of these published and new findings in the Discussion section of our revised manuscript. 

(3) There is no apoptosis analysis provided for any of the samples.

We evaluated the presence of apoptotic cells in E12.5 craniofacial sections using immunofluorescence for Cleaved Caspase 3 in Supplementary Fig. 3d. Although we found a modest increase in the labeling index of apoptotic cells, there was insufficient evidence to conclude that apoptosis is a substantial factor in craniofacial hypoplasia resulting from Eed loss in post-migratory neural crest craniofacial tissues. We have clarified these findings in the Results and Discussion sections of our revised manuscript. 

(4) As Eed is a core component of the PRC2 complex, were any other components altered in the Eed cKO mutant? How does Eed regulation influence osteogenic differentiation and proliferation through known pathways?

We thank the editors for this thoughtful inquiry. Although we did not specifically investigate expression or stability of other PRC2 components in Eed conditional mutants, and little is known about how Eed regulates osteogenic differentiation or proliferation through any pathway, our single-cell RNA sequencing data presented in Fig. 4, Supplementary Fig. 5-7, and Supplementary Tables 1-6 provide a significant conceptual advance with mechanistic implications for understanding bone development downstream of Eed and do not reveal any alterations in the expression of other PRC2 components across genotypes. We have clarified these important details in the Discussion section of our revised manuscript. 

(5) The authors may compare the Eed cKO phenotype with that of the previous EZH2 cKO mouse model since both Eed and EZH2 are essential subunits of PRC2.

Please see responses to editorial comment 2 above and the last paragraph of the Discussion section of our revised manuscript for comparisons between Eed and Ezh2 knockout phenotypes.

eLife Assessment

This useful study explores the role of RAP2A in asymmetric cell division (ACD) regulation in glioblastoma stem cells (GSCs), drawing parallels to Drosophila ACD mechanisms and proposing that an imbalance toward symmetric divisions drives tumor progression. While findings on RAP2A's role in GSC expansion are promising, and the reviewers found the study innovative and technically solid, the study relies on neurosphere models without in vivo confirmation and will therefore need to be further validated in the future.

Reviewer #1 (Public review):

Summary:

The authors validate the contribution of RAP2A to GB progression. RAp2A participates in asymetric cell division, and the localization of several cell polarity markers including cno and Numb.

Strengths:

The use of human data, Drosophila models and cell culture or neurospheres is a good scenario to validate the hypothesis using complementary systems.

Moreover, the mechanisms that determine GB progression, and in particular glioma stem cells biology, are relevant for the knowledge on glioblastoma and opens new possibilities to future clinical strategies.

Weaknesses:

While the manuscript presents a well-supported investigation into RAP2A's role in GBM, some methodological aspects could benefit from further validation. The major concern is the reliance on a single GB cell line (GB5), including multiple GBM lines, particularly primary patient-derived 3D cultures with known stem-like properties, would significantly enhance the study's robustness.

Several specific points raised in previous reviews have improved this version of the manuscript:

• The specificity of Rap2l RNAi has been further confirmed by using several different RNAi tools.

• Quantification of phenotypic penetrance and survival rates in Rap2l mutants would help determine the consistency of ACD defects. The authors have substantially increased the number of samples analyzed including three different RNAi lines (both the number of NB lineages and the number of different brains analyzed) to confirm the high penetrance of the phenotype.

• The observations on neurosphere size and Ki-67 expression require normalization (e.g., Ki-67+ cells per total cell number or per neurosphere size). This is included in the manuscript and now clarified in the text.

• The discrepancy in Figures 6A and 6B requires further discussion. The authors have included a new analysis and further explanations and they can conclude that in 2 cell-neurospheres there are more cases of asymmetric divisions in the experimental condition (RAP2A) than in the control.

• Live imaging of ACD events would provide more direct evidence. Live imaging was not done due to technical limitations. Despite being a potential contribution to the manuscript, the current conclusions of the manuscript are supported by the current data, and live experiments can be dispensable

• Clarification of terminology and statistical markers (e.g., p-values) in Figure 1A would improve clarity. This has been improved.

Comments on revisions:

The manuscript has improved the clarity in general, and I think that it is suitable for publication. However, for future experiments and projects, I would like to insist in the relevance of validating the results in vivo using xenografts with 3D-primary patient-derived cell lines or GB organoids.

Reviewer #2 (Public review):

This study investigates the role of RAP2A in regulating asymmetric cell division (ACD) in glioblastoma stem cells (GSCs), bridging insights from Drosophila ACD mechanisms to human tumor biology. They focus on RAP2A, a human homolog of Drosophila Rap2l, as a novel ACD regulator in GBM is innovative, given its underexplored role in cancer stem cells (CSCs). The hypothesis that ACD imbalance (favoring symmetric divisions) drives GSC expansion and tumor progression introduces a fresh perspective on differentiation therapy. However, the dual role of ACD in tumor heterogeneity (potentially aiding therapy resistance) requires deeper discussion to clarify the study's unique contributions against existing controversies.

Comments on revisions:

More experiments as suggested in the original assessment of the submission are needed to justify the hypothesis drawn in the manuscript.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors validate the contribution of RAP2A to GB progression. RAp2A participates in asymmetric cell division, and the localization of several cell polarity markers, including cno and Numb.

Strengths:

The use of human data, Drosophila models, and cell culture or neurospheres is a good scenario to validate the hypothesis using complementary systems.

Moreover, the mechanisms that determine GB progression, and in particular glioma stem cells biology, are relevant for the knowledge on glioblastoma and opens new possibilities to future clinical strategies.

Weaknesses:

While the manuscript presents a well-supported investigation into RAP2A's role in GBM, several methodological aspects require further validation. The major concern is the reliance on a single GB cell line (GB5), which limits the generalizability of the findings. Including multiple GBM lines, particularly primary patient-derived 3D cultures with known stem-like properties, would significantly enhance the study's relevance.

Additionally, key mechanistic aspects remain underexplored. Further investigation into the conservation of the Rap2l-Cno/aPKC pathway in human cells through rescue experiments or protein interaction assays would be beneficial. Similarly, live imaging or lineage tracing would provide more direct evidence of ACD frequency, complementing the current indirect metrics (odd/even cell clusters, Numb asymmetry).

Several specific points require attention:

(1) The specificity of Rap2l RNAi needs further confirmation. Is Rap2l expressed in neuroblasts or intermediate neural progenitors? Can alternative validation methods be employed?

There are no available antibodies/tools to determine whether Rap2l is expressed in NB lineages, and we have not been able either to develop any. However, to further prove the specificity of the Rap2l phenotype, we have now analyzed two additional and independent RNAi lines of Rap2l along with the original RNAi line analyzed. We have validated the results observed with this line and found a similar phenotype in the two additional RNAi lines now analyzed. These results have been added to the text ("Results section", page 6, lines 142-148) and are shown in Supplementary Figure 3.

(2) Quantification of phenotypic penetrance and survival rates in Rap2l mutants would help determine the consistency of ACD defects.

In the experiment previously mentioned (repetition of the original Rap2l RNAi line analysis along with two additional Rap2l RNAi lines) we have substantially increased the number of samples analyzed (both the number of NB lineages and the number of different brains analyzed). With that, we have been able to determine that the penetrance of the phenotype was 100% or almost 100% in the 3 different RNAi lines analyzed (n>14 different brains/larvae analyzed in all cases). Details are shown in the text (page 6, lines 142-148), in Supplementary Figure 3 and in the corresponding figure legend.

(3) The observations on neurosphere size and Ki-67 expression require normalization (e.g., Ki-67+ cells per total cell number or per neurosphere size). Additionally, apoptosis should be assessed using Annexin V or TUNEL assays.

The experiment of Ki-67+ cells was done considering the % of Ki-67+ cells respect the total cell number in each neurosphere. In the "Materials and methods" section it is well indicated: "The number of Ki67+ cells with respect to the total number of nuclei labelled with DAPI within a given neurosphere were counted to calculate the Proliferative Index (PI), which was expressed as the % of Ki67+ cells over total DAPI+ cells"

Perhaps it was not clearly showed in the graph of Figure 5A. We have now changed it indicating: "% of Ki67+ cells/ neurosphere" in the "Y axis". 

Unfortunately, we currently cannot carry out neurosphere cultures to address the apoptosis experiments. 

(4) The discrepancy in Figures 6A and 6B requires further discussion.

We agree that those pictures can lead to confusion. In the analysis of the "% of neurospheres with even or odd number of cells", we included the neurospheres with 2 cells both in the control and in the experimental condition (RAP2A). The number of this "2 cell-neurospheres" was very similar in both conditions (27,7 % and 27 % of the total neurospheres analyzed in each condition), and they can be the result of a previous symmetric or asymmetric division, we cannot distinguish that (only when they are stained with Numb, for example, as shown in Figure 6B). As a consequence, in both the control and in the experimental condition, these 2-cell neurospheres included in the group of "even" (Figure 6A) can represent symmetric or asymmetric divisions. However, in the experiment shown in Figure 6B, it is shown that in these 2 cellneurospheres there are more cases of asymmetric divisions in the experimental condition (RAP2A) than in the control.

Nevertheless, to make more accurate and clearer the conclusions, we have reanalyzed the data taking into account only the neurospheres with 3-5-7 (as odd) or 4-6-8 (as even) cells. Likewise, we have now added further clarifications regarding the way the experiment has been analyzed in the methods.

(5) Live imaging of ACD events would provide more direct evidence.

We agree that live imaging would provide further evidence. Unfortunately, we currently cannot carry out neurosphere cultures to approach those experiments.

(6) Clarification of terminology and statistical markers (e.g., p-values) in Figure 1A would improve clarity.

We thank the reviewer for pointing out this issue. To improve clarity, we have now included a Supplementary Figure (Fig. S1) with the statistical parameters used. Additionally, we have performed a hierarchical clustering of genes showing significant or not-significant changes in their expression levels.

(7) Given the group's expertise, an alternative to mouse xenografts could be a Drosophila genetic model of glioblastoma, which would provide an in vivo validation system aligned with their research approach.

The established Drosophila genetic model of glioblastoma is an excellent model system to get deep insight into different aspects of human GBM. However, the main aim of our study was to determine whether an imbalance in the mode of stem cell division, favoring symmetric divisions, could contribute to the expansion of the tumor. We chose human GBM cell lines-derived neurospheres because in human GBM it has been demonstrated the existence of cancer stem cells (glioblastoma or glioma stem cells -GSCs--). And these GSCs, as all stem cells, can divide symmetric or asymmetrically. In the case of the Drosophila model of GBM, the neoplastic transformation observed after overexpressing the EGF receptor and PI3K signaling is due to the activation of downstream genes that promote cell cycle progression and inhibit cell cycle exit. It has also been suggested that the neoplastic cells in this model come from committed glial progenitors, not from stem-like cells.

With all, it would be difficult to conclude the causes of the potential effects of manipulating the Rap2l levels in this Drosophila system of GBM. We do not discard this analysis in the future (we have all the "set up" in the lab). However, this would probably imply a new project to comprehensively analyze and understand the mechanism by which Rap2l (and other ACD regulators) might be acting in this context, if it is having any effect. 

However, as we mentioned in the Discussion, we agree that the results we have obtained in this study must be definitely validated in vivo in the future using xenografts with 3D-primary patient-derived cell lines.

Reviewer #2 (Public review):

This study investigates the role of RAP2A in regulating asymmetric cell division (ACD) in glioblastoma stem cells (GSCs), bridging insights from Drosophila ACD mechanisms to human tumor biology. They focus on RAP2A, a human homolog of Drosophila Rap2l, as a novel ACD regulator in GBM is innovative, given its underexplored role in cancer stem cells (CSCs). The hypothesis that ACD imbalance (favoring symmetric divisions) drives GSC expansion and tumor progression introduces a fresh perspective on differentiation therapy. However, the dual role of ACD in tumor heterogeneity (potentially aiding therapy resistance) requires deeper discussion to clarify the study's unique contributions against existing controversies. Some limitations and questions need to be addressed.

(1) Validation of RAP2A's prognostic relevance using TCGA and Gravendeel cohorts strengthens clinical relevance. However, differential expression analysis across GBM subtypes (e.g., MES, DNA-methylation subtypes ) should be included to confirm specificity.

We have now included a Supplementary figure (Supplementary Figure 2), in which we show the analysis of RAP2A levels in the different GBM subtypes (proneural, mesenchymal and classical) and their prognostic relevance (i.e. the proneural subtype that presents RAP2A levels significantly higher than the others is the subtype that also shows better prognostic).

(2) Rap2l knockdown-induced ACD defects (e.g., mislocalization of Cno/Numb) are well-designed. However, phenotypic penetrance and survival rates of Rap2l mutants should be quantified to confirm consistency.

