Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

The current claims should be better supported by more evidence.

R1-1: In the first experiment, have the statistics undergone multiple comparison corrections (e.g., Line 441-442)? Given the small sample size, incorporating additional statistical tests (such as the Bayes Factor) could strengthen the analysis.

We confirm that corrections for multiple comparisons are now applied where appropriate, particularly in the group-level ANOVA analyses.

“Post-hoc tests using Holm-Bonferroni correction show that V1 neuronal populations receiving inputs from the central visual field (0.5-4.5°) showed greater contrast sensitivity to high spatial frequency as compared to low spatial frequency stimuli (steeper slope for the 3cpd versus 0.3cpd condition: 0.5-2.5º: t(6) = 4.35, p_bonf = 0.0149; 2.5-4.5º: t(6) = 3.471, p_bonf = 0.0266). Conversely, peripheral eccentricities in V1 (above 9.5°) showed higher contrast sensitivity to low as compared to high spatial frequency stimuli (steeper slope for 0.3cpd versus 3cpd condition: 9.5-15º: 𝑡(6) = −4.591, p_bonf = 0.0149; 15-20º: t(6) = −6.615, p_bonf = 0.0029). Between 4.5° and 9.5°, V1 contrast sensitivity was similar for both spatial frequencies (t(6) = −0.226, p_bonf = 0.8286). Crucially, these effects remained when using retinotopic estimates based on structural scans derived from the Benson retinotopic atlas instead of the pRF-mapping measures (0.5-2.5º: 𝑡(6) = 5.768, p_bonf = 0.0059 ; 2.5-4.5º: t(6) = 2.531, p_bonf = 0.0892 ; 4.5-9.5º: 𝑡(6) = −0.293, p_bonf = 0.7792; 9.5-15º: t(6) = −3.274, p_bonf = 0.0509; 15-20º: t(6) = −3.528, p_bonf = 0.0496; see Figure A2 and Table A3 in Appendix section).”

“Post-hoc pairwise comparisons using Holm-Bonferroni corrections revealed that, as predicted, the cortical contrast response function had a higher slope – indicating better V1 sensitivity – along the horizontal versus vertical quadrants (Horizontal-Vertical Anisotropy – HVA: 𝑡(6) = 5.908, p_bonf = 0.0031) and along the lower versus upper quadrant (Vertical Meridian Anisotropy – VMA: 𝑡(6) = 4.106, p_bonf = 0.0126). Conversely, no difference in cortical contrast sensitivity was found between V1 neuronal populations encoding the left and right quadrants of the visual field (Left-Right Horizontal Meridian Anisotropy – LRHMA: t(6) = 0.7197, p_bonf = 0.4988).”

“We found that the horizontal-vertical anisotropy effect was recovered (HVA: t(6) = 3.584, p_bonf = 0.0347), but that the vertical meridian anisotropy effect was not (VMA: t(6) = 0.744, p_bonf = 0.9697) with this approach.”

R1-2a: The authors claim that "structure-based atlases can replace the need for pRF mapping in cases where it might otherwise be difficult or impossible to collect pRF data." This claim needs further scrutiny. Currently, only one simulated condition of visual field loss was examined in one subject.

AR-R1-2a: We agree that further work is needed to fully establish the utility of structure-based atlases. As a first step, we have followed the reviewer’s suggestion and collected an additional dataset from one of the seven participants, in whom we simulated another condition of visual field loss – specifically, loss of the upper right quadrant. This participant is the same individual already presented in the manuscript (C5), but with a different simulated vision loss condition.

This new condition has been introduced in the Methods, Results and Discussion section, and a new Figure 10 alongside Figure 9 which showed the 3º-8º scotoma. With relevant changes as follows:

“We also demonstrate the clinical relevance of this approach by recovering simulated scotomas (i.e., a ring of visual field loss around fixation and the loss of an entire visual field quadrant), as well as visual field loss in a patient with a neurodegenerative disorder causing large areas of visual field loss.”

“Additionally, one participant (C5) repeated the task under two simulated vision loss conditions (ring or quadrant loss), and two others (C5, C6) completed it with different levels of eye movement.”

“Simulated vision loss

One healthy control participant (C5) also performed a version of the task designed to simulate two forms of visual input loss (i.e., artificial scotoma). These simulations were implemented by: (a) masking a region of the visual field with a grey, annular ring, covering 3º-8º eccentricity, and (b) masking the upper right visual quadrant using a grey quarter-sector overlay. The stimuli and contrast levels used in this task were identical to those described in the original task.”

“A test-case of simulated loss of visual inputs

In the previous sections, we showed that the slope of a square root function provides a reliable measure of contrast sensitivity in the brain of healthy controls. But can this brain-level model also quantify loss of visual inputs? To test this, we first simulated an artificial scotoma in one normal sighted participant, by (a) masking a region of the visual field with a grey, annular ring, covering 3°-8° eccentricity (Figure 9A), and (b) masking the upper-right visual quadrant using a grey quarter-sector overlay (Figure 10A). We expect smaller slope values in V1 neuronal populations that would under normal circumstances encode that part of the visual space.

As expected, we observed reduced responses in V1 locations corresponding to the artificial scotoma (Figures 9 and 10), with increased responses along the edges of the mask for the ring scotoma condition (Figure 9B). This artificial loss of visual input was also clearly present in the cortical contrast sensitivity estimate, with significantly reduced slope steepness in V1 between 3-8° for the ring scotoma condition (Figure 9C&D) and in the upper-right quadrant for the quarter-sector scotoma condition (Figure 10B&C). Additionally, we could recover this scotoma using the calibrated Benson template, although less accurately (Figures 9E and 10D). These results show that this measure of V1 contrast sensitivity is sensitive enough to detect loss of visual inputs in the brain at an individual level, when a complete local loss of sight is simulated, and that this approach does not crucially rely on pRF mapping data from the individual. This supports the utility of our approach in recovering patterns of vision loss and recovery at a cortical level.”

“Mapping Simulated and Pathology-Driven Vision Loss

Our method successfully identified both simulated retinal loss in a healthy volunteer and real visual field loss in a patient with Leber Hereditary Optic Neuropathy (LHON). The signal drop observed in response to masking portions of the visual field in the healthy control was both large and significant at the individual level, as demonstrated by non-overlapping 95% confidence intervals (Figures 9B-C and 10B). This provides proof-of-concept evidence that our approach can detect signal changes in individual patients, which is a critical requirement for clinical translation.

Unlike previous fMRI studies that used high-contrast stimuli (Farahbakhsh et al., 2022; Pawloff et al., 2023; Ritter et al., 2019), which may not accurately represent partial vision loss due to potential saturation effects and the stimulation of less sensitive retinal cells, our use of multiple contrast levels offers a more nuanced assessment of cortical contrast sensitivity.

Combined with the large-field set-up allowing stimulation up to 20° eccentricity, this approach may be particularly well-suited for evaluating treatment efficacy in cases of widespread and variable vision loss.

Future work will focus on further validating reconstruction accuracy under controlled conditions, including simulated scotomas of varying severity and location, expanding testing to larger patient cohorts, and establishing a normative dataset to contextualize patient data.

R1-2b: Also, in Figure 7, contrast sensitivity in the periphery differs between pRF mapping and the Benson atlas. How do the authors explain this discrepancy?