We have now analyzed two additional and independent RNAi lines of Rap2l along with the original RNAi line. We have validated the results observed with this line and found a similar phenotype in the two additional RNAi lines now analyzed. To determine the phenotypic penetrance, we have substantially increased the number of samples analyzed (both the number of NB lineages and the number of different brains analyzed). With that, we have been able to determine that the penetrance of the phenotype was 100% or almost 100% in the 3 different Rap2l RNAi lines analyzed (n>14 different brains/larvae analyzed in all cases). These results have been added to the text ("Results section", page 6, lines 142-148) and are shown in Supplementary Figure 3 and in the corresponding figure legend. 

(3) While GB5 cells were effectively used, justification for selecting this line (e.g., representativeness of GBM heterogeneity) is needed. Experiments in additional GBM lines (especially the addition of 3D primary patient-derived cell lines with known stem cell phenotype) would enhance generalizability.

We tried to explain this point in the paper (Results). As we mentioned, we tested six different GBM cell lines finding similar mRNA levels of RAP2A in all of them, and significantly lower levels than in control Astros (Fig. 3A). We decided to focus on the GBM cell line called GB5 as it grew well (better than the others) in neurosphere cell culture conditions, for further analyses. We agree that the addition of at least some of the analyses performed with the GB5 line using other lines (ideally in primary patientderive cell lines, as the reviewer mentions) would reinforce the results. Unfortunately, we cannot perform experiments in cell lines in the lab currently. We will consider all of this for future experiments.

(4) Indirect metrics (odd/even cell clusters, NUMB asymmetry) are suggestive but insufficient. Live imaging or lineage tracing would directly validate ACD frequency.

We agree that live imaging would provide further evidence. Unfortunately, we cannot approach those experiments in the lab currently.

(5) The initial microarray (n=7 GBM patients) is underpowered. While TCGA data mitigate this, the limitations of small cohorts should be explicitly addressed and need to be discussed.

We completely agree with this comment. We had available the microarray, so we used it as a first approach, just out of curiosity of knowing whether (and how) the levels of expression of those human homologs of Drosophila ACD regulators were affected in this small sample, just as starting point of the study. We were conscious of the limitations of this analysis and that is why we followed up the analysis in the datasets, on a bigger scale. We already mentioned the limitations of the array in the Discussion:

"The microarray we interrogated with GBM patient samples had some limitations. For example, not all the human genes homologs of the Drosophila ACD regulators were present (i.e. the human homologs of the determinant Numb). Likewise, we only tested seven different GBM patient samples. Nevertheless, the output from this analysis was enough to determine that most of the human genes tested in the array presented altered levels of expression"[....] In silico analyses, taking advantage of the existence of established datasets, such as the TCGA, can help to more robustly assess, in a bigger sample size, the relevance of those human genes expression levels in GBM progression, as we observed for the gene RAP2A."

(6) Conclusions rely heavily on neurosphere models. Xenograft experiments or patient-derived orthotopic models are critical to support translational relevance, and such basic research work needs to be included in journals.

We completely agree. As we already mentioned in the Discussion, the results we have obtained in this study must be definitely validated in vivo in the future using xenografts with 3D-primary patient-derived cell lines.

(7) How does RAP2A regulate NUMB asymmetry? Is the Drosophila Rap2l-Cno/aPKC pathway conserved? Rescue experiments (e.g., Cno/aPKC knockdown with RAP2A overexpression) or interaction assays (e.g., Co-IP) are needed to establish molecular mechanisms.

The mechanism by which RAP2A is regulating ACD is beyond the scope of this paper. We do not even know how Rap2l is acting in Drosophila to regulate ACD. In past years, we did analyze the function of another Drosophila small GTPase, Rap1 (homolog to human RAP1A) in ACD, and we determined the mechanism by which Rap1 was regulating ACD (including the localization of Numb): interacting physically with Cno and other small GTPases, such as Ral proteins, and in a complex with additional ACD regulators of the "apical complex" (aPKC and Par-6). Rap2l could be also interacting physically with the "Ras-association" domain of Cno (domain that binds small GTPases, such as Ras and Rap1). We have added some speculations regarding this subject in the Discussion:

"It would be of great interest in the future to determine the specific mechanism by which Rap2l/RAP2A is regulating this process. One possibility is that, as it occurs in the case of the Drosophila ACD regulator Rap1, Rap2l/RAP2A is physically interacting or in a complex with other relevant ACD modulators."

(8) Reduced stemness markers (CD133/SOX2/NESTIN) and proliferation (Ki-67) align with increased ACD. However, alternative explanations (e.g., differentiation or apoptosis) must be ruled out via GFAP/Tuj1 staining or Annexin V assays.

We agree with these possibilities.  Regarding differentiation, the potential presence of increased differentiation markers would be in fact a logic consequence of an increase in ACD divisions/reduced stemness markers. Unfortunately, we cannot approach those experiments in the lab currently.

(9) The link between low RAP2A and poor prognosis should be validated in multivariate analyses to exclude confounding factors (e.g., age, treatment history).

We have now added this information in the "Results section" (page 5, lines 114-123).

(10) The broader ACD regulatory network in GBM (e.g., roles of other homologs like NUMB) and potential synergies/independence from known suppressors (e.g., TRIM3) warrant exploration.

The present study was designed as a "proof-of-concept" study to start analyzing the hypothesis that the expression levels of human homologs of known Drosophila ACD regulators might be relevant in human cancers that contain cancer stem cells, if those human homologs were also involved in modulating the mode of (cancer) stem cell division. 

To extend the findings of this work to the whole ACD regulatory network would be the logic and ideal path to follow in the future.

We already mentioned this point in the Discussion:

"....it would be interesting to analyze in the future the potential consequences that altered levels of expression of the other human homologs in the array can have in the behavior of the GSCs. In silico analyses, taking advantage of the existence of established datasets, such as the TCGA, can help to more robustly assess, in a bigger sample size, the relevance of those human genes expression levels in GBM progression, as we observed for the gene RAP2A."

(11) The figures should be improved. Statistical significance markers (e.g., p-values) should be added to Figure 1A; timepoints/culture conditions should be clarified for Figure 6A.

Regarding the statistical significance markers, we have now included a Supplementary Figure (Fig. S1) with the statistical parameters used. Additionally, we have performed a hierarchical clustering of genes showing significant or notsignificant changes in their expression levels. 

Regarding the experimental conditions corresponding to Figure 6A, those have now been added in more detail in "Materials and Methods" ("Pair assay and Numb segregation analysis" paragraph).

(12) Redundant Drosophila background in the Discussion should be condensed; terminology should be unified (e.g., "neurosphere" vs. "cell cluster").

As we did not mention much about Drosophila ACD and NBs in the "Introduction", we needed to explain in the "Discussion" at least some very basic concepts and information about this, especially for "non-drosophilists". We have reviewed the Discussion to maintain this information to the minimum necessary.

We have also reviewed the terminology that the Reviewer mentions and have unified it.

Reviewer #1 (Recommendations for the authors):

To improve the manuscript's impact and quality, I would recommend:

(1) Expand Cell Line Validation: Include additional GBM cell lines, particularly primary patient-derived 3D cultures, to increase the robustness of the findings.

(2) Mechanistic Exploration: Further examine the conservation of the Rap2lCno/aPKC pathway in human cells using rescue experiments or protein interaction assays.

(3) Direct Evidence of ACD: Implement live imaging or lineage tracing approaches to strengthen conclusions on ACD frequency.

(4) RNAi Specificity Validation: Clarify Rap2l RNAi specificity and its expression in neuroblasts or intermediate neural progenitors.

(5) Quantitative Analysis: Improve quantification of neurosphere size, Ki-67 expression, and apoptosis to normalize findings.

(6) Figure Clarifications: Address inconsistencies in Figures 6A and 6B and refine statistical markers in Figure 1A.

(7) Alternative In Vivo Model: Consider leveraging a Drosophila glioblastoma model as a complementary in vivo validation approach.

Addressing these points will significantly enhance the manuscript's translational relevance and overall contribution to the field.

We have been able to address points 4, 5 and 6. Others are either out of the scope of this work (2) or we do not have the possibility to carry them out at this moment in the lab (1, 3 and 7). However, we will complete these requests/recommendations in other future investigations.

Reviewer #2 (Recommendations for the authors):

Major Revision /insufficient required to address methodological and mechanistic gaps.

(1) Enhance Clinical Relevance

Validate RAP2A's prognostic significance across multiple GBM subtypes (e.g., MES, DNA-methylation subtypes) using datasets like TCGA and Gravendeel to confirm specificity.

Perform multivariate survival analyses to rule out confounding factors (e.g., patient age, treatment history).

(2) Strengthen Mechanistic Insights

Investigate whether the Rap2l-Cno/aPKC pathway is conserved in human GBM through rescue experiments (e.g., RAP2A overexpression with Cno/aPKC knockdown) or interaction assays (e.g., Co-IP).

Use live-cell imaging or lineage tracing to directly validate ACD frequency instead of relying on indirect metrics (odd/even cell clusters, NUMB asymmetry).

(3) Improve Model Systems & Experimental Design

Justify the selection of GB5 cells and include additional GBM cell lines, particularly 3D primary patient-derived cell models, to enhance generalizability.

It is essential to perform xenograft or orthotopic patient-derived models to support translational relevance.

(5) Address Alternative Interpretations

Rule out other potential effects of RAP2A knockdown (e.g., differentiation or apoptosis) using GFAP/Tuj1 staining or Annexin V assays.

Explore the broader ACD regulatory network in GBM, including interactions with NUMB and TRIM3, to contextualize findings within known tumor-suppressive pathways.

(6) Improve Figures & Clarity

Add statistical significance markers (e.g., p-values) in Figure 1A and clarify timepoints/culture conditions for Figure 6A.

Condense redundant Drosophila background in the discussion and ensure consistent terminology (e.g., "neurosphere" vs. "cell cluster").

We have been able to address points 1, partially 3 and 6. Others are either out of the scope of this work or we do not have the possibility to carry them out at this moment in the lab. However, we are very interested in completing these requests/recommendations and we will approach that type of experiments in other future investigations.

eLife Assessment

This important study reveals that connexin43 (Cx43) hemichannels are directly activated by CO₂ through a conserved carbamylation motif, extending a mechanism previously described for β-connexins to α-connexins. The evidence is convincing, supported by complementary biochemical and electrophysiological analyses showing CO₂-induced hemichannel opening and ATP release in cultured cells and hippocampal slices. These findings advance our understanding of connexin regulation by metabolic gases and will be of broad interest to researchers studying cell communication, neural signaling, and gasotransmitter biology.

Reviewer #1 (Public review):

Summary:

This study builds on previous work demonstrating that several beta connexins (Cx26, Cx30 and Cx32) have a carbamylation motif which renders them sensitive to CO2. In response to CO2, hemichannels composed of these connexins open, enabling diffusion of small molecules (such as ATP) between the cytosol and extracellular environment. Here, the authors have identified that an alpha connexin, Cx43, also contains a carbamylation motif, and they demonstrate that CO2 opens Cx43 hemichannels. Most of the study involves using transfected cells expressing wild-type and mutant Cx43 to define amino acids required for CO2 sensitivity. Hippocampal tissue slices in culture were used to show that CO2-induced synaptic transmission was affected by Cx43 hemichannels, providing a physiological context. The authors point out that the Cx43 gene significantly diverges from the beta connexins that are CO2 sensitive, suggesting that the conserved carbamylation motif was present before the alpha and beta connexin genes diverged.

Strengths:

The molecular analysis defining the amino acids which contribute to the CO2 sensitivity of Cx43 is a major strength of the study. The rigor of analysis was strengthened by using three independent assays for hemichannel opening: dye uptake, patch clamp channel measurements and ATP secretion. The resulting analysis identified key lysines in Cx43 that were required for CO2-mediated hemichannel opening. A double K to E Cx43 mutant produced a construct that produced hemichannels that were constitutively open, which further strengthened the analysis.

Using hippocampal tissue sections to demonstrate that CO2 can influence field excitatory postsynaptic potentials (fEPSPs) provides a native context for CO2 regulation of Cx43 hemichannels. Cx43 mutations associated with Oculodentodigital Dysplasia (ODDD) inhibited CO2-induced hemichannel opening, although the mechanism by which this occurs was not elucidated.

Cytosolic pH was measured and it was further demonstrated that Cx43 hemichannels composed of untagged Cx43 are sensitive to CO2.

A molecular phylogenetic survey was performed which identified several other non-beta connexins that have a putative carbamylation motif. How this relates to connexin evolution was added to the discussion.

Weaknesses:

Cultured cells are typically grown in incubators containing 5% CO2 which is ~40 mmHg. Determining compensatory mechanisms that enable the cells to be viable if Cx43 hemichannels are open at this PCO2 would strengthen the study.

Experiments using Gap26 to inhibit Cx43 hemichannels in fEPSP measurements used a scrambled peptide as a control. Including gap peptides specifically targeting Cx26, Cx30 and Cx32 as additional controls would strengthen the study, since the tissue sections have a complex pattern of connexin expression.

Reviewer #2 (Public review):

Summary:

This paper examines the CO2 sensitivity of Cx43 hemichannels and gap junctional channels in transiently transfected Hela cells using several different assays including ethidium dye uptake, ATP release, whole cell patch clamp recordings and an imaging assay of gap junctional dye transfer. The results show that raising pCO2 from 20 to 70 mmHg (at a constant pH of 7.3) cause an increase in opening of Cx43 hemichannels but did not block Cx43 gap junctions. This study also showed that raising pCO2 from 20 to 35 mm Hg resulted in an increase in synaptic strength in hippocampal rat brain slices, presumably due to downstream ATP release, suggesting that the CO2 sensitivity of Cx43 may be physiologically relevant. As a further test of the physiological relevance of the CO2 sensitivity of Cx43, it was shown that two pathological mutations of Cx43 that are associated with ODDD caused loss of Cx43 CO2-sensitivity. Cx43 has a potential carbamylation motif that is homologous to the motif in Cx26. To understand the structural changes involved in CO2 sensitivity, a number of mutations were made in Cx43 sites thought to be the equivalent of those known to be involved in the CO2 sensitivity of Cx26 and the CO2 sensitivity of these mutants was investigated.

Strengths:

This study shows that the apparent lack of functional Cx43 hemichannels observed in a number of previous in vitro function studies may be due to the use of HEPES to buffer the external pH. When Cx43 hemichannels were studied in external solutions in which CO2/bicarbonate was used to buffer pH instead of HEPES, Cx43 hemichannels showed significantly higher levels of dye uptake, ATP release, and ionic conductance. These findings may have major physiological implications since Cx43 hemichannels are found in many organs throughout the body including the brain, heart and immune system.

Weaknesses:

Interpretation of the site-directed mutation studies is complicated. Although Cx43 has a potential carbamylation motif that is homologous to the motif in Cx26, the results of site-directed mutation studies were inconsistent with a simple model in which K144 and K105 interact following carbamylation to cause the opening of Cx43 hemichannels.

Secondly, although it is shown that two Cx43 ODDD associated mutations show a loss of CO2 sensitivity, there is no evidence that the absence of CO2 sensitivity is involved in the pathology of ODDD.

Reviewer #3 (Public review):

In this paper, authors aimed to investigate carbamylation effects on the function of Cx43-based hemichannels. Such effects have previously been characterized for other connexins, e.g. for Cx26, which display increased hemichannel (HC) opening and closure of gap junction channels upon exposure to increased CO2 partial pressure (accompanied by increased bicarbonate to keep pH constant). The authors used HeLa cells transiently transfected with Cx43 to investigate CO2-dependent carbamylation effects on Cx43 HC function. In contrast to Cx43-based gap junction channels that are here reported to be insensitive to PCO2 alterations, they provide evidence that Cx43 HC opening is highly dependent on the PCO2 pressure in the bath solution, over a range of 20 up to 70 mmHg encompassing the physiologically normal resting level of around 40 mmHg. They furthermore identified several Cx43 residues involved in Cx43 HC sensitivity to PCO2: K105, K109, K144 & K234; mutation of 2 or more of these AAs is necessary to abolish CO2 sensitivity. The subject is interesting and the results indicate that a fraction of HCs is open at a physiological 40 mmHg PCO2, which differs from the situation under HEPES buffered solutions where HCs are mostly closed under resting conditions. The mechanism of HC opening with CO2 gassing is linked to carbamylation and authors pinpointed several Lys residues involved in this process. Overall, the work is interesting as it shows that Cx43 HCs have a significant open probability under resting conditions of physiological levels of CO2 gassing, probably applicable to/relevant for brain, heart and other Cx43 expressing organs. The paper gives a detailed account on various experiments performed (dye uptake, electrophysiology, ATP release to assess HC function) and results concluded from those. They further consider many candidate carbamylation sites by mutating them to negatively charged Glu residues. The paper finalizes with hippocampal slice work showing evidence for connexin-dependent increases of the EPSP amplitude that could be inhibited by HC inhibition with Gap26 (Fig. 10). Another line of evidence comes from the Cx43-linked ODDD genetic disease whereby L90V as well as the A44V mutations of Cx43 prevented the CO2 induced hemichannel opening response (Fig. 11). Although the paper is interesting, in its present state it suffers from (i) a problematic Fig. 3, precluding interpretation of the data shown, and (ii) the poor use of hemichannel inhibitors that are necessary to strengthen the evidence in the crucial experiment of Fig. 2 and others.

Comments on revisions:

The traces in Fig.2B show that the HC current is inward at 20 mmHg PCO2, while it switches to an outward current at 55mmHg PCO2. HCs are non-selective channels, so their current should switch direction around 0 mV but not around -50 mV. As such, the -50 mV switching point indicates involvement of another channel distinct from non-selective Cx43 hemichannels. In the revised version, this problem has not been solved nor addressed. Additionally, I identified another problem in that the experimental traces shown lack a trace at the baseline condition of PCO2 35mmHg, while the summary graph depicts a data point. Not showing a trace at baseline PCO2 35mmHg renders data interpretation in the summary graph questionable.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

This study builds on previous work demonstrating that several beta connexins (Cx26, Cx30, and Cx32) have a carbamylation motif which renders them sensitive to CO₂. In response to CO₂, hemichannels composed of these connexins open, enabling diffusion of small molecules (such as ATP) between the cytosol and extracellular environment. Here, the authors have identified that an alpha connexin, Cx43, also contains a carbamylation motif, and they demonstrate that CO₂ opens Cx43 hemichannels. Most of the study involves using transfected cells expressing wildtype and mutant Cx43 to define amino acids required for CO₂ sensitivity. Hippocampal tissue slices in culture were used to show that CO₂-induced synaptic transmission was affected by Cx43 hemichannels, providing a physiological context. The authors point out that the Cx43 gene significantly diverges from the beta connexins that are CO₂ sensitive, suggesting that the conserved carbamylation motif was present before the alpha and beta connexin genes diverged. 

Strengths: 

(1) The molecular analysis defining the amino acids that contribute to the CO₂ sensitivity of Cx43 is a major strength of the study. The rigor of analysis was strengthened by using three independent assays for hemichannel opening: dye uptake, patch clamp channel measurements, and ATP secretion. The resulting analysis identified key lysines in Cx43 that were required for CO₂-mediated hemichannel opening. A double K to E Cx43 mutant produced a construct that produced hemichannels that were constitutively open, which further strengthened the analysis. 

(2) Using hippocampal tissue sections to demonstrate that CO₂ can influence field excitatory postsynaptic potentials (fEPSPs) provides a native context for CO₂ regulation of Cx43 hemichannels. Cx43 mutations associated with Oculodentodigital Dysplasia (ODDD) inhibited CO₂-induced hemichannel opening, although the mechanism by which this occurs was not elucidated. 

Weaknesses: 

(1) Cx43 channels are sensitive to cytosolic pH, which will be affected by CO₂. Cytosolic pH was not measured, and how this affects CO₂-induced Cx43 hemichannel activity was not addressed. 

We have now addressed this with intracellular pH measurements and removal of the C-terminal pH sensor from Cx43 -the hemichannel remains CO₂ sensitive.

(2) Cultured cells are typically grown in incubators containing 5% CO₂, which is ~40 mmHg. It is unclear how cells would be viable if Cx43 hemichannels are open at this PCO2. 

The cells look completely healthy with normal morphology and no sign of excessive cell death in the cultures. Presumably they have ways of compensating for the effects of partially open Cx43 hemichannels.

(3) Experiments using Gap26 to inhibit Cx43 hemichannels in fEPSP measurements used a scrambled peptide as a control. Analysis should also include Gap peptides specifically targeting Cx26, Cx30, and Cx32 as additional controls. 

We don’t feel this is necessary given the extensive prior literature in hippocampus showing the effect of ATP release via open Cx43 hemichannels on fEPSP amplitude that used astrocytic specific knockout of Cx43 and Gap26 (doi: 10.1523/jneurosci.0015-14.2014).

(4) The mechanism by which ODDD mutations impair CO2-mediated hemichannel opening was not addressed. Also, the potential roles for inhibiting Cx43 hemichannels in the pathology of ODDD are unclear. 

These pathological mutations that alter CO<SUB>2</SUB> sensitivity are similar to pathological mutation in Cx26 and Cx32, which also remove CO<SUB>2</SUB> sensitivity. Our cryo-EM studies on Cx26 give clues as to why these mutations have this effect -they alter conformational mobility of the channel (Brotherton et al 2022 doi: 10.1016/j.str.2022.02.010 and Brotherton et al 2024 doi: 10.7554/eLife.93686). We assume that similar considerations apply to Cx43, but this requires improved cryoEM structures of Cx43 hemichannels at differing levels of PCO<SUB>2</SUB>.

We agree that the link between loss of CO<SUB>2</SUB> sensitivity of Cx43 and ODDD is not established and have revised the text to make this clear.

(5) CO2 has no effect on Cx43-mediated gap junctional communication as opposed to Cx26 gap junctions, which are inhibited by CO2. The molecular basis for this difference was not determined. 

Cx26 gap junction channels are so far unique amongst CO<SUB>2</SUB> sensitive connexins in being closed by CO<SUB>2</SUB>. We have addressed the mechanism by which this occurs in Nijjar et al 2025 DOI: 10.1113/JP285885 -the requirement of carbamylation of K108 in Cx26 (in addition to K125) for GJC closure.

(6) Whether there are other non-beta connexins that have a putative carbamylation motif was not addressed. Additional discussion/analysis of how the evolutionary trajectory for Cx43 maintaining a carbamylation motif is unique for non-beta connexins would strengthen the study. 

We have performed a molecular phylogenetic survey to show that the carbamylation motif occurs across the alpha connexin clade and have shown that Cx50 is indeed CO<SUB>2</SUB> sensitive (doi: 10.1101/2025.01.23.634273). This is now in Fig 12.

Reviewer #2 (Public review): 

Summary: 

This paper examines the CO<SUB>2</SUB>  sensitivity of Cx43 hemichannels and gap junctional channels in transiently transfected Hela cells using several different assays, including ethidium dye uptake, ATP release, whole cell patch clamp recordings, and an imaging assay of gap junctional dye transfer. The results show that raising pCO₂ from 20 to 70 mmHg (at a constant pH of 7.3) causes an increase in opening of Cx43 hemichannels but does not block Cx43 gap junctions. This study also showed that raising pCO<SUB>2</SUB> from 20 to 35 mm Hg resulted in an increase in synaptic strength in hippocampal rat brain slices, presumably due to downstream ATP release, suggesting that the CO<SUB>2</SUB> sensitivity of Cx43 may be physiologically relevant. As a further test of the physiological relevance of the CO₂ sensitivity of Cx43, it was shown that two pathological mutations of Cx43 that are associated with ODDD caused loss of Cx43 CO₂-sensitivity. Cx43 has a potential carbamylation motif that is homologous to the motif in Cx26. To understand the structural changes involved in CO<SUB>2</SUB> sensitivity, a number of mutations were made in Cx43 sites thought to be the equivalent of those known to be involved in the CO<SUB>2</SUB> sensitivity of Cx26, and the CO<SUB>2</SUB> sensitivity of these mutants was investigated. 

Strengths: 

This study shows that the apparent lack of functional Cx43 hemichannels observed in a number of previous in vitro function studies may be due to the use of HEPES to buffer the external pH. When Cx43 hemichannels were studied in external solutions in which CO<SUB>2</SUB>/bicarbonate was used to buffer pH instead of HEPES, Cx43 hemichannels showed significantly higher levels of dye uptake, ATP release, and ionic conductance. These findings may have major physiological implications since Cx43 hemichannels are found in many organs throughout the body, including the brain, heart, and immune system. 

Weaknesses: 

(1) Interpretation of the site-directed mutation studies is complicated. Although Cx43 has a potential carbamylation motif that is homologous to the motif in Cx26, the results of site-directed mutation studies were inconsistent with a simple model in which K144 and K105 interact following carbamylation to cause the opening of Cx43 hemichannels. 

The mechanism of opening of Cx43 is more complex than that of Cx26, Cx32 and Cx50 and involves more Lys residues. The 4 Lys residues in Cx43 that are involved in opening the hemichannel have their equivalents in Cx26, but in Cx26 these additional residues seem to be involved in the closing of the GJC rather than opening of the hemichannel (see above). Cx50 is simpler and involves only two Lys residues (doi: 10.1101/2025.01.23.634273), which are equivalent to those in Cx26.

(2) Secondly, although it is shown that two Cx43 ODDD-associated mutations show a loss of CO₂ sensitivity, there is no evidence that the absence of CO2 sensitivity is involved in the pathology of ODD

We agree, but this is probably because this has not been directly tested by experiment, as the CO<Sub>2</sub> sensitivity of Cx43 was not previously known. As mentioned above we have revised the text to ensure that this is clear.