AR-R1-2b: The discrepancy in periphery between pRF mapping and Benson atlas is caused by various factors. These include (a) individual differences in the retinotopy/structure relationship that are not captured in the template, (b) the fact that the Benson atlas at larger eccentricities was obtained with hemifield stimulation, and (c) a larger impact of any inaccuracies at larger eccentricities because of cortical magnification. As a result, peripheral vertices are more likely to be mis-assigned by the template than central ones. Note that this adds distortion in cortical visual field maps which will be consistent across timepoints (rather than noise). Critically, a reduction in accuracy does not preclude utility if meaningful differences in spatial patterns in cortical sensitivity can still be recovered, as is the case in our data. We cover this in the discussion.

“Particularly at large eccentricities however, we initially observed inaccuracies between the template and individual retinotopy eccentricity estimates which led to substantial distortions in cortical visual field maps due to cortical magnification (see Figure A4 in Appendix section). To address this, we adjusted the Benson eccentricity estimates to align with the cortical magnification scaling function (Horton & Hoyt, 1991).”

“Beyond ROI considerations, we still observed differences in cortical sensitivity between pRF mapping and the adjusted Benson atlas - particularly in the periphery. Several factors likely contribute to this. First, individual differences in the relationship between cortical structure and retinotopy are not fully captured by the template. Second, the Benson atlas has never been fit with empirical data more eccentric than approximately 20°, which naturally limits its precision in the far periphery. Third, because of cortical magnification, any small inaccuracy at larger eccentricities has a disproportionately large effect, making peripheral vertices more susceptible to mis-assignment than central ones. These influences introduce systematic distortions in cortical visual field maps rather than random noise and thus remain consistent across time points - an important point when assessing longitudinal changes (e.g., ageing or gene-therapy interventions). Importantly, the spatial gradients in cortical contrast sensitivity were preserved across both the pRF and Benson atlas approaches, indicating that minor ROI differences do not affect our conclusions. Together, these findings show that the Benson Atlas remains a useful alternative when pRF mapping is not feasible.

R1-3: Overall, the writing could be significantly improved.

AR-R1-3: We have made edits throughout the manuscript and hope this has improved the writing.

Reviewer #1 (Recommendations for the authors):

R1-Recommendation 1a: The writing can be significantly improved for clarity.

The introduction section is not well-organized, and the motivation for developing the current method (Paragraphs 2-3) is vague and lacks adequate documentation.

Several references are missing (e.g., Lines 90-92) or incorrectly placed (e.g., Lines 108-109).

AR-R1-Recommendation 1a: We have revised the Introduction to clarify the motivation for developing the current method and to correct missing or misplaced references.

“Still, testing visual function across the visual field remains limited in clinical and therapeutic contexts, especially in patients with drastic central vision loss. In this study, we aimed to address this gap by introducing a novel fMRI-based approach to measure visual field sensitivity across a wide expanse of the visual field (40º diameter).”

“Beyond visual acuity, functional impairment across the wider visual field can be measured using a range of visual field tests, from the finger counting visual confrontation field test to more complicated and/or computerized tests (e.g., standard automatic perimetry, kinetic perimetry, microperimetry; Rai et al., 2024). Computerized tests typically involve measuring sensitivity to the luminance contrast of a target relative to a background at different visual field locations while the participant’s gaze is fixed on a central point. In some cases (e.g., microperimetry), sensitivity measurements are paired with fundus imaging, offering greater precision in linking visual field functions to specific retinal locations (Rai et al., 2024). As a result, visual field assessments can reveal functionally relevant deficits – including localized sensitivity loss and scotomas – that are not captured by foveal acuity alone, and are therefore potentially valuable for tracking disease progression and therapeutic efficacy.

Despite their clinical relevance, visual field testing comes with challenges and limitations, and as a result, the inclusion of visual field measures in sight-rescuing therapy trials is limited. Firstly, it requires prolonged fixation and sustained visual attention. This can be very challenging for patients with severe vision loss, who often struggle to fixate, and strain to detect even high intensity stimuli. This can lead to long and unpleasant testing sessions with unreliable results. Secondly, as perception of light stimuli is inherently subjective (Rai et al., 2024) and effortful, patients may vary in their criteria for visual recognition, and in their ability to report visual signals that are weakened or distorted by disease. Together, these constraints reduce the feasibility, robustness, and interpretability of conventional visual field testing in clinical trials, underscoring the need for alternative or complementary approaches that can assess functional vision while placing fewer demands on subjective reporting.”

“Functional MRI (fMRI) has recently been proposed as a promising alternative to measure visual field loss, as it requires no overt task, and instead measures visual sensitivity directly from brain responses (Farahbakhsh et al., 2022; Prabhakaran et al., 2021; Ritter et al., 2019). Population receptive field (pRF) mapping fMRI can measure which parts of the cortex respond to which parts of the visual scene (Dumoulin & Wandell, 2008).”

“Finally, most studies use a single maximum contrast stimulus to assess visual function (Broderick et al., 2022; Farahbakhsh et al., 2022; Liu et al., 2006; O’Connell et al., 2016; Ritter et al., 2019).”

R1-Recommendation 1b: The strengths of the current method and its applicable scenarios are unclear. For example, in Lines 39-40: "We developed an fMRIbased approach to measure contrast sensitivity across the visual field without the need for precise fixation." To what extent can fixation be imprecise? Could this protocol be applied to patients with strabismus, who have biased fixation?

AR-R1-Recommendation 1b: We agree with the reviewer that the tolerance to fixation challenges is key here and so we collected additional data to respond to your points regarding the effects of eye movement on the cortical contrast sensitivity maps.

In terms of biased fixation, the approach should be very robust to this, as this would just reduce the cortical visual field covered on one side and extend it on the other.

We collected new data to test the tolerance to fixation instability across a wide range of eye movement, including severe nystagmus-level movement. Despite large eye movements, the cortical contrast-sensitivity pattern remained largely consistent, though extreme movements reduced slope estimates and flattened the cortical sensitivity pattern for 3cpd, indicating reduced measurement sensitivity for extreme eye movement to high spatial frequency gratings.

These additions have been incorporated into the Abstract, Methods, Results, and Discussion sections as follows:

Abstract

“To assess the method’s tolerance to fixation variability, we further investigated how different levels of eye movement affect cortical sensitivity patterns in two participants. We found that cortical sensitivity patterns were largely preserved across eye movement, particularly at low spatial frequencies. This suggests that our approach can accommodate several degrees of fixation instability, making it suitable for populations with unstable or biased fixation for whom visual field maps are harder to acquire behaviorally (e.g., patients with dense central scotoma or strabismus).”

Methods

“Additionally, one participant (C5) repeated the task under two simulated vision loss conditions (ring or quadrant loss), and two others (C5, C6) completed it with different levels of eye movement.”

Results

“Effect of eye movement

Participants C5 and C6 also performed a version of the task designed to test the effect of eye movements. In this version, saccades were elicited by randomly and rapidly shifting the fixation dot away from central fixation (C5: 2º and 5º from fixation and random motion; C6: up to 2º from fixation). Participant C5 was tested using 0.3 and 3cpd gratings at four contrast levels (7.5, 42.2, 60, 100%), while participant C6 was tested only under the low spatial frequency condition (0.3cpd).