Reviewer #3 (Public review): 

In this paper, the authors aimed to investigate carbamylation effects on the function of Cx43-based hemichannels. Such effects have previously been characterized for other connexins, e.g., for Cx26, which display increased hemichannel (HC) opening and closure of gap junction channels upon exposure to increased CO₂ partial pressure (accompanied by increased bicarbonate to keep pH constant). 

The authors used HeLa cells transiently transfected with Cx43 to investigate CO₂ dependent carbamylation effects on Cx43 HC function. In contrast to Cx43-based gap junction channels that are reported here to be insensitive to PCO₂ alterations, they provide evidence that Cx43 HC opening is highly dependent on the PCO2 pressure in the bath solution, over a range of 20 up to 70 mmHg encompassing the physiologically normal resting level of around 40 mmHg. They furthermore identified several Cx43 residues involved in Cx43 HC sensitivity to PCO2: K105, K109, K144 & K234; mutation of 2 or more of these AAs is necessary to abolish CO₂ sensitivity. The subject is interesting and the results indicate that a fraction of HCs is open at a physiological 40 mmHg PCO₂, which differs from the situation under HEPES buffered solutions where HCs are mostly closed under resting conditions. The mechanism of HC opening with CO₂ gassing is linked to carbamylation, and the authors pinpointed several Lys residues involved in this process. 

Overall, the work is interesting as it shows that Cx43 HCs have a significant open probability under resting conditions of physiological levels of CO₂ gassing, probably applicable to the brain, heart, and other Cx43 expressing organs. The paper gives a detailed account of various experiments performed (dye uptake, electrophysiology, ATP release to assess HC function) and results concluded from those. They further consider many candidate carbamylation sites by mutating them to negatively charged Glu residues. The paper ends with hippocampal slice work showing evidence for connexin-dependent increases of the EPSP amplitude that could be inhibited by HC inhibition with Gap26 (Figure 10). Another line of evidence comes from the Cx43-linked ODDD genetic disease, whereby L90V as well as the A44V mutations of Cx43 prevented the CO₂-induced hemichannel opening response (Figure 11). Although the paper is interesting, in its present state, it suffers from (i) a problematic Figure 3, precluding interpretation of the data shown, and (ii) the poor use of hemichannel inhibitors that are necessary to strengthen the evidence in the crucial experiment of Figure 2 and others. 

The panels in Figure 3 were mislabelled in the accompanying legend possibly leading to some confusion. This has now been corrected.

We disagree that hemichannel blockers are needed to strengthen the evidence in Figure 2 and other figures. Our controls show that the CO₂-sensitive responses absolutely requires expression of Cx43 and was modified by mutations of Cx43. It is hard to see how this evidence would be strengthened by use of peptide inhibitors or other blockers of hemichannels that may not be completely selective.

Reviewing Editor Comments:

(1) Improve electrophysiological evidence, addressing concerns about the initial experiment and including peptide inhibitor data where applicable. 

We think the concerns about the electrophysiological evidence arise from a misunderstanding because we gave insufficient information about how we conducted the experiments. We have now provided a much more complete legend, added explanations in the text and given more detail in the Methods. We further respond to the reviewer below.

We do not agree on the necessity of the peptide inhibitor to demonstrate dependence on Cx43.  We have shown that parental HeLa cells do not release ATP to changes in PCO₂ or voltage (Fig 2D; Butler & Dale 2023, 10.3389/fncel.2023.1330983; Lovatt et al 2025, 10.1101/2025.03.12.642803, 10.1101/2025.01.23.634273). Our previous papers have shown many times that parental HeLa cells do not load with dye to CO₂ or zero Ca²⁺ (e.g. Huckstepp et al 2010, 10.1113/jphysiol.2010.192096; Meigh et al 2013, 10.7554/eLife.01213; Meigh et al 2014, 10.7554/eLife.04249), and we have shown that parental HeLa cells do not exhibit the same CO₂ dependent change in whole cell conductance that the Cx43-expressing cells do (Fig 2B). In addition, we shown that mutating key residues in Cx43 alters both CO₂-sensitive release of ATP and the CO₂-dependent dye loading without affecting the respective positive control. To bolster this, we have included data for the K144R mutation as a supplement to Fig 3. Given the expense of Gap26 it is impractical to include this as a standard control and unnecessary given the comprehensive controls outlined.

Collectively, these data show that the responses to CO₂ require expression of Cx43 and can be modified by mutation of Cx43.

(2) Strengthen the manuscript by measuring the effects of CO on cytosolic pH and Cx43 hemichannel opening. Consider using tail truncation mutants to assess the role of the C-terminal pH sensor in CO-mediated channel opening.

We agree and have performed the suggested experiments to address this issue.

(3) Investigate the effect of expressing the K105E/K109E Cx43 double mutant on cell viability.

In our experiments the cells look completely healthy based on their morphology in brightfield microscopy and growth rates. 

(4) Discuss and analyze the uniqueness of Cx43 among alpha connexins in maintaining the carbamylation motif.

now discuss this -Cx43 is not unique. We have added a molecular phylogenetic survey of the alpha connexin clade in Fig 12. Apart from Cx37, the carbamylation motif appears in all the other members of the clade (but not necessarily in the human orthologue). In a different MS, currently posted on bioRxiv, we have documented the CO₂ sensitivity of Cx50 and its dependence on the motif.

(5) Consider omitting data on ODDD-associated mutations unless there is evidence linking CO₂ sensitivity to disease pathology.

This experiment is observational, and we are not making claims that there is a direct causal link. Removing the ODDD mutant findings would lose potentially useful information for anyone studying how these mutations alter channel function. We have reworded the text to ensure that we say that the link between loss of CO₂ sensitivity and ODDD remains unproven.

(6) Justify the choice of high K^⁺ and low external calcium as a positive control in ATP release experiments.

These two manipulations can open the hemichannel independently of the CO₂ stimulus. Extracellular Ca²⁺ is well known to block all connexin hemichannels, and Cx43 is known to be voltage sensitive. The depolarisation from high K⁺ is effective at opening the hemichannel and we preferred this as a more physiological way of opening the Cx43 hemichannel. We have added some explanatory text.

(7) Clarify whether Cx43A44V or Cx43L90V mutations block gap junctional coupling.

This is an interesting point. Since Cx43 GJCs are not CO₂ sensitive we feel this is beyond the scope of our paper. 

(8) Discuss the potential implications of pCO₂ changes on myocardial function through alterations in intracellular pH.

We have modified the discussion to consider this point.

Reviewer #1 (Recommendations for the authors):

(1) Measurements of the effects of CO₂ on cytosolic pH/Cx43 hemichannel opening would strengthen the manuscript. Since the pH sensor of Cx43 is on the C terminus, the authors could consider making tail truncation mutants to see how this affects CO₂-mediated Cx43 channel opening.

We have done this (truncating after residue 256) -the channel remains highly CO₂ and voltage sensitive. We have also documented the effect of the  hypercapnic solutions on intracellular pH measured with BCECF. These new data are now included as figure supplements to Figure 2.

(2) What is the impact of expressing the K105E / K109E Cx43 double mutant on cell viability?

There was no obvious observed impact, cell density was as expected (no evidence of increased cell death), brightfield and fluorescence visualisation indicated normal healthy cells. We have added a movie (Fig 9, movie supplement 1) to show the effect of La³⁺ on the GRAB_ATP signal in cells expressing Cx43^{K105E, K109E} so readers can appreciate the morphology and its stability during the recording.

(3) A quick look at other alpha connexins suggested that Cx43 was unique among alpha connexins in maintaining the carbamylation motif. This merits additional discussion/ analysis.

This is an interesting point. Cx43 is not unique in the alpha clade in having the carbamylation motif as a number of other human alpha connexins also possess: Cx50, Cx59 and Cx62, and non-human alpha connexins (Cx40, Cx59, Cx46) also possess the motif. We have shown that Cx50 is CO₂ sensitive. We have performed a brief molecular phylogenetic analysis of the alpha connexon clade to highlight the occurrence of the carbamylation motif. This is now presented as Fig 12 to go with the accompanying discussion.

(4) There were some minor writing issues that should be addressed. For instance, fEPSP is not defined. Also, insets showing positive controls in some experiments were not described in the figure legends.

We have corrected these issues.

Reviewer #2 (Recommendations for the authors):

(1) I would omit the data on the ODDD-associated mutations since there is no evidence that loss of CO₂ sensitivity plays an important role in the underlying disease pathology.

We are not making the claim CO₂ loss leads to the underlying pathology and have reviewed the text to ensure that we clearly express that this is a correlation not a cause. We think this is worth retaining as many pathological mutations in other CO₂ sensitive connexins (Cx26, Cx32 and Cx50) cause loss of CO₂ sensitivity, and this information may be helpful to other researchers.

(2) Why is high K+ rather than low external calcium used as a positive control in ATP release experiments?

We used of high K⁺ and depolarisation as a positive control as regard this as a more physiological stimulus than the low external Ca²⁺.

(3) Does Cx43A44V or Cx43L90V block gap junctional coupling?

An interesting question but we have not examined this.

(4) Provide references for biophysical recordings of Cx43 hemichannels performed in HEPES-buffered salines, which document Cx43 hemichannels as being shut.

have added the original and some later references which examine Cx43 hemichannel gating in HEPES buffer and shows the need for substantial depolarisation to induce channel opening.

(5) In the heart muscle, changes in PCO₂ have long been hypothesized to cause changes in myocardial function by changing pHi.

This is true and we now add some discussion of this point. Now that we know that Cx43 is directly sensitive to CO₂ a direct action of CO₂ cannot be ruled out and careful experimentation is required to test this possibility. 

Reviewer #3 (Recommendations for the authors):

(1) Page 3: "... homologs of K125 and R104 ... ": the context is linked to Cx26, so Cx26 needs to be added here.

Done

(2) Page 4 text and related Figure 2:

(a) Figure 2A&B: PCO2-dependent Cx43 HC opening is clearly present in the carboxy-fluorescein dye uptake experiments (Figure 2A) as well as in the electrophysiological experiments (Figure 2B). The curves look quite different between these two distinct readouts: dye uptake doubles from 20 to 70 mmHg in Figure 2A while the electrophysiological data double from 45 to 70 mmHg in Figure 2B. These responses look quite distinct and may be linked to a non-linearity of the dye uptake assay or a problem in the electrophysiological measurements of Figure 2B discussed in the next point.

Different molecules/ions may have different permeabilities through the channel, which could explain the observed difference. Also, there is some contamination of the whole cell conductance change with another conductance (evident in recordings from parental HeLa cells). This is evident particularly at 70 mmHg. If this contaminating conductance were subtracted from the total conductance in the Cx43 expressing cells, then the dose response relations would be more similar. However, we are reluctant to add this additional data processing step to the paper.

(b) The traces in Figure 2B show that the HC current is inward at 20 mmHg PCO2, while it switches to an outward current at 55mmHg PCO2. HCs are non-selective channels, so their current should switch direction around 0 mV but not at -50 mV. As such, the -50 mV switching point indicates involvement of another channel distinct from non-selective Cx43 hemichannels.

We think that our incomplete description in the legend led to this misunderstanding. We used a baseline of 35 mmHg (where the channels will be slightly open) and changed to 20 mmHg to close them (or to higher PCO₂ to open them from this baseline), hence a decrease in conductance and loss of outward current for 20 mmHg. The holding potential for the recordings and voltage steps were the same in all recordings. We have now edited the legend and added more information into the methods to clarify this and how we constructed the dose response curve.

We agree that Cx43 hemichannels are relatively nonselective and would normally be expected to have a reversal potential around 0 mV, but we are using K-Gluconate and the lowered reversal potential (~-65 mV) is likely due to poor permeation of this anion via Cx43.

(c) A Hill slope of 6 is reported for this curve, which is extremely steep. The paper does not provide any further consideration, making this an isolated statement without any theoretical framework to understand the present finding in such context (i.e., in relation to the PCO2 dependency of Cx channels).

Yes, we agree -it seems to be the case with all CO₂ sensitive connexins that we have looked at that the Hill coefficient versus CO₂ is >4. Hemichannels are of course hexameric so there is potential for 6 CO₂ molecules to be bound and extensive cooperativity. We have modified the text to give greater context.

(d) A further remark to Figure 2 is that it does not contain any experiment showing the effect of Cx43 hemichannel inhibition with a reliable HC inhibitor such as Gap26, which is only used in the penultimate illustration of Figure 10. Gap26 should be used in Figure 2 and most of the other figures to show evidence of HC contribution. The lanthanum ions used in Figure 9 are a very non-specific hemichannel blocker and should be replaced by experiments with Gap26.

We have addressed the first part of this comment above.

We agree that La³⁺ blocks all hemichannels, but in the context of our experiments and the controls we have performed it is entirely adequate and supports our conclusions. Our controls show (mentioned above and below) show that the expression of Cx43 is absolutely required for CO₂-dependent ATP release (and dye loading). In Figure 9 our use of La³⁺ was to show the presence of a constitutively open Cx43 mutant hemichannel. Gap26 would add little to this. Our further controls show that with expression of Cx43^WT La³⁺ did nothing to the ATP signal under baseline conditions (20 mmHg) supporting our conclusion that the mutant channels are constitutively open.