Fixation stability was assessed for each fMRI run using the bivariate contour ellipse area (BCEA), which estimates the area (in degrees² or arcmin²) of an ellipse that contains approximately 95% of fixation points. BCEA was calculated using the formula: , as described by Morales et al. (2016). In this expression, σ_h and σ_v represent the standard deviations of eye position in the horizontal and vertical directions, respectively, while p corresponds to the Pearson correlation coefficient between horizontal and vertical eye positions. The constant k determines the size of the ellipse based on the desired probability area, defined by the relationship P =1 – e^-k, with P set to 0.95 in this study. A smaller BCEA indicates greater fixation stability.

“Effect of eye movements on V1 cortical sensitivity

So far, we have demonstrated that our measure of cortical sensitivity can reliably recover known gradients in sensitivity across eccentricities and visual quadrants. We also showed that this measure was consistent across visits and sessions, suggesting its potential utility for monitoring changes over time. However, all prior tasks were conducted under conditions of central fixation, with participants instructed to maintain gaze on a central dot. A key motivation for this approach was its theoretical robustness to fixation instability. We therefore also aimed to investigate how varying degrees of eye movement might influence cortical sensitivity across the visual field.

To address this, two participants (C5 and C6) completed a modified version of the contrast sensitivity task in which they made eye movements either by following a dot moving randomly at a radius of 2º or 5º around fixation, or by self-initiated very large eye movements. Eye movements across these or by self-initiated very large eye movements. Eye movements across these conditions (Figure 7, bottom row; Figure 8, bottom row), were quantified using BCEA (C5 – Central fixation: mean±SD = 0.57±0.11 deg², 2º eye motion: 2.69±0.48 deg², 5º eye motion: 20.3±1.32 deg², random eye motion: 133.7±23.36 deg²; C6 – Central fixation: 0.96±0.56 deg², 2º eye motion: 1.28±0.15 deg²). For reference, in severe (idiopathic) nystagmus, the eye movement variability along the vertical and horizontal planes is on average 1.08 deg and 1.60 deg, respectively (Tailor et al., 2021). Assuming a moderate correlation between axes (p = 0.3), the average fixation stability would equate to a BCEA of ~21.46 deg² (i.e., ~5º eye motion condition in our data).

Despite these very large levels of eye movements, we observed that the overall cortical contrast sensitivity spatial pattern across eccentricity remained remarkably consistent (Figure 7, top and middle rows; Figure 8, top row). However, at the most extreme movements, contrast sensitivity estimates (slope values) were lower; and while the overall cortical visual field map structure was still clearly present for low spatial frequencies, it appeared more flattened for 3cpd, suggesting reduced sensitivity of our measure for large eye movement and high spatial frequency stimuli.”

Discussion

“Crucially, one advantage of cortical visual field mapping is that the maps are inherently centered on the foveal confluence, providing a stable reference point for comparing responses across eccentricities. When combined with large-field, spatially homogeneous stimuli, this anchoring means that our approach should remain robust to moderate fixation variability and still quantify sensitivity changes across the visual field – provided that fixation instability does not exceed the stimulus extent (40º diameter).

When measuring the impact of eye movements, we found that spatial sensitivity patterns were largely preserved, even for extreme eye movements (emulating severe nystagmus). However, under the most extreme conditions, sensitivity estimates (i.e., slope values) were reduced, especially for high spatial frequency (SF) stimuli. This likely reflects image blurring from large rapid eye movements, which degrades high-SF inputs and shifts activation toward neurons tuned to lower SFs. This aligns with evidence that nystagmus and large saccades impair perception of fine detail and grating stimuli due to retinal image slip (Abadi & Bjerre, 2002; Dickinson & Abadi, 1985; Hertle et al., 2017; Randall et al., 2020). While classic findings report suppression of low-SF signals during saccades (Burr et al., 1994; Ross et al., 2001), our results suggest that high SF sensitivity may be more vulnerable to large eye movements when participants are presented with 2Hz phase-flickering gratings. Further validation in clinical groups with naturally-occurring fixation instability would further strengthen these conclusions.”

R1-Recommendation 1c: There are also some confusing descriptions, such as Lines 130-132.

AR-R1-Recommendation 1c: We have also clarified ambiguous descriptions of the Benson atlas templates.

“We therefore also evaluated the approach using the structure-based atlas of retinotopic values developed by Benson et al. (Benson et al., 2014; Benson & Winawer, 2018). This atlas predicts retinotopic organization by aligning individual cortical anatomy (e.g., surface curvature) to a group-average template that incorporates an algebraic model of retinotopy (Benson et al., 2014). Once the subject’s brain is aligned to this structural atlas, retinotopic maps defined by the model – i.e., polar angle and eccentricity maps – are projected onto the individual’s cortex. This allows estimation of visual field maps without requiring functional imaging, and provides a non-invasive, anatomy-driven approximation of visual field representations.”

R1-Recommendation 1d: Line 361: "Assessing the brain's ability to discriminate shapes"-is the author referring to the functional relevance of contrast tuning assessment here? Since the task or stimuli are not related to shapes, this description is unclear.

AR-R1-Recommendation 1d: We have revised the reference to “discriminating shapes” to more accurately reflect the functional relevance of contrast sensitivity mapping.

“To measure visual field function, we developed a new measure of cortical contrast sensitivity, assessing the brain’s ability to discriminate gratings of varying spatial frequencies based on luminance variations.”

R1-Recommendation 2a: Simulated visual loss experiment: only one condition of visual field loss was examined in a single subject. I encourage the authors to include additional subjects to meet statistical test criteria at group level. Simulated scotomas in more visual quadrants, including both central and peripheral areas, should be examined, as asymmetries may exist.

AR-R1-Recommendation 2a: We agree that it is important to verify that the approach can also capture other types of scotomas. We have therefore now incorporated another simulated condition of visual field loss, namely loss of the upper right quadrant.

Regarding adding more participants: The drop in signal is clearly large and significant at the individual level (error bars corresponding to 95% confidence interval do not overlap; Figures 9B-C & 10B). The ability to detect signal change at the individual level is what we need for clinical application, and here we are showing proof-of-concept of its feasibility with our approach. However, we do appreciate that it might be valuable to test cortical visual field loss reconstruction accuracy with simulated scotomas of varying levels of vision loss in variable locations. We now highlight this as a future direction.

Please refer to our response to R1-2a, where we also detail the corresponding changes made in the manuscript.

R1-Recommendation 2b: Additionally, why do the results from pRF mapping and the corrected Benson atlas differ, particularly in the far periphery?

AR-R1-Recommendation 2b: Please refer to our response to R1-2b, where we also detail the corresponding changes made in the manuscript.

R1-Recommendation 3: To validate the recovery of visual field loss in the case study, it would be necessary to include fundus imaging to characterize the structural loss and correlate it with the behavioral and fMRI results.

AR-R1-Recommendation 3: We included Compass perimetry data for the LHON patient, which is fundus-tracked perimetry and uses fundus imaging to keep the visual stimulation fixed to retinal locations.

In the context of LHON, the fundus image is not expected to provide more information than perimetry. This is because the visual deficit in LHON arises from optic nerve dysfunction, and retinal abnormalities are typically minimal. Aside from the characteristic pallor of the optic disc, the fundus appearance is usually normal in appearance.

For illustration, Author response image 1 shows the Compass-acquired fundus image from the LHON patient included in this study. For comparison, we also show a normal fundus image from a 25-year-old male volunteer, reproduced from Häggström, Mikael (2014). "Medical gallery of Mikael Häggström 2014". WikiJournal of Medicine 1 (2). DOI:10.15347/wjm/2014.008. ISSN 2002-4436. Public Domain.

Author response image 1.

We do, however, recognize the importance of linking functional changes to structural alterations (e.g., retinal thickness measured with OCT), and we now highlight this as a key future direction in the discussion. This will be a central focus of a planned follow-up study involving a larger patient cohort.

“Next steps in this work will therefore involve testing larger patient cohorts with diverse forms of vision loss, validating the approach for tracking pathology over time, and investigating how cortex-based visual field measures relate to and complement other visual field and retinal integrity indices including Compass measures and OCT-derived retinal layer thickness.”

“Additionally, linking brain-based variations in function across the visual field to behavioral performance (e.g., perimetry, microperimetry) and retinal structure (fundus imaging, retinal thickness from Optical Coherence Tomography), could help bridge the gap between neural measures and functional outcomes. Such integration would provide deeper insights into developmental, learning, and vision loss mechanisms.”

R1-Recommendation 4a: Why is a 0.5 mm smoothing applied to the contrast task data?

AR-R1-Recommendation 4a: We have now clarified in the Methods section. This 0.5 mm FWHM smoothing kernel was applied to the contrast sensitivity task data to meet the minimum requirements of the GLM module in SPM.

“To accurately capture neural activity across various eccentricities and polar angle locations, minimal smoothing (0.5mm FWHM Gaussian blur) was applied to the contrast sensitivity task data using FSL’s 3dmerge program. This was done to meet the minimum requirements of the GLM module in SPM.”

R1-Recommendation 4b: Is this the first time the cortical magnification calibration has been applied to the Benson atlas? I recommend including a figure to describe this method.

AR-R1-Recommendationn 4b: This is indeed the first time this correction has been applied to the Benson atlas. We have now added a figure (Figure 3) to illustrate the eccentricity adjustment procedure applied to the Benson atlas.

R1-Recommendation 5: In Figure 5, the test-retest reliability can be reported by including r-values.

AR-R1-Recommendation 5: We have now included Spearman correlation 𝜌-coefficients for test-retest and between-condition comparisons in Figure 6 (previously Figure 5).

R1-Recommendation 6: Inconsistency in the reporting format of statistical values: e.g., the degrees of freedom are presented with, or without parentheses.

AR-R1-Recommendation 6: Thank you for pointing this out. We have reviewed and standardized the reporting format of all statistical values throughout the manuscript to ensure consistency. Degrees of freedom are now all presented with parentheses, in details:

“Using ANOVA, we found the expected interaction between spatial frequency and eccentricity (F(1.96,11.79) = 28.66, p < 0.001; Figure 4) as well as a main effect of eccentricity (F(2.33,13.99) = 12.67, p < 0.001).”

“We found a main effect of visual field quadrant location on V1 sensitivity (F(2.46,14.76) = 20.71, p < 0.001).”

“Moreover, there was no interaction between spatial frequency and (F(2.16,12.99) = 1.34, p = 0.298), visual field quadrant positions suggesting V1 visual field anisotropies are relatively constant across spatial frequencies.”

Reviewer #2 (Public reviews):

R2-1a: Questionable sensitivity to differences in patients. The variability in heat maps across healthy control participants is somewhat surprising. Do differences between individuals represent actual visual sensitivity differences, or are they an artifact of the measurement technique, e.g., due to signal-to-noise differences introduced by local variations in brain anatomy? Will the substantial variance across controls allow for a sufficiently stable baseline to detect meaningful differences in individual patients?

AR-R2-1a: We agree the variability across healthy controls is surprising. It is unclear whether this reflects true individual differences in visual sensitivity or arises from factors like local signal-to-noise introduced by local variations in brain anatomy. It will be really interesting to investigate this further by examining structural variations across the visual field and comparing them with behavioral measures.

As for establishing a stable baseline for patient comparisons, this is inherently an empirical question and depends on the degree of vision loss. LHON patients typically show dense central scotomas (up to 15º) in the chronic phase, making them well suited for detecting sensitivity differences – e.g., between central versus peripheral locations. Detecting subtler changes – in the acute phase or other conditions – may be more challenging. We agree with the reviewer that a normative range will be essential for contextualizing patient data, which we now mention in the Discussion, and we aim to develop in the future based on the present data.

“Future work will focus on further validating reconstruction accuracy under controlled conditions, including simulated scotomas of varying severity and location, expanding testing to larger patient cohorts, and establishing a normative dataset to contextualize patient data.”

R2-1b: Also, as the authors rightly point out, Benson atlas does not model differences along meridians, so upper/lower field differences might not be detectable.

AR-R2-1b: We acknowledge the limitations of the Benson atlas, particularly its inability to model meridional asymmetries (e.g., upper vs. lower visual field). Still, our goal is to provide a method for tracking visual cortex changes over time. By consistently projecting longitudinal functional data onto the same structural image fitted with the Benson atlas, we maintain a stable anatomical reference, which supports reliable comparisons across timepoints – even with limited spatial accuracy. Future improvements could include shearing corrections, Bayesian updating, or alternative models such as DeepRetinotopy developed by Ribeiro et al.

“Further enhancing the alignment between retinotopic template atlases and individual retinotopic tuning could improve this approach further, for example, by integrating them with functional measures using Bayesian methods (Benson & Winawer, 2018). In parallel, geometric deep learning frameworks such as DeepRetinotopy (Ribeiro et al., 2021) could also offer anatomy-driven predictions from structural MRI, and combining these strategies may yield more accurate and generalizable retinotopic reconstructions.”

R2-2: Effects of unstable fixation/eye movements not explicitly tested: The methods state, 'In all tasks, participants were asked to report when the color of a central fixation dot changed', suggesting participants maintained fairly good fixation. Most of the results seem to pertain to measurements where central fixation is required. How does unstable fixation affect measurements?

AR-R2-2: This is an important point. We have now extensively and systematically investigated the impact of eye movements on the cortical contrast sensitivity maps and updated the Abstract, Methods, Results, and Discussion sections (see R1-1b).

R2-3: Potential for clinical translation. Although it is a sensitive measure, functional MRI is costly, is not available in all clinical settings, requires significant post-processing analyses, and may be contraindicated in some individuals due to safety (e.g., metallic implants) or other concerns (e.g., claustrophobia). These could present significant barriers to widespread clinical translation if this were the ultimate goal of the study.

AR-R2-3: We agree that fMRI, while sensitive, has practical limitations for broad clinical adoption due to cost, accessibility, and contraindications. However, it remains a valuable tool in targeted contexts, where sensitive detection of visual field loss has large utility – for example for evaluating treatment effects in clinical trials. This application has been demonstrated in recent studies (Farahbakhsh et al., 2022; Maimon-Mor et al., 2025; Haal et al., 2016; Ritter et al., 2019).

R2-4: Limited range of spatial frequencies. The spatial frequencies tested were still quite low (0.3 and 3cpd) compared to measures such as visual acuity. Extending the measurements to higher spatial frequencies could allow better characterization of central vision, although necessarily for peripheral vision.