(e) As the experiments of Figure 2 form the basis of what is to follow, the above remarks cast doubt on the robustness of the experiments and the data produced.

We disagree, our results are extremely robust: 1) we have used three independent assays confirm the presence of the response; 2) parental HeLa cells do not release ATP, dye load or show large conductance changes to CO₂ showing the absolute requirement for expression of Cx43; 3) mutations of Cx43 (in the carbamylation motif) alter the CO₂ evoked ATP release and dye loading giving further confirmation of Cx43 as the conduit for ATP release and dye loading; and 4) we use standard positive controls (0 Ca^², high K) to confirm cells still have functional channels for those mutations that modified CO₂ sensitivity.

(f) The sentence "Cells transfected with GRAB-ATP only, showed ... " should be

modified to "In contrast, cells not expressing Cx43 showed no responses to any applied CO2 concentration as concluded from GRAB-ATP experiments"

We have modified the text.

(3) Page 5 and Figures 3 & 4:

(a) Figure 3 illustrates results obtained with mutations of 4 distinct Lys residues. However, the corresponding legend indicates mutations that are different from the ones shown in the corresponding illustrations, making it impossible to reliably understand and interpret the results shown in panels A-E.

Thanks for pointing this out. Our apologies, we modified the figure so that the order of the images matched the order of the graph (and the legend) but then forgot to put the new version of the figure in the text. We have now corrected this so that Figure and legend match.

(b) Figure 4 lacks control WT traces!

The controls for this (showing that parental HeLa cells do not release ATP in response to CO₂ or depolarisation) are shown in Figure 2.

(c) Figure 4, Supplement 1: High Hill coefficients of 10 are shown here, but they are not discussed anywhere, as is also the case for the remark on p.4. A Hill steepness of 10 is huge and points to many processes potentially involved. As reported above, these data are floating around in the manuscript without any connection.

Yes, we agree this is very high and surprising. It may reflect as mentioned above the hexameric nature of the channel and that 4 Lys residues seem to be involved. We have used this equation to give some quantitative understanding of the effect of the mutations on CO₂ sensitivity and still think this is useful. We have no further evidence to interpret these values one way or the other.

(4) Page 6: Carbamate bridges are proposed to be formed between K105 and K144, and between K109 and K234. The first three of these Lysine residues are located in the 55aa long cytoplasmic loop of Cx43, while K234 is in the juxta membrane region involved in tubulin interactions. Both K144 and and K234 are involved in Cx43 HC inhibition: K144 is the last aa of the L2 peptide (D119-K144 sequence) that inhibits Cx43 hemichannels while K234 is the first aa of the TM2 peptide that reduces hemichannel presence in the membrane (sequence just after TM4, at the start of the C-tail). This context should be added to increase insight and understanding of the CO2 carbamylation effects on Cx43 hemichannel opening.

Thanks for suggesting this. We have added some discussion of CT to CL interactions in the context of regulation by pH and [Ca²⁺].

(5) Page 7: The Cx43 ODDD A44V and L90V mutations lead to loss of pCO2 sensitivity in dye loading and ATP assays. However, A44V located in EL1 is reportedly associated with Cx43 HC activation, while L90V in TM2 is associated with HC inhibition. Remarkably, these mutations are focused on non-Lys residues, which brings up the question of how to link this to the paper's main thread.

This follows the pattern that we have seen for other mutations such as A40V, A88V in Cx26 and several CMTX mutations of Cx32. Our cryoEM structures of Cx26 suggest that these mutations alter the flexibility of the molecule and hence abolish CO₂ sensitivity. We have reworded the text to avoid giving the impression that there is a demonstrated link between loss of CO₂ sensitivity of Cx43 and pathology.

(6) Page 8: HCs constitutively open - 'constutively' perhaps does not have the best connotation as it is not related to HC constitution but CO2 partial pressure.

Yes, we agree and have reworded this.

(7) Page 9: "in all subtypes" -> not clear what is meant - do you mean "in all cell types"?

We agree this is unclear -it refers to all astrocytic subtypes. We have amended the text.

(8) Page 10: Composition of hypocapnic recording solution: bubbling description is incomplete "95%O2/5%" and should be "95%O2/5%CO2".

Changed.

(9) Page 11: Composition of zero Ca^²⁺ hypocapnic recording solution: perhaps better to call this "nominally Ca^²⁺-free hypocapnic recording solution" as no Ca^²⁺ buffer is included in this solution

Thanks for pointing this out. We did in fact add 1 mM EGTA to the solutions but omitted this from the recipe, this has now been corrected.

(10) Page 11: in M&M I found that the NaHCO3- is lowered to 10 mM in the zero Ca^²⁺condition, while the control experimental condition has 26 mM NaHCO3-. The zero Ca condition should be kept at a physiologically normal 26 mM NaHCO3- concentration, so why was this done? Lowering NaHCO3- during hemichannel stimulation may result in smaller responses and introduce non-linearities.

For the dye loading we used 20 mmHg as the baseline condition and increased PCO₂ from this. Hence for the zero Ca²⁺ positive control we modified the 20 mmHg hypocapnic solution by substituting Mg²⁺ for Ca²⁺ and adding EGTA. We have modified the text in the Methods to clarify this.

Further remarks on the figures:

(1) Figure 2A: Add 20 & 70 mmHg to the images, to improve the readability of this illustration.

Done

(2) Figure 3: WT responses are shown in panel F, but experimental data (images and curves) are lacking and should be included in a revised version.

The wild type data is shown in Fig 2A. We have some sympathy for the comment, but we felt that Fig 2 should document CO₂ sensitivity, and then the subsequent Figs should analyse its basis. Hence the separation of Cx43^WT data from the mutant data. In panel F, we state that we have recalculated the WT data from Fig 2A to allow the comparison.

(3) Figures 4, 6, 8: Color codes for mmHg CO₂ pressure make reading these figures difficult; perhaps better to add mmHg values directly in relation to the traces.

We have considered this suggestion but feel that the figures would become very cluttered with the additional labelling.

(4) I wouldn't use colored lines when not necessary, e.g., Figure 9 100 µM La3+; Figure 10 (add 20->35 mmHg PCO2 switch; add scrGap26 above blue bars); Figure 11C & D.

We agree and can see that in Figs 9 and 10 this muddles our colour scheme in other figures so have modified these figures. There was not space to put the suggested labels.

(5) The mechanism of increased HC opening is not clear.

We agree and have discussed various options and the analogy with what we know about Cx26. Ultimately new cryo-EM data is required.

(6) Figure 10: 35G/35S are weird abbreviations for 35 mmHg Gap26 and scrambled Gap26.

Yes, but we used these to fit into the available space.

(7) Figure 11, legend: '20 mmHg PCO2 for each transfection for 70 mmHg PCO2'. It is not clear what is meant here.

Thanks for pointing this out, we have reworded this to ensure clarity.

eLife Assessment

The authors develop an important microfluidic microvascular model called "Vessel-on-Chip", which they use to study Neisseria meningitidis interactions within this in vitro vascular system. Compelling evidence shows that the fabricated channels are lined by endothelial cells, and these can be colonized by N. meningitidis that in turn triggers neutrophil recruitment. This model has advantages over the human skin xenograft mouse model, which requires complex surgical techniques, however, it also carries limitations in that only endothelial cells and supplied specific immune cells in the microfluidics are present, while true vasculature contains a number of other cell types including smooth muscle cells, pericytes, and components of the immune system.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

The work by Pinon et al describes the generation of a microvascular model to study Neisseria meningitidis interactions with blood vessels. The model uses a novel and relatively high throughput fabrication method that allows full control over the geometry of the vessels. The model is well characterized from the vascular standpoint and shows improvements when exposed to flow. The authors show that Neisseria binds to the 3D model in a similar geometry that in the animal xenograft model, induces an increase in permeability short after bacterial perfusion, and endothelial cytoskeleton rearrangements including a honeycomb actin structure. Finally, the authors show neutrophil recruitment to bacterial microcolonies and phagocytosis of Neisseria.

Strengths:

The article is overall well written, and it is a great advancement in the bioengineering and sepsis infection field. The authors achieved their aim at establishing a good model for Neisseria vascular pathogenesis and the results support the conclusions. I support the publication of the manuscript. I include below some clarifications that I consider would be good for readers.

One of the most novel things of the manuscript is the use of a relatively quick photoablation system. Could this technique be applied in other laboratories? While the revised manuscript includes more technical details as requested, the description remains difficult to follow for readers from a biology background. I recommend revising this section to improve clarity and accessibility for a broader scientific audience.

The authors suggest that in the animal model, early 3h infection with Neisseria do not show increase in vascular permeability, contrary to their findings in the 3D in vitro model. However, they show a non-significant increase in permeability of 70 KDa Dextran in the animal xenograft early infection. As a bioengineer this seems to point that if the experiment would have been done with a lower molecular weight tracer, significant increases in permeability could have been detected. I would suggest to do this experiment that could capture early events in vascular disruption.

One of the great advantages of the system is the possibility of visualizing infection-related events at high resolution. The authors show the formation of actin of a honeycomb structure beneath the bacterial microcolonies. This only occurred in 65% of the microcolonies. Is this result similar to in vitro 2D endothelial cultures in static and under flow? Also, the group has shown in the past positive staining of other cytoskeletal proteins, such as ezrin in the ERM complex. Does this also occur in the 3D system?

Significance:

The manuscript is comprehensive, complete and represents the first bioengineered model of sepsis. One of the major strengths is the carful characterization and benchmarking against the animal xenograft model. Beyond the technical achievement, the manuscript is also highly quantitative and includes advanced image analysis that could benefit many scientists. The authors show a quick photoablation method that would be useful for the bioengineering community and improved the state-of-the-art providing a new experimental model for sepsis.

My expertise is on infection bioengineered models.

Comments on revised version:

The authors have addressed all my concerns.

Reviewer #2 (Public review):

Pinon and colleagues have developed a Vessel-on-Chip model showcasing geometrical and physical properties similar to the murine vessels used in the study of systemic infections. The authors succeed on their aim of developing an complex, humanized, in vitro model that can faithfully recapitulate the hallmarks of systemic infections.

The vessel was created via highly controllable laser photoablation in a collagen matrix, subsequent seeding of human endothelial cells, and flow perfusion to induce mechanical cues. This model could be infected with Neisseria meningitidis as a model of systemic infection. In this model, microcolony formation and dynamics, and effects on the host were very similar to those described for the human skin xenograft mouse model (the current gold standard for systemic studies) and were consistent with observations made in patients. The model could also recapitulate the neutrophil response upon N. meningitidis systemic infection.

The claims and the conclusions are supported by the data, the methods are properly presented, and the data is analyzed adequately. The most important strength of this manuscript is the technology developed to build this model, which is impressive and very innovative. The Vessel-on-Chip can be tuned to acquire complex shapes and, according to the authors, the process has been optimized to produce models very quickly. This is a great advancement compared with the technologies used to produce other equivalent models. This model proves to be equivalent to the most advanced model used to date (skin xenograft mouse model). The human skin xenograft mouse model requires complex surgical techniques and has the practical and ethical limitations associated with the use of animals. However, the Vessel-on-chip model is free of ethical concerns, can be produced quickly, and allows to precisely tune the vessel's geometry and to perform higher resolution microscopy. Both models were comparable in terms of the hallmarks defining the disease, suggesting that the presented model can be an effective replacement of the animal use in this area. In addition, the Vessel-on-Chip allows to perform microscopy with higher resolution and ease, which can in turn allow more complex and precise image-based analysis. The authors leverage the image-based analysis to obtain further insights into the infection, highlighting the capabilities of the model in this aspect.

A limitation of this model is that it lacks the multicellularity that characterizes other similar models, which could be useful to research disease more extensively. However, the authors discuss the possibilities of adding other cells to the model, for example, fibroblasts. The methodology would allow for integrating many different types of cells into the model, which would increase the scope of scientific questions that can be addressed. In addition, the technology presented in the current paper is also difficult to adapt for standard biology labs. The methodology is complex and requires specialized equipment and personnel, which might hinder its widespread utilization of this model by researchers in the field.

This manuscript will be of interest for a specialized audience focusing on the development of microphysiological models. The technology presented here can be of great interest to researchers whose main area of interest is the endothelium and the blood vessels, for example, researchers on the study of systemic infections, atherosclerosis, angiogenesis, etc. This manuscript can have great applications for a broad audience focusing on vasculature research. Due to the high degree of expertise required to produce these models, this paper can present an interesting opportunity to begin collaborations with researchers dealing with a wide range of diseases, including atherosclerosis, cancer (metastasis), and systemic infections of all kinds.