AR-R2-4: We agree that extending to higher spatial frequencies could improve central vision characterization and note this can be readily incorporated into future studies using the current framework. However, LHON patient’s acuity tends to be very low, and we found that 5cpd did not allow us to measure any cortical contrast sensitivity in a prior pilot. So, to characterize the visual field in LHON with fMRI, we therefore aimed to balance central and peripheral coverage: 0.3 cpd ensured broad detectability, while 3 cpd offered a middle ground to assess central vision without exceeding acuity of this population. Additional approaches, such as neural contrast sensitivity functions (e.g., Roelofzen et al., 2025) may also offer complementary insights such as acuity, and contrast sensitivity across the full spatial frequency range (area under the curve).

Reviewer #2 (Recommendations for the authors):

R2-Recommendation 1: It appears that the reliability measures, comparing differences in Spearman correlations between and within sessions, were not tested statistically, but evaluated qualitatively. What was the justification for this? The results only state Spearman values, but the discussion claims that the differences between the two comparisons were significant.

AR-R2-Recommendation 1: The differences in Spearman correlations between and within sessions were tested statistically, and the omission of p-values was an oversight. We have now revised the Results section results from the paired one-tail t-test as follows:

“We collected test-retest reliability measures from 4 out of 7 participants (Figures 6A-B) and benchmarked them against the correlations between the 0.3cpd condition and 3cpd spatial frequency condition, collected in the same session (Figure 6C). If measures are reliable, correlations should be higher for repeated measures with the same spatial frequency stimulus, collected on different days. We tested this prediction using a one-tailed paired t-test.”

“This difference was statistically significant (t(3) = 2.62, p < 0.0395).”

R2-Recommendation 2a: The variability of heat maps (visual field sensitivities) between healthy controls should also be discussed. What are potential explanations for this variability?

AR-R2-Recommendation 2: We have expanded the Discussion section to address the variability observed in cortical sensitivity maps across healthy controls.

“We also observed intriguing variability in cortical visual field maps across healthy controls, and this variability was consistent across measures. This may reflect genuine individual differences in visual sensitivity that are relevant for behavioral performance. Alternatively, it could arise from factors such as local signal-to-noise differences driven by anatomical variability. However, the fact that maps derived from different spatial stimulus conditions showed markedly different patterns argues against a purely anatomical explanation and suggests that at least part of the variability is functional. Despite this inter-subject variability, variations in cortical contrast sensitivity across eccentricities and visual field quadrants were significant at the individual level indicating high sensitivity.”

R2-Recommendationn 2b: There should also be more discussion about any potential effects of eye movements/unstable fixation in order to address the suitability of the methods for these clinical populations.

AR-R2-Recommendation 2b: Please refer to our response to R2-2, where we also detail the corresponding changes made in the manuscript.

Reviewer #3 (Public review):

R3-1: The authors should more strongly emphasize their findings on the organization of contrast sensitivity, particularly in light of the stimulation extent provided by the wide-field setup.

AR-R3-1: Thank you for this important point – we have now emphasized more clearly in the manuscript that our method extends the measurement of contrast sensitivity to 20º eccentricity, which represents a significant advancement over previous studies.

“These results demonstrate that our approach can detect subtle changes in visual sensitivity across eccentricities at the individual participant level. The ability to reveal these gradients was made possible by the large peripheral coverage provided by our large-field stimulation set-up (see Figure A1 in Appendix section), which enabled a more complete characterization of V1 sensitivity across the visual field. Importantly, the same effects were preserved when using retinotopic estimates derived from structure-based atlases, demonstrating that atlas-based methods can be used as alternative to pRF mapping in cases where it might otherwise be difficult or impossible to directly collect pRF measures. Together, these highlight both the validity of our approach and its potential to broaden the scope of visual neuroscience.”

“Crucially, the ability to visualize these sensitivity gradients was made possible by the large peripheral coverage provided by our large-field stimulation set-up. Such coverage is particularly important for clinical applications, as it enables the detection of visual field losses beyond the macula (i.e., beyond 10º eccentricity) and the evaluation of residual peripheral vision in patients with macular-restricted damage. In doing so, this work provides a useful tool for advancing both basic visual neuroscience and translational research in clinical populations.”

R3-2: Certain methodological aspects require further clarification, particularly regarding the correction of eccentricity values from the Benson atlas. It's not clear which V1 masks are used for the specific analysis which could have a substantial impact on the reported differences between the two approaches of pRF mapping and atlas-based pRF parameters.

AR-R3-2: The correction of eccentricity values was performed using the V1 label provided by the Benson atlas. We have now explicitly stated this in the Methods section:

“We collected data from 7 healthy controls (mean±SD: 29.6±4.7yo; 1M). All controls either had normal or corrected to normal vision, with no other ocular pathologies, and were recruited from the local staff and student pool at the University College of London. Each control completed both the population receptive field (pRF) mapping and the fMRI contrast sensitivity task. To assess measurement repeatability, four participants (C2, C4, C5, C6) performed the contrast sensitivity task twice. Additionally, one participant (C5) repeated the task under two simulated vision loss conditions (ring or quadrant loss), and two others (C5, C6) completed it with different levels of eye movement.”

“Four participants (C2, C4, C5, C6) were invited for a second session in which they repeated the task to assess the reliability of the measures.”

R3-4: The conclusion that high-contrast patterns as in pRF mapping are not optimal to test for subtle but potentially clinically relevant changes in the visual field coverage is very valid. The suggested use of contrast sensitivity can therefore be a potentially well-suited parameter for estimating visual field losses. The presented work is an interesting starting point and the proposed method of using contrast sensitivity as a measure for partial vision loss should further be explored.

AR-R3-4: Thank you for the positive evaluation of our work.

Reviewer #3 (Recommendations for the authors):

R3-Recommendation 1: The shown organization of contrast sensitivities is consistent with previous studies; however, it extends the measurements to up to 20º eccentricity, which is, to my knowledge, much more than previously reported. The authors should therefore emphasize this more strongly.

AR-R3-Recommendation 1: Please refer to our response to R3-1, where we also detail the corresponding changes made in the manuscript.

R3-Recommendation 2: In the Methods section, it is not entirely clear why the eccentricity values originating from the Benson atlas need to be corrected using Horton & Hoyt cortical magnification. Do the authors consider these cortical magnification measurements as ground truth? Is the correction only applied to higher eccentricity values that are not mapped by the Benson atlas?

AR-R3-Recommendation 2: The Benson et al. (2014) atlas predicts both polar angle and eccentricity from cortical anatomy (curvature, thickness) using a template pRF dataset and a mathematical retinotopic model. However, it does not incorporate a smooth parametric cortical magnification function such as Horton & Hoyt. Because the atlas is fit to an average map across subjects, and because the FreeSurfer alignment used to apply the template cannot incorporate functional information, the atlas cannot capture individual variability in eccentricity or cortical magnification. In practice, we therefore treat the Benson atlas as providing the correct topological layout of eccentricity, but not necessarily the correct eccentricity values for a given individual. Moreover, the data used to generate the Benson atlas have mainly been restricted to the central visual field (roughly 8º-12º) and the Benson atlas themselves has never been fit with data more eccentric than 20º. Consequently, peripheral eccentricity values are more model-driven and less constrained by ground-truth data.

To improve the correspondence between the atlas and expected cortical representations, we applied Horton & Hoyt cortical magnification function to all eccentricities in the V1 Benson mask (from the foveal confluence to the periphery, up to 90º). We assume that the Horton & Hoyt model, adapted from physiology data, provides an accurate model of group level cortical magnification (Benson et al., 2021) – even though it does not capture individual differences. This means it offers the best approximation of ground-truth in the absence of individual pRF data, which is often not feasible to collect in patients with unstable fixation. We have now added a figure that showcases the method and shows how this correction affects the distribution of eccentricity values in the Benson atlas.

R3-Recommendation 3: For the analysis using the atlas-based retinotopy, it is not entirely clear whether the authors also use the provided V1 masks. In other words, differences between the original pRF-based and atlas-based analyses could originate from different borders of V1 rather than from the atlas-based pRF parameters. The authors could try using the same mask for both analyses, either the manually delineated one or the atlas-based one.

AR-R3-Recommendation 3: This is a well-noted point that is important to clarify. We used a manually delineated V1 mask for the own pRF map data and the Benson mask for the adjusted Benson atlas-based analysis – both restricted to the screen size. The difference in included vertices could have indeed introduced some additional error beyond the atlas/pRF mapping itself. We have opted not to correct this in this version of the manuscript because (1) the error introduced is likely small (as we inspected that the alignment of V1 ROI delineations with the Benson ROIs are good, so effects are likely not too major - although using identical masks may slightly improve the mapping further in particular the very center and outer-periphery), and (2) our ROI selection for each respective approach is in line with typical procedures used in reality. Critically, the spatial gradients in cortical contrast sensitivity are preserved across the pRF and Benson atlas approach with the different ROIs, so we believe that improvements would not alter our conclusions that Benson offers a useful alternative when pRF mapping is not possible - however, we now highlight this important difference across the two approaches in the paper.

“With this structure-based atlas, we successfully replicated key variations in visual field function (across eccentricity and polar quadrants), although sensitivity to more subtle differences (e.g., upper versus lower quadrant anisotropy) was reduced. This reduction may partly stem from differences in ROI definitions: a manually delineated V1 mask was used for the pRF-based data, while the Benson atlas mask was used for the adjusted Benson atlas analysis. Such differences could introduce minor error beyond the atlas/pRF mapping itself due to differences in the vertices included by each mask.”

“Importantly, the spatial gradients in cortical contrast sensitivity were preserved across both the pRF and Benson atlas approaches, indicating that minor ROI differences do not affect our conclusions. Together, these findings show that the Benson atlas remains a useful alternative when pRF mapping is not feasible.”

R3-Recommendation 4: The patient was measured monocularly. Given the widefield stimulation setup and the fact that the blind spot is located at about 15º eccentricity, do the authors expect to measure this blind spot with the given setup?

Does this have an influence in binocular measurements?

AR-R3-Recommendation 4: This is an interesting point. In theory, our wide-field setup could allow for the detection of the blind spot, as located around 12-15º eccentricity. However, in our LHON patient, the visual field defect typically extends to or beyond the blind spot, making it difficult to isolate its boundary, as shown in Figure 11 (previously Figure 7). Additionally, under binocular viewing, the brain integrates inputs from both eyes to create a unified percept, which may obscure blind spots unless specific paradigms are used (e.g., binocular rivalry or dichoptic tasks). Whilst this is outside the scope of this work, our setup could be adapted to map out the blind spot or explore phenomena like binocular rivalry more directly in future research.

R3-Recommendation 5: How stable is the presented wide-field stimulation setup? In other words, does the eye tracker still capture the eye reliably after small head movements?

AR-R3-Recommendation 5: While small head movements can occur, these were minimized by the use of padding cushions and monitored throughout the session, and the eye tracker maintained reliable tracking throughout the sessions.

R3-Recommendation 6: Are the shown sine-wave gratings always oriented the same? We would expect orientation tuning curves in the early visual cortex; how could this influence the results?

AR-R3-Recommendation 6: For six of the seven control participants (C1-C6), the sinewave gratings were presented with a fixed horizontal orientation. In an updated version of the task – used for participant C7, cases of simulated eye movements, cases of artificial scotoma, and the patient – the orientation of the gratings was varied every 5 seconds among four angles (−45º, 0º, 45º, 90º) during each 15-second stimulus block.

We acknowledge that orientation tuning in the early visual cortex could influence responses, since V1 neurons are selective for specific stimulus orientations and respond most strongly to their preferred orientation. However, we replicated the same overall pattern of results in groups tested with a single orientation and with multiple orientations. Importantly, some participants completed both versions of the task, and the contrast sensitivity patterns remained consistent across conditions. This suggests that the results we report are robust across different orientation-tuned populations for the purposes of this study. A more fine-grained investigation of orientation effects would nevertheless be an interesting direction for future work.

“For six control participants (C1–C6), gratings were initially presented with a fixed horizontal orientation. In an updated version of the task – used for C7, cases of simulated eye movement, cases of artificial scotoma, and the LHON patient – the orientation varied every 5 s among four angles (−45º, 0º, 45º, 90º). Contrast sensitivity patterns were consistent across single and multiple-orientation conditions, including in participants who completed both versions, indicating robustness across orientation-tuned populations.”

R3-Recommendation 7: Are pRF centers also fitted outside the stimulated 20º radius? If yes, were they masked for the analysis?

AR-R3-Recommendation 7: During pRF model fitting, pRF centers were allowed to extend beyond the stimulated visual field, up to approximately 1.5 times the maximum stimulus eccentricity (~30°), to improve model stability near stimulus boundaries. Eccentricity was sampled on a logarithmically spaced grid defined as 2^*, with 𝑥 ranging from -5 to 0.6 in steps of 0.2, and then scaled by the maximum stimulus eccentricity (20°) to express pRF centers in degrees of visual angle. This spacing approach provided finer sampling near the fovea and progressively coarser sampling at larger eccentricities, consistent with cortical magnification principles. For all subsequent analyses of cortical contrast sensitivity, pRF centers located outside the stimulated 20° eccentricity were explicitly excluded. Likewise, although the Benson atlas provides eccentricity estimates extending well beyond the stimulated range (up to ~90°), only pRF centers within 20° were included to ensure consistency across pRF based and atlas-based analyses.

“During pRF model fitting, pRF centers were allowed to extend beyond the stimulated visual field to improve model stability near stimulus boundaries – up to approximately 1.5 times the maximum stimulus eccentricity (~30°). Eccentricity was sampled on a logarithmically spaced grid defined as 2*, with x ranging from −5 to 0.6 in steps of 0.2, and then scaled by the maximum stimulus eccentricity (20°) to express pRF centers in degrees of visual angle. This sampling scheme provided finer resolution near the fovea and progressively coarser sampling at larger eccentricities, consistent with cortical magnification principles.”

“For all subsequent analyses of cortical contrast sensitivity, pRF centers outside the stimulated 20° eccentricity were excluded. Similarly, although the Benson atlas provides eccentricity estimates extending far beyond the stimulated range (up to ~90°), only values within 20° were retained to maintain consistency across pRF-based and atlas-based analyses.”

R3-Recommendation 8: L212: Could the authors please clarify what "scaled across eccentricity to account for cortical magnification" means for the given stimulus?