Reviewer #3 (Public review):

Summary:

In this manuscript Pinon et al. describe the development of a 3D model of human vasculature within a microchip to study Neisseria meningitidis (Nm)- host interactions and validate it through its comparison to the current gold-standard model consisting of human skin engrafted onto a mouse. There is a pressing need for robust biomimetic models with which to study Nm-host interactions because Nm is a human-specific pathogen for which research has been primarily limited to simple 2D human cell culture assays. Their investigation relies primarily on data derived from microscopy and its quantitative analysis, which support the authors' goal of validating their Vessel-on-Chip (VOC) as a useful tool for studying vascular infections by Nm, and by extension, other pathogens associated with blood vessels.

Strengths:

• Introduces a novel human in vitro system that promotes control of experimental variables and permits greater quantitative analysis than previous models<br /> • The VOC model is validated by direct comparison to the state-of-the-art human skin graft on mouse model<br /> • The authors make significant efforts to quantify, model, and statistically analyze their data<br /> • The laser ablation approach permits defining custom vascular architecture<br /> • The VOC model permits the addition and/or alteration of cell types and microbes added to the model<br /> • The VOC model permits the establishment of an endothelium developed by shear stress and active infusion of reagents into the system

Weaknesses:

• The VOC model contains one cell type, human umbilical cord vascular endothelial cells (HUVECs), while true vasculature contains a number of other cell types that associate with and affect the endothelium, such as smooth muscle cells, pericytes, and components of the immune system. However, adding such complexity may be a future goal of this VOC model.

Impact:

The VOC model presented by Pinon et al. is an exciting advancement in the set of tools available to study human pathogens interacting with the vasculature. This manuscript focuses on validating the model, and as such sets the foundation for impactful research in the future. Of particular value is the photoablation technique that permits the custom design of vascular architecture without the use of artificial scaffolding structures described in previously published works.

Comments on revised version:

The authors have nicely addressed my (and other reviewers') comments.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

One of the most novel things of the manuscript is the use of a relatively quick photoablation system. Could this technique be applied in other laboratories? While the revised manuscript includes more technical details as requested, the description remains difficult to follow for readers from a biology background. I recommend revising this section to improve clarity and accessibility for a broader scientific audience.

As suggested, we have adapted the paragraph related to the photoablation technique in the Material & Method section, starting line 1147. We believe it is now easier to follow.

The authors suggest that in the animal model, early 3h infection with Neisseria do not show increase in vascular permeability, contrary to their findings in the 3D in vitro model. However, they show a non-significant increase in permeability of 70 KDa Dextran in the animal xenograft early infection. As a bioengineer this seems to point that if the experiment would have been done with a lower molecular weight tracer, significant increases in permeability could have been detected. I would suggest to do this experiment that could capture early events in vascular disruption.

Comparing permeability under healthy and infected conditions using Dextran smaller than 70 kDa is challenging. Previous research (1) has shown that molecules below 70 kDa already diffuse freely in healthy tissue. Given this high baseline diffusion, we believe that no significant difference would be observed before and after N. meningitidis infection, and these experiments were not carried out. As discussed in the manuscript, bacteria-induced permeability in mice occurs at later time points, 16h post-infection, as shown previously (2). As discussed in the manuscript, this difference between the xenograft model and the chip could reflect the absence of various cell types present in the tissue parenchyma or simply vessel maturation time.

One of the great advantages of the system is the possibility of visualizing infection-related events at high resolution. The authors show the formation of actin in a honeycomb structure beneath the bacterial microcolonies. This only occurred in 65% of the microcolonies. Is this result similar to in vitro 2D endothelial cultures in static and under flow? Also, the group has shown in the past positive staining of other cytoskeletal proteins, such as ezrin, in the ERM complex. Does this also occur in the 3D system?

We imaged monolayers of endothelial cells in the flat regions of the chip (the two lateral channels) using the same microscopy conditions (i.e., Obj. 40X N.A. 1.05) that have been used to detect honeycomb structures in the 3D vessels in vitro. We showed that more than 56% of infected cells present these honeycomb structures in 2D, which is 13% less than in 3D, and is not significant due to the distributions of both populations. Thus, we conclude that under both in vitro conditions, 2D and 3D, the amount of infected cells exhibiting cortical plaques is similar. These results are in Figure 4E and S4B.

We also performed staining of ezrin in the chip and imaged both the 3D and 2D regions. Although ezrin staining was visible in 3D (Author response image 1), it was not as obvious as other markers under these infected conditions, and we did not include it in the main text. Interpretation of this result is not straightforward, as the substrate of the cells is different, and it would require further studies on the behavior of ERM proteins in these different contexts.

Author response image 1.

F-actin (red) and ezrin (yellow) staining after 3h of infection with N. meningitidis (green) in 2D (top) and 3D (bottom) vessel-on-chip models.

Recommendation to the authors:

Reviewer #1 (Recommendation to the authors):

I appreciate that the authors addressed most of my comments, of special relevance are the change of the title and references to infection-on-chip. I think that the current choice of words better acknowledges the incipient but strong bioengineering infection community. I also appreciate the inclusion of a limitation paragraph that better frames the current work and proposes future advancements.

The addition of more methodological details has improved the manuscript. Although as mentioned earlier the wording needs to be accessible for the biology community. I also appreciated the addition of the quantification of binding under the WSS gradient in the different geometries and shown in Fig 3H. However, the description of the figure and the legend is not clear. What does "vessel" mean on the graph and "normalized histograms ...(blue)" in the figure legend. Could the authors rephrase it?

In Figure 3F, we investigated whether Neisseria meningitidis exhibits preferential sites of infection. We hypothesized that, if bacteria preferentially adhered to specific regions, the local shear stress at these sites would differ from the overall distribution. To test this, we compared the shear stress at bacterial adhesion sites in the VoC (orange dots and curve) with the shear stress along the entire vascular edges (blue dots and curve). The high Spearman correlation indicates that there is no distinct shear stress value associated with bacterial adhesion. This suggests that bacteria can adhere across all regions, independently of local shear stress. To enhance clarity, the legend of Figure 3 and the related text have been rephrased in the revised manuscript (L289-314).

Line 415. Should reference to Fig S5B, not Fig 5B. Also, the titles in Supplementary Figure 4 and 5 are duplicated, and the description of the legend inf Fig S5 seems a bit off. A and B seem to be swapped.

Indeed, the reference to the right figure has been corrected. Also, the title of Figure S4 has been adapted to its contents, and the legend of Figure S5 has been corrected.

Reviewer #2 (Recommendation to the authors):

Minor comments to the authors:

Line 163 "they formed" instead of "formed".

Line 212 "two days" instead of "two day"

Line 269 a space between two words is missing.

These three comments have been addressed in the revised manuscript.

In addition, I appreciate answering the comments, especially those requiring hypothesizing about including further cells. However, when discussing which other cells could be relevant for the model (lines 631 to 632) it would be beneficial to discuss not only the role of those cells but also how could they be included in the model. I think for the reader, inclusion of further cells could be seen as a challenge or limitation, and addressing these technical points in the discussion could be helpful.

We thank Reviewer #2 for the insightful suggestion. Indeed, the method of introducing cells into the VoC depends on their type. Fibroblasts and dendritic cells, which are resident tissue cells, should be embedded in the collagen gel before polymerization and UV carving. This requires careful optimization to preserve chip integrity, as these cells exert pulling forces while migrating within the collagen matrix. In contrast, T cells and macrophages should be introduced through the vessel lumen to mimic their circulation in vivo. Pericytes can be co-seeded with endothelial cells, as they have been shown to self-organize within a few hours post-seeding. These important informations are now included in the manuscript (L577-587).

Reviewer #3 (Recommendation to the authors):

Suggestions and Recommendations

Some suggestions related to the VOC itself:

Figure 1, Fig S1, paragraph starting line 1071: More information would be helpful for the laser photoablation. For instance, is a non-standard UV laser needed? Which form of UV light is used? What is the frequency of laser pulsing? How many pulses/how long is needed to ablate the region of interest?

The photoablation process requires a focused UV-laser, with high frequency (10 kHz) to lower the carving time while providing the required intensity to degrade collagen gel. To carve a reproducible number of 30 µm-large vessels, we used a 2 µm-large laser beam at an energy of 10 mW and moved the stage (i.e., sample) at a maximum speed of 1 mm/s. This information has been added to the related paragraph starting on line 1147 of the revised manuscript.

It is difficult to understand the geometry of the VOC. In Figure 1C, is the light coloration representing open space through which medium can flow, and the dark section the collagen? On a single chip, how many vessels are cut through the collagen? It looks as if at least two are cut in Figure 1C in the righthand photo.

In Figure 1C, the light coloration is the Factin staining. The horizontal upper and lower parts are the 2D lateral channels that also contain endothelial cells, and are connected to inlets and outlets, respectively. In the middle, two vertically carved 3D vessels are shown in the confocal image.

Technically, we designed the PDMS structures to allow carving of 1 to 3 channels, maximizing the number of vessels that can be imaged while minimizing any loss of permeability at the PDMS/collagen/cells interface. This information has been added in the revised manuscript (L. 1147).

If multiple vessels are cut in the center channel between the lateral channels, how do you ensure that medium flow is even between all vessels? A single chip with multiple different vessel architectures through the center channel would be expected to have different hydrostatic resistance with different architectures, thereby causing differences in flow rates in each vessel.

To ensure a consistent flow rate regardless of the number of carved vessels, we opted to control the flow rate directly across the chip with a syringe pump. During experiments, one inlet and one outlet were closed, and a syringe pump was used. Because the carved vessels are arranged in parallel (derivation), the flow rate remains the same in each vessel. If a pressure controller had been used instead, the flow would have been distributed evenly across the different channels. This has been added to the revised manuscript in the paragraph starting on line 1210.

The figures imply that the laser ablation can be performed at depth within the collagen gel, rather than just etching the surface. If this is the case, it should be stated explicitly. If not, this needs to be clarified.

One of the main advantages of the photoablation technique is carving the collagen gel in volume, and not only etching the surface. Thanks to the 3D UV degradation, we can form the 3D architecture surrounded by the bulk collagen. This has been added to the revised manuscript, lines 154-155.

Is the in-vivo-like vessel architecture connected to the lateral channel at an oblique angle, or is the image turned to fit the entire structure? (Figure 1F and 3E). Is that why there is high shear stress at its junction with the lateral channel depicted in Figure 3E?

All structures require connection to the lateral channels to ensure media circulation and nutrient supply. The in vivo-like design must be rotated to allow the upper and lower branches of the complex structure to pass between the fixed PDMS pillars. To remain consistent with the image and the flow direction, we have kept the same orientation as in the COMSOL simulation. This leads to a locally higher shear stress at the top of the architecture. This has been added in the revised manuscript, in the paragraph starting on line 1474.

Figure S1F,G: In the legend, shapes are circles, not squares. On the graphs, what do the numbers in parentheses mean?

Indeed, the terms "squares" have been replaced by "circles" in Figure 1. (1) and (2) refer to the providers of the collagen, FujiFilm and Corning, respectively. We have added this mention in the legend in Figure S1.

Figure 3B: how do the images on the left and right differ? Each of the 4 images needs to be explained.

The four images represent the infected VoC from different viewing angles, illustrating the three-dimensional spread of infection throughout the vessel. A more detailed description has been added in the legend of Figure 3.

Figure S3C is not referenced but should be, likely before sentence starting on line 299.

Indeed, the reference to Figure S3C has been added line 301 of the revised manuscript.

Results in Figure 3 with the pilD mutant are very interesting. It is worth commenting in the Discussion about how T4P functionality in addition to the presence of T4P contributes to Nm infection, and how in the future this could be probed with pilT mutants.

We thank Reviewer #3 for this relevant insight. Following adhesion, a key functionality of Neisseria meningitidis for colony formation and enhanced infection is twitching motility. As suggested, we have added in the Discussion the idea of using a PilT mutant, which can adhere but cannot retract its pili, in the VoC model to investigate the role of motility in colonization in vitro under flow conditions (L611–623).

Which vessel design was used for the data presented in Figures 4, 5, and 6 and associated supplemental figures?

Straight channels have been mostly used in figures 4, 5, and 6. Rarely, we used the branched in vivo-like designs to observe potential similar infection patterns to in vivo, and related neutrophil activity. This has been added in the revised manuscript, lines 1435-1439.

Figure 4B-D: the images presented in Figure 4C are not representative of the averages presented in Figures 4B,D. For instance, the aggregates appear much larger and more elongated in the animal model in Figure 4C, but the animal model and VOC have the colony doubling time (implying same size) in Figure 4B, and same average aggregate elongation in Figure 4D.

The images in Figure 4C were selected to illustrate the elongation of colonies quantified in Figure 4D. The elongation angles are consistent between both images and align with the channel orientation. Representative images of colony expansion over time, corresponding to Figure 4A and 4B, are provided in Figure S4A.

Figures 4E-F: dextran does not appear to diffuse in the VOC in response to histamine in these images, yet there is a significant increase in histamine-induced permeability in Figure 4F. Dotted lines should be used to indicate vessel walls for histamine, and/or a more representative image should be selected. A control set of images should also be included for comparison.