AR-R3-Recommendation 8: The pRF stimulus was scaled across eccentricity using a logarithmic transformation of retinal radius to approximate cortical magnification. Radial checker boundaries were defined in log eccentricity space (log(r)), resulting in an exponential increase in checker size with eccentricity (scaling factor = 3.2; ~1.37× increase per radial step). As a result, the spatial frequency content of the stimulus decreases with eccentricity (i.e., checker size increases), compensating for known changes in V1 spatial frequency preference across the visual field. This eccentricity dependent scaling inherently relies on precise fixation to stimulate the intended retinal locations, which can be difficult for patients with central vision loss and therefore motivates the use of Benson templates.

“This scaling was implemented by applying a logarithmic transformation of retinal radius, such that radial checker boundaries were defined in log eccentricity space (log(r)), where r denotes to eccentricity relative to the fixation target). This produced an exponential increase in checker size with eccentricity (scaling factor = 3.2; ~1.37 times increase per radial step), resulting in lower spatial frequency content at larger eccentricities – consistent with known variations in V1 spatial frequency tuning. Because this eccentricity dependent scaling assumes precise fixation, it can be challenging for individuals with central vision loss, further motivating the use of Benson atlas templates in such populations.”

R3-Recommendation 9: L213: Three runs were measured per session, were they averaged before analysis or analyzed independently? If analyzed independently, how were the individual results handled?

AR-R3-Recommendation 9: As described in the Methods, data from all three runs were first aligned to an alignment scan that had been co-registered to the MPRAGE image – typically the scan with the fewest outlier voxels, or alternatively, a single-band reference scan in cases of misregistration. The runs were then analyzed as separate regressors in a single design matrix in SPM to account for run-specific variation - following standard recommendations for this software (Author response image 2 shows the SPM design matrix for the GLM). We did not average the runs beforehand due to differences in the order of stimulus presentation across runs. Instead, the GLM modeled each run’s specific presentation sequence to estimate condition-specific beta values, capturing the average contribution of each spatial frequency and contrast level to the BOLD response.

Author response image 2.

R3-Recommendation 10: L289: Did the authors check for very small pRF sizes, as SamSrf is prone to fitting many small sizes?

AR-R3-Recommendation 10: We did not apply an explicit filter to remove very small pRF sizes; we excluded only pRFs with σ > 6.

R3-Recommendation 11: L384: p is missing before the value.

AR-R3-Recommendation 11: Thank you for catching this oversight. We have now added the missing p-value in the revised manuscript.

“Post-hoc tests using Holm-Bonferroni correction show that V1 neuronal populations receiving inputs from the central visual field (0.5-4.5°) showed greater contrast sensitivity to high spatial frequency as compared to low spatial frequency stimuli (steeper slope for the 3cpd versus 0.3cpd condition: 0.5-2.5º: t(6) = 4.35, p_bonf = 0.0149; 2.5-4.5º: 𝑡(6) = 3.471, p_bonf = 0.0266).”

R3-Recommendation 12: I have a very subjective comment regarding the figures. I do not really like the use of the hot colormap in this setting, as I feel it is hard to interpret high and low values.

AR-R3-Recommendation 12: We appreciate the suggestion, but we have had many heated discussions amongst the authors about this and have moved back forth several times before settling. Hopefully the reviewer will be happy for us to stick with the author’s eventually agreed-on subjective preference although we acknowledge that it is by no means a perfect color scheme.

R3-Recommendation 13: L474: Suddenly, a second session appears in the Results section; please report this in Methods.

AR-R3-Recommendation 13: Please refer to our response to R3-3, where we also detail the corresponding changes made in the manuscript.

R3-Recommendation 14: Figure 5C: are the reported results from the first session of the same subjects?

AR-R3-Recommendation 14: That is correct. The results shown in Figure 6C (previously 5C) reflect correlations between slope estimates obtained from the 0.3 and 3cpd conditions within the same session for each subject. We have updated the panel title to “C. 0.3cpd vs 3cpd (within session)” to clarify this point.

R3-Recommendation 15: For the classic pRF mapping (Figure 6D), the artificial scotoma shows lower contrast sensitivity within the scotoma and increased values outside its borders. In contrast, using the retinotopic template (Figure 6E), the area of increased sensitivity is shifted inside the scotoma. Can the authors please comment on this discrepancy?

Is this shift due to systematic differences between the eccentricity values estimated during the pRF run and those derived from the template?

If such a shift exists, is it induced by the eccentricity correction step performed?

AR-R3-Recommendation 15: The shift inside the scotoma observed in the atlas-based analysis (Figure 9E; previously Figure 6E) compared to the pRF-based analysis (Figure 9D; previously Figure 6D) likely reflects residual inaccuracies in eccentricity estimates from the adjusted Benson atlas. While the Horton & Hoyt correction improves the alignment of eccentricity values, it does not ensure perfect matching with the pRF data. Without the Horton & Hoyt correction, the misalignment and shift of activity in the scotoma region are even more pronounced (see below).

We have added a sentence to the Methods section to justify the applied correction. Furthermore, to illustrate the impact of misalignment and its correction on cortical sensitivity maps, we have included an additional figure in the Appendix section showcasing the effect of applying the correction to improve mapping of the artificial scotoma.

“We initially observed inaccuracies between the template and individual retinotopy eccentricity estimates which led to substantial distortions in cortical visual field maps due to cortical magnification – especially in peripheral locations (see Figure A4 in Appendix section).”

R3-Recommendation 16: L532: The age and mutation type of the patient are already reported in the Methods. In general, many Methods and Discussion statements are embedded within the Results section.

AR-R3-Recommendation 16: We are aware that it is a stylistic choice to remind of method in the results and foreshadow discussion. We chose this approach to support the interpretability of the results for less specialist readers.

R3-Recommendation 17: L636: Did the authors consider other options for estimating pRF parameters based on anatomical features, like Ribeiro et al. (2021;https://github.com/felenitaribeiro/deepRetinotopy_TheToolbox).

AR-R3-Recommendation 17: We agree that alternative approaches to estimating pRF parameters based on anatomical features, such as the DeepRetinotopy method proposed by Ribeiro et al. (2021), are promising and worth exploring. In this study, we used the Benson atlas as a starting point, along with an adjustment of eccentricity estimates based on cortical magnification. Future work could compare the performance of different retinotopic template fitting approaches, including deep learning-based methods, to further improve anatomical alignment and functional predictions.

“Further enhancing the alignment between retinotopic template atlases and individual retinotopic tuning could improve this approach further, for example, by integrating them with functional measures using Bayesian methods (Benson & Winawer, 2018). In parallel, geometric deep learning frameworks such as DeepRetinotopy (Ribeiro et al., 2021) could also offer anatomy-driven predictions from structural MRI, and combining these strategies may yield more accurate and generalizable retinotopic reconstructions.”

R3-Recommendation 18: Figure A4: This figure brings up a very important point, namely, whether small eye movements reduce the accuracy of pRF and contrast sensitivity estimates. However, these experiments and results are not reported in the manuscript. I would prefer the authors to add all necessary Methods and Results, or at least not leave this Figure unexplained.