We thank Reviewer #3 for the insightful comment. We confirm that we have carefully selected representative images for the histamine condition and adjusted them to display the same range of gray levels. The apparent increase in permeability with histamine is explained by a slight rise in background fluorescence, combined with the smaller channel size shown in Figure 4E.

Figure S4 title is a duplicate of Figure S5 and is unrelated to the content of Figure S4. Suggest rewording to mention changes in permeability induced by Nm infection in the VOC and animal model.

Indeed, the title of Figure S4 did not correspond to its content. We have, thus, changed it in the revised manuscript.

Line 489 "...our Vessel-on-Chip model has the potential to fully capture the human neutrophil response during vascular infections, in a species-matched microenvironment", is an overstatement. As presented, the VOC model only contains endothelial cells and neutrophils. Many other cell types and structures can affect neutrophil activity. Thus, it is an overstatement to claim that the model can fully capture the human neutrophil response.

We agree with the Reviewer #3, that neutrophil activity is fully recapitulated with other cell types, such as platelets, pericytes, macrophages, dendritic cells, and fibroblasts, that secrete important molecules such as cytokines, chemokines, TNF-α, and histamine. In our simplified model we were able to reconstitute the complex interaction of neutrophils with endothelial cells and with bacteria. The text was modified accordingly.

Supplemental Figure 6 - Does CD62E staining overlap with sites of Nm attachment

E-selectin staining does not systematically colocalize with Neisseria meningitidis colonies although bacterial adhesion is required. Its overall induced expression is heterogeneous across the tissue and shows heterogeneity from cell to cell as seen in vivo.

Line 475, Figure 6E- Phagocytosis of Nm is described, but it is difficult to see. An arrow should be added to make this clear. Perhaps the reference should have been to Figure 6G? Consider changing the colors in Figure 6G away from red/green to be more color-blind friendly.

Indeed, the reference to the right figure is Figure 6G, where the phagocytosis event is zoomed in. We have changed it in the text. Adapting the color of this figure 6G would imply to also change all the color codes of the manuscript, as red has been used for actin and green for Neisseria meningitidis.

Lines 621-632 - This important discussion point should be reworked. Some suggested references to cite and discuss include PMID: 7913984, 15186399, 17991045, 18640287, 19880493.

We have introduced in the discussion parts the following references as suggested (3–7), and discussed more the importance of introducting of immune cells to study immune cell-bacteria interaction and related immune response (L659-678).

Minor corrections:

•  Line 8 - suggest "photoablation-generated" instead of "photoablation-based"

•  Line 57- remove the word "either", or modify the sentence

•  Sentence on lines 162-165 needs rewording

•  Lines 204-205- "loss of vascular permeability" should read "increase in vascular permeability"

•  Line 293- "Measured" shear stress, should be "computed", since it was not directly measured (according to the Materials & Methods)

•  Line 304- "consistently" should be "consistent"

•  Fig. 3 legend, second line: replace "our" with "the VoC"

•  Line 371, change "our" to "the"

•  Line 415- Figure 5B doesn’t appear to show 2-D data. Is this in Figure S5B? Some clarification is needed. The quantification of Nm vessel association in both the VOC and the animal model should be shown in Figure 5, for direct comparison.

•  Supplementary Figure 5C: correlation coefficient with statistical significance should be calculated.

•  Figure 6 title, rephrase to "The infected VOC model"

•  Line 450, replace "important" with "statistically significant"

•  Line 459, suggest rephrasing to "bacterial pilus-mediated adhesion"

•  Line 533- grammar needs correction

•  Line 589- should be "sheds"

•  Line 1106- should be "pellet"

•  Lines 1223-1224 - is the antibody solution introduced into the inlet of the VOC for staining? Please clarify.

•  Line 1295-unclear why Figure 2B is being referenced here

All the suggested minor corrections have been taken into account in the revised manuscript.

References

(1) Gyohei Egawa, Satoshi Nakamizo, Yohei Natsuaki, Hiromi Doi, Yoshiki Miyachi, and Kenji Kabashima. Intravital analysis of vascular permeability in mice using two-photon microscopy. Scientific Reports, 3(1):1932, Jun 2013. ISSN 2045-2322. doi: 10.1038/srep01932.

(2) Valeria Manriquez, Pierre Nivoit, Tomas Urbina, Hebert Echenique-Rivera, Keira Melican, Marie-Paule Fernandez-Gerlinger, Patricia Flamant, Taliah Schmitt, Patrick Bruneval, Dorian Obino, and Guillaume Duménil. Colonization of dermal arterioles by neisseria meningitidis provides a safe haven from neutrophils. Nature Communications, 12(1):4547, Jul 2021. ISSN 2041-1723. doi: 10.1038/s41467-021-24797-z.

(3) Katherine A. Rhodes, Man Cheong Ma, María A. Rendón, and Magdalene So. Neisseria genes required for persistence identified via in vivo screening of a transposon mutant library. PLOS Pathogens, 18(5):1–30, 05 2022. doi: 10.1371/journal.ppat.1010497.

(4) Heli Uronen-Hansson, Liana Steeghs, Jennifer Allen, Garth L. J. Dixon, Mohamed Osman, Peter Van Der Ley, Simon Y. C. Wong, Robin Callard, and Nigel Klein. Human dendritic cell activation by neisseria meningitidis: phagocytosis depends on expression of lipooligosaccharide (los) by the bacteria and is required for optimal cytokine production. Cellular Microbiology, 6(7):625–637, 2004. doi: https://doi.org/10.1111/j.1462-5822.2004.00387.x.

(5) M. C. Jacobsen, P. J. Dusart, K. Kotowicz, M. Bajaj-Elliott, S. L. Hart, N. J. Klein, and G. L. Dixon. A critical role for atf2 transcription factor in the regulation of e-selectin expression in response to non-endotoxin components of neisseria meningitidis. Cellular Microbiology, 18(1):66–79, 2016. doi: https://doi.org/10.1111/cmi.12483.

(6) Andrea Villwock, Corinna Schmitt, Stephanie Schielke, Matthias Frosch, and Oliver Kurzai. Recognition via the class a scavenger receptor modulates cytokine secretion by human dendritic cells after contact with neisseria meningitidis. Microbes and Infection, 10(10):1158–1165, 2008. ISSN 1286-4579. doi: https://doi.org/10.1016/j.micinf.2008.06.009.

(7) Audrey Varin, Subhankar Mukhopadhyay, Georges Herbein, and Siamon Gordon. Alternative activation of macrophages by il-4 impairs phagocytosis of pathogens but potentiates microbial-induced signalling and cytokine secretion. Blood, 115(2):353–362, Jan 2010. ISSN 0006-4971. doi: 10.1182/blood-2009-08-236711.

eLife Assessment

This important study characterises the morphogenesis of cortical folding in the ferret and human cerebral cortex using complementary physical and computational modelling. Notably, these approaches are applied to charting, in the ferret model, known abnormalities of cortical folding in humans. The study finds convincing evidence that variation in cortical thickness and expansion account for deviations in morphology, and supports these findings using cutting-edge approaches from both physical gel models and numerical simulations. The study will be of broad interest to the field of developmental neuroscience.

Reviewer #1 (Public review):

The manuscript by Choi and colleagues investigates the impact of variation in cortical geometry and growth on cortical surface morphology. Specifically, the study uses physical gel models and computational models to evaluate the impact of varying specific features/parameters of the cortical surface. The study makes use of this approach to address the topic of malformations of cortical development and finds that cortical thickness and cortical expansion rate are the drivers of differences in morphogenesis.

The study is composed of two main sections. First, the authors validate numerical simulation and gel model approaches against real cortical postnatal development in the ferret. Next, the study turns to modelling malformations in cortical development using modified tangential growth rate and cortical thickness parameters in numerical simulations. The findings investigate three genetically linked cortical malformations observed in the human brain to demonstrate the impact of the two physical parameters on folding in the ferret brain.

This is a tightly presented study that demonstrates a key insight into cortical morphogenesis and the impact of deviations from normal development. The dual physical and computational modeling approach offers the potential for unique insights into mechanisms driving malformations. This study establishes a strong foundation for further work directly probing the development of cortical folding in the ferret brain.

Reviewer #2 (Public review):

Summary:

Based on MRI data of the ferret (a gyrencephalic non-primate animal, in whom folding happens postnatally), the authors create in vitro physical gel models and in silico numerical simulations of typical cortical gyrification. They then use genetic manipulations of animal models to demonstrate that cortical thickness and expansion rate are primary drivers of atypical morphogenesis. These observations are then used to explain cortical malformations in humans.

Strengths:

The paper is very interesting and original, and combines physical gel experiments, numerical simulations, as well as observations in MCD. The figures are informative, and the results appear to have good overall face validity.

Comment on the revised version from the Reviewing Editor:

The reviewers are happy with the authors replies and the eLife Assessment has been amended accordingly.

Author response:

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

Reviewer #1 (Public review):

The manuscript by Choi and colleagues investigates the impact of variation in cortical geometry and growth on cortical surface morphology. Specifically, the study uses physical gel models and computational models to evaluate the impact of varying specific features/parameters of the cortical surface. The study makes use of this approach to address the topic of malformations of cortical development and finds that cortical thickness and cortical expansion rate are the drivers of differences in morphogenesis.

The study is composed of two main sections. First, the authors validate numerical simulation and gel model approaches against real cortical postnatal development in the ferret. Next, the study turns to modelling malformations in cortical development using modified tangential growth rate and cortical thickness parameters in numerical simulations. The findings investigate three genetically linked cortical malformations observed in the human brain to demonstrate the impact of the two physical parameters on folding in the ferret brain.

This is a tightly presented study that demonstrates a key insight into cortical morphogenesis and the impact of deviations from normal development. The dual physical and computational modeling approach offers the potential for unique insights into mechanisms driving malformations. This study establishes a strong foundation for further work directly probing the development of cortical folding in the ferret brain. One weakness of the current study is that the interpretation of the results in the context of human cortical development is at present indirect, as the modelling results are solely derived from the ferret. However, these modelling approaches demonstrate proof of concept for investigating related alterations more directly in future work through similar approaches to models of the human cerebral cortex.

We thank the reviewer for the very positive comments. While the current gel and organismal experiments focus on the ferret only, we want to emphasize that our analysis does consider previous observations of human brains and morphologies therein (Tallinen et al., Proc. Natl. Acad. Sci. 2014; Tallinen et al., Nat. Phys. 2016), which we compare and explain. This allows us to analyze the implications of our study broadly to understand the explanations of cortical malformations in humans using the ferret to motivate our study. Further analysis of normal human brain growth using computational and physical gel models can be found in our companion paper (Yin et al., 2025), now also published to eLife: S. Yin, C. Liu, G. P. T. Choi, Y. Jung, K. Heuer, R. Toro, L. Mahadevan, Morphogenesis and morphometry of brain folding patterns across species. eLife, 14, RP107138, 2025. doi:10.7554/eLife.107138

In future work, we plan to obtain malformed human cortical surface data, which would allow us to further investigate related alterations more directly. We have added a remark on this in the revised manuscript (please see page 8–9).

Reviewer 2 (Public review):

Summary:

Based on MRI data of the ferret (a gyrencephalic non-primate animal, in whom folding happens postnatally), the authors create in vitro physical gel models and in silico numerical simulations of typical cortical gyrification. They then use genetic manipulations of animal models to demonstrate that cortical thickness and expansion rate are primary drivers of atypical morphogenesis. These observations are then used to explain cortical malformations in humans.

Strengths:

The paper is very interesting and original, and combines physical gel experiments, numerical simulations, as well as observations in MCD. The figures are informative, and the results appear to have good overall face validity.

We thank the reviewer for the very positive comments.

Weaknesses:

On the other hand, I perceived some lack of quantitative analyses in the different experiments, and currently, there seems to be rather a visual/qualitative interpretation of the different processes and their similarities/differences. Ideally, the authors also quantify local/pointwise surface expansion in the physical and simulation experiments, to more directly compare these processes. Time courses of eg, cortical curvature changes, could also be plotted and compared for those experiments. I had a similar impression about the comparisons between simulation results and human MRI data. Again, face validity appears high, but the comparison appeared mainly qualitative.

We thank the reviewer for the comments. Besides the visual and qualitative comparisons between the models, we would like to point out that we have included the quantification of the shape difference between the real and simulated ferret brain models via spherical parameterization and the curvature-based shape index as detailed in main text Fig. 4 and SI Section 3. We have also utilized spherical harmonics representations for the comparison between the real and simulated ferret brains at different maximum order N. In our revision, we have included more calculations for the comparison between the real and simulated ferret brains at more time points in the SI (please see SI page 6). As for the comparison between the malformation simulation results and human MRI data in the current work, since the human MRI data are two-dimensional while our computational models are threedimensional, we focus on the qualitative comparison between them. In future work, we plan to obtain malformed human cortical surface data, from which we can then perform the parameterization-based and curvature-based shape analysis for a more quantitative assessment.

I felt that MCDs could have been better contextualized in the introduction.

We thank the reviewer for the comment. In our revision, we have revised the description of MCDs in the introduction (please see page 2).

Reviewer #1 (Recommendations for the authors):

The study is beautifully presented and offers an excellent complement to the work presented by Yin et al. In its current form, the malformation portion of the study appears predominantly reliant on the numerical simulations rather than the gel model. It might be helpful, therefore, to further incorporate the results presented in Figure S5 into the main text, as this seems to be a clear application of the physical gel model to modelling malformations. Any additional use of the gel models in the malformation portion of the study would help to further justify the necessity and complementarity of the dual methodological approaches.

We thank the reviewer for the suggestion. We have moved Fig. S5 and the associated description to the main text in the revised manuscript (please see the newly added Figure 5 on page 6 and the description on page 5–7). In particular, we have included a new section on the physical gel and computational models for ferret cortical malformations right before the section on the neurology of ferret and human cortical malformations.

One additional consideration is that the analyses in the current study focus entirely on the ferret cortex. Given the emphasis in the title on the human brain, it may be worthwhile to either consider adding additional modelling of the human cortex or to consider modifying the title to more accurately align with the focus of the methods/results.

We thank the reviewer for the suggestion. While the current gel and organismal experiments focus on the ferret only, we want to emphasize that our analysis does consider previous observations of human brains and morphologies therein (Tallinen et al., Proc. Natl. Acad. Sci. 2014; Tallinen et al., Nat. Phys. 2016), which we compare and explain. This allows us to analyze the implications of our study broadly to understand the explanations of cortical malformations in humans using the ferret to motivate our study. Therefore, we think that the title of the paper seems reasonable. To further highlight the connection between the ferret brain simulations and human brain growth, we have included an additional comparison between human brain surface reconstructions adapted from a prior study and the ferret simulation results in the SI (please see SI Section S4 and SI Fig. S5 on page 9–10).

Two additional minor points:

Table S1 seems sufficiently critical to the motivation for the study and organization of the results section to justify inclusion in the main text. Of course, I would leave any such minor changes to the discretion of the authors.

We thank the reviewer for the suggestion. We have moved Table S1 and the associated description to the main text in the revised manuscript (please see Table 1 on page 7).

Page 7, Column 1: “macacques” → “macaques”.

We thank the reviewer for pointing out the typo. We have fixed it in the revised manuscript (please see page 8).

Reviewer #2 (Recommendations for the authors):

The methods lack details on the human MRI data and patients.

We thank the reviewer for the comment. Note that the human MRI data and patients were from prior works (Smith et al., Neuron 2018; Johnson et al., Nature 2018; Akula et al., Proc. Natl. Acad. Sci. 2023) and were used for the discussion on cortical malformations in Fig. 6. In the revision, we have included a new subsection in the Methods section and provided more details and references of the MRI data and patients (please see page 9–10).

eLife Assessment

This study thoroughly assesses tactile acuity on women's breasts, for which no dependable data currently exists. The study provides two important contributions, by convincingly showing that tactile acuity on the breast is poor in comparison to other body parts, and that acuity is worst in larger breasts, indicating that the number of tactile sensors is fixed. However, further arguments concerning the role of the nipple in spatial localisation are not well supported by the current evidence, therefore diluting the overall contribution of the study. This study will be of interest to the broader community of touch, as well as those interested in breast reconstruction and sexual function.

Reviewer #1 (Public review):

The authors investigated tactile spatial perception on the breast using discrimination, categorization, and direct localization tasks. They reach four main conclusions:

(1) The breast has poor tactile spatial resolution.

This conclusion is based on comparing just noticeable differences, a marker of tactile spatial resolution, across four body regions, two on the breast. The data compellingly support the conclusion; the study outshines other studies on tactile spatial resolution that tend to use problematic measures of tactile resolution, such as two-point-discrimination thresholds. The result will interest researchers in the field and possibly in other fields due to the intriguing tension between the finding and the sexually arousing function of touching the breast.

The manuscript incorrectly describes the result as poor spatial acuity. Acuity measures the average absolute error, and acuity is good when response biases are absent. Precision relates to the error variance. It is common to see high precision with low acuity or vice versa. Just noticeable differences assess precision or spatial resolution, while points of subjective equality evaluate acuity or bias. Similar confusions between these terms appear throughout the manuscript.<br /> A paragraph within the next section seems to follow up on this insight by examining the across-participant consistency of the differences in tactile spatial resolution between body parts. To this aim, pairwise rank correlations between body sites are conducted. This analysis raises red flags from a statistical point of view. 1) An ANOVA and its follow-up tests assume no variation in the size of the tested effect but varying base values across participants. Thus, if significant differences between conditions are confirmed by the original statistical analysis, most participants will have better spatial resolution in one condition than the other condition, and the difference between body sites will be similar across participants. 2) Correlations are power-hungry, and non-parametric tests are power-hungry. Thus, the number of participants needed for a reliable rank correlation analysis far exceeds that of the study. In sum, a correlation should emerge between body sites associated with significantly different tactile JNDs; however, these correlations might only be significant for body sites with pronounced differences due to the sample size.

(2) Larger breasts are associated with lower tactile spatial resolution

This conclusion is based on a strong correlation between participants' JNDs and the size of their breasts. The depicted correlation convincingly supports the conclusion. The sample size is below that recommended for correlations based on power analyses, but simulations show that spurious correlations of the reported size are extremely unlikely at N=18. Moreover, visual inspection rules out that outliers drive these correlations. Thus, they are convincing. This result is of interest to the field, as it aligns with the hypothesis that nerve fibers are more sparsely distributed across larger body parts.

(3) The nipple is a unit

The data do not support this conclusion. The conclusion that the nipple is perceived as a unit is based on poor tactile localization performance for touches on the nipple compared to the areola. The problem is that the localization task is a quadrant identification task with the center being at the nipple. Quadrants for the areola could be significantly larger due to the relative size of the areola and the nipple; the results section seems to suggest this was accounted for when placing the tactile stimuli within the quadrants, but the methods section suggests otherwise. Additionally, the areola has an advantage because of its distance from the nipple, which leads to larger Euclidean distances between the centers of the quadrants than for the nipple. Thus, participants should do better for the areola than for the nipple even if both sites have the same tactile resolution.

To justify the conclusion that the nipple is a unit, additional data would be required. 1) One could compare psychometric curves with the nipple as the center and psychometric curves with a nearby point on the areola as the center. 2) Performance in the quadrant task could be compared for the nipple and an equally sized portion of the areola and tactile locations that have the same distance to the border between quadrants in skin coordinates. 3) Tactile resolution could be directly measured for both body sites using a tactile orientation task with either a two-dot probe or a haptic grating.

Categorization accuracy in each area was tested against chance using a Monte Carlo test, which is fine, though the calculation of the test statistic, Z, should be reported in the Methods section, as there are several options. Localization accuracies are then compared between areas using a paired t-test. It is a bit confusing that once a distribution-approximating test is used, and once a test that assumes Gaussian distributions when the data is Bernoulli/Binomial distributed. Sampling-based and t-tests are very robust, so these surprising choices should have hardly any effect on the results.

A correlation based on N=4 participants is dangerously underpowered. A quick simulation shows that correlation coefficients of randomly sampled numbers are uniformly distributed at such a low sample size. This likely spurious correlation is not analyzed, but quite prominently featured in a figure and discussed in the text, which is worrisome.

(4) Localization of tactile events on the breast is biased towards the nipple

The conclusion that tactile percepts are drawn toward the nipple is based on localization biases for tactile stimuli on the breast compared to the back. Unfortunately, the way participants reported the tactile locations introduces a major confound. Participants indicated the perceived locations of the tactile stimulus on 3D models of these body parts. The nipple is a highly distinctive and cognitively represented landmark, far more so than the scapula, making it very likely that responses were biased toward the nipple regardless of the actual percepts. One imperfect but better alternative would have been to ask participants to identify locations on a neutral grey patch and help them relate this patch to their skin by repeatedly tracing its outline on the skin.

Participants also saw their localization responses for the previously touched locations. This is unlikely to induce bias towards the nipple, but it renders any estimate of the size and variance of the errors unreliable. Participants will always make sure that the marked locations are sufficiently distant from each other.

The statistical analysis is again a homebrew solution and hard to follow. It remains unclear why standard and straightforward measures of bias, such as regressing reported against actual locations, were not used.

Null-hypothesis significance testing only lets scientists either reject the null hypothesis or not. The latter does NOT mean the Null hypothesis is true, i.e., it can never be concluded that there is no effect. This rule applies to every NHST test. However, it raises particular concerns with distribution tests. The only conclusion possible is that the data are unlikely from a population with the tested distribution; these tests do not provide insight into the actual distribution of the data, regardless of whether the result is significant or not.

Reviewer #2 (Public review):

Summary:

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

Results:

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

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

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

Overall assessment:

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

Author response:

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

Reviewer #1 (Public review):

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

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

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

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

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

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

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

“Reports are biased towards the nipple”

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public review):

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

We have removed the qualifier to simplify the text.

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

Correct. We have added text to state as such.

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

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

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

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

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

We have adjusted the text to clarify our meaning.

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

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

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

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

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

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

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

We have clarified this to now read:

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

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

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

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

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

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

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

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

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

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

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

General assessment of the work:

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

Summary of substantive concerns:

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

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

Weaknesses:

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

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

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

Summary:

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

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

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

Strengths:

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

Weaknesses:

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

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

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

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

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

Weaknesses:

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

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

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

Strengths:

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

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

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

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

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

Weaknesses:

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

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

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

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

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

Appraisal:

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

Significance of Findings:

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

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

Large dataset annotated was deposited for the use of the community

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

Weaknesses:

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

Comments on revisions:

The authors addressed all my concerns.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

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

Comments on revisions:

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

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

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

video compression, spatial and temporal resolution trade-offs

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

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

Intro typo: "one link in the chainDIY rigs"

Author response:

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

Reviewer #1 (Public review):

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

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

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

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

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

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

Reviewer #2 (Public review):

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #1 (Recommendations for the authors):

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

We have fixed this in the manuscript. 

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Recommendations for the authors):

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

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

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

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

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

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

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

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

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

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

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

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

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

(5) References 

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

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

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

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

(6) Section 2.2:

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

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

(7) Section 2.3.1:

(a) Should again add the DeepEthogram reference here

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

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

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

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

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

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

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

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

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

We have clarified this in the text. 

(8) Section 2.5:

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

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

(9) Minor corrections:

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

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

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

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

We have fixed them in the updated manuscript.

eLife Assessment

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

Reviewer #1 (Public review):

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

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

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

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

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

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

We thank the Reviewer for finding our work interesting. 

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

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

SI: 

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

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

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

Main Text: 

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

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

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

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

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

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

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

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

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

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

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

Reviewer #3 (Public review):

Summary:

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

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

Strengths:

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

Weaknesses:

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

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

eLife Assessment

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

Reviewer #1 (Public review):

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

Comments on revisions:

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

Reviewer #2 (Public review):

Summary:

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

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

Comments on revisions:

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

Author response:

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

Reviewer #1 (Public review):

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

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

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

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

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

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

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

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

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

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

We thank the Reviewer for the supportive and affirmative feedback.

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public review):

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

We appreciate the clear synthesis and support for the manuscript.

Strengths:

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

We thank the Reviewer for this positive summary.

Weaknesses:

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

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

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

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

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

Reviewer #3 (Public review):

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

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

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

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

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

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

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

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

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

Reviewing Editor Comments:

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

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

Reviewer #2 (Recommendations for the authors):

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

We have added the text as suggested by the Reviewer.

Reviewer #3 (Recommendations for the authors):

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

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

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

We have added 16h to the text.

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

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

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

Weaknesses:

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

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

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

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

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

Reviewer #2 (Public review):

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

Major concerns:

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

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

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

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

(3) Proper annotation of the investigated ray regions.

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

Reviewer #3 (Public review):

Summary:

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

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

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

Strengths:

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

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

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

Weaknesses:

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

Author response:

Reviewer #1

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

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

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

Reviewer #2

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

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

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

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

Reviewer #3

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

References

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

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

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

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

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

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

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

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

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

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

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

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

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

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #3 (Public review):

Summary:

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

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

Strengths:

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

Weaknesses:

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

Author response:

Reviewer #1 (Public review):

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

Reviewer #3 (Public review):

Summary:

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

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

Strengths

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

Weaknesses:

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

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

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

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

eLife Assessment

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

Reviewer #1 (Public review):

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

Comments on revisions:

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

Reviewer #2 (Public review):

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

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

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

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

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

Reviewer #2 (Public review):

Summary:

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

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

Comments on revisions:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

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

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

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

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

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

Additional changes/corrections not outlined above

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

Response letter references

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

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

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

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

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

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

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

eLife Assessment

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