AR-R3-Recommendation 18: We thank the reviewer for highlighting the importance of this figure. To address this point, we collected additional data and have revised the manuscript to include a dedicated section on the effects of eye movements, with corresponding updates in the Abstract, Methods, Results, and Discussion.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) First, a central claim is that arousal modulates functional connectivity in a hemispherically asymmetric and community-specific manner. Although structured asymmetries are demonstrated at the group level, it remains unclear whether these effects reflect a stable neurobiological principle or arise from high-dimensional, connection-wise analyses that are sensitive to sampling variability. Given the interpretive weight placed on hemispheric lateralization, stronger evidence of robustness and individual-level consistency would be necessary to support this conclusion.

We appreciate your critical comments on the robustness of our lateralization findings. We fully agree with you that it is essential to demonstrate that the observed hemispheric asymmetries reflect a stable neurobiological principle rather than an artifact of sampling variability or high-dimensional noise. To address this concern, we performed two rigorous validation analyses using 500-iteration resampling schemes, consisting of a split-half reliability test and a participant-level consistency assessment.

First, to ensure our findings do not depend on specific sample compositions, we conducted a split-half reliability test where the dataset was randomly partitioned into two independent subgroups over 500 iterations. As shown in Figure S1A, the community labels maintained high spatial consistency across iterations (as evidenced by the confusion matrix and Dice coefficient distributions), and our original findings—including network-pair community architecture (Fig. S2A), regional affiliation patterns (Fig. S3A-B), and arousal–tvFC coupling lateralization (Fig. S4A-B)—were consistently situated at the center of the iteration distributions.

Second, to account for potential within-participant dependencies in the HCP 7T dataset, we performed a participant-level resampling analysis (N = 139). By randomly selecting a different session for each participant across 500 iterations, we confirmed that the community architecture and hemispheric biases remain robust even under this strict control (Figure S1A, S2B, S3C-D and S4C-D). Collectively, these additional analyses provide strong evidence that the hemispheric lateralization we reported is not a byproduct of sampling bias, but instead represents a stable organizational principle of the arousal-modulated connectome.

(2) Second, all analyses are based on ultra-high-field imaging. The manuscript does not address whether the reported arousal-related patterns, including the community structure and hemispheric asymmetries, are expected to be reproducible at standard field strengths. It therefore remains unclear whether the findings depend critically on the use of high-field data or whether they would generalize to more widely available datasets, limiting the broader applicability of the results.

We appreciate your constructive comments on the generalizability of our findings across different field strengths.

As you noted, our primary motivation for employing 7T ultra-high-field imaging was to leverage its superior signal-to-noise ratio (SNR) and significantly enhanced BOLD sensitivity. These technical advantages were instrumental in capturing the subtle, moment-to-moment coupling between spontaneous pupillary fluctuations and tvFC—signals that might be close to the detection threshold in standard field strength environments.

However, we fully recognize your point that 3T remains the standard in most clinical and research settings. In the revised manuscript, we have added a dedicated discussion to address this (page 21, lines 447-456):

“Fifth, the findings reported here were derived exclusively from ultra-high-field (7T) imaging data. The superior BOLD sensitivity of 7T fMRI was instrumental in resolving the fine-scale community architecture of arousal–tvFC coupling, which involves subtle signals that may be challenging to detect at lower field strengths. Given that 3T remains the most common parameter for neuroimaging research and clinical applications, future investigations are needed to determine the extent to which these organizational principles generalize to standard field strength data. Validating these motifs in large-scale 3T datasets will be essential to establish their broader applicability across different imaging environments.”

(3) Third, arousal-connectivity coupling is assessed using zero-lag correlations between pupil diameter and time-resolved connectivity estimates. Physiological and hemodynamic considerations suggest that pupil-linked arousal and blood-based imaging signals may exhibit systematic temporal delays. The absence of analyses examining sensitivity to such delays raises the possibility that the reported coupling patterns depend on a specific temporal alignment assumption.

Given the inherent delay of the hemodynamic response function (HRF) and the complex temporal relationship between pupillary dynamics and neural activity, we conducted an additional lagged cross-correlation analysis to test the sensitivity of our findings. Following established frameworks for linking BOLD signals with pupillometry (Yellin et al., 2015; Gonzalez-Castillo et al., 2022; Lloyd et al., 2023), we systematically shifted the pupil time series relative to the fMRI data by -3 TR to +3 TR (-3s to +3s) and evaluated the consistency of the community architecture across these different lags using Dice coefficients.

As shown in Figure S5, these results demonstrate that the community organization remain stable across the tested range of physiological delays. This stability indicates that the arousal-modulated communities we reported are not specific to the zero-lag assumption but instead persist throughout the physiologically plausible lag window. Consequently, our findings reflect a robust neurobiological phenomenon rather than an artifact of a specific temporal alignment.

(4) Fourth, the estimation of time-resolved connectivity relies on a single choice of sliding-window length. The manuscript does not examine whether the reported patterns are stable across different window sizes. Given ongoing concerns about parameter dependence in time-resolved connectivity analyses, sensitivity analyses would be important to establish that the findings are not artifacts of a particular analytical choice.

To ensure that our findings are not artifacts of a specific analytical choice, we performed an exhaustive sensitivity analysis by repeating our entire pipeline across a wide range of window lengths (30s, 35s, 60s, and 90s) and step sizes (1s, 5s, and 10s). We then employed Dice coefficients to quantify the topological similarity between these alternative configurations and our original parameters (30s window, 5s step).

As shown in Figure S5, our results demonstrate high topological consistency, with Dice coefficients for community structures remaining consistently above 0.8 across all tested parameter combinations. These findings provide strong evidence that the arousal-modulated organizational principles we reported are inherent to the data rather than being driven by specific analytical choices in the sliding-window setup.

(5) Finally, the identification of seven connectivity communities is a central result, yet the justification for this choice relies primarily on a single clustering quality measure. In practice, evaluation of clustering solutions typically draws on multiple complementary criteria, including measures of compactness and separation, approaches for selecting the number of clusters, and assessments of stability under resampling. Without such complementary evaluations, it is difficult to determine whether the reported community structure reflects a stable organizational feature or sensitivity to specific methodological decisions.

We agree that relying on a single measure can be limiting, and in the revised manuscript, we have implemented a comprehensive multi-criteria evaluation to justify our selection of K=7. To ensure the robustness of the community partition, we expanded our analysis to include several complementary indices, such as the Davies-Bouldin Index, Calinski-Harabasz Score, and Silhouette Coefficient, alongside the original Within-Cluster Sum of Squares (WCSS), as detailed in Figure S7A.

To further minimize subjective bias in "elbow" detection, we utilized the L-method (Salvador & Chan, 2004), which identifies the optimal K by minimizing the combined root-mean-square error (RMSE) of two linear regression segments. As illustrated in Figure S7B, the RMSE was minimized at K=7, providing a robust mathematical basis for our partition. Furthermore, we systematically visualized the community maps across a range of granularities from K=5 to 9 (Figure S7C). This stability analysis demonstrates that the fundamental topological features and the resulting hemispheric asymmetries are not transient artifacts of a specific K but are consistently preserved as the clustering granularity increases. These additional evaluations demonstrate that the seven-community structure reflects a stable organizational feature of arousal-modulated connectivity

Reviewer #2 (Public review):

(1) Arousal effects on BOLD signals and on pupil size can have different delays, so it would be valuable to test lagged relationships (for example, shifting the pupil series forward and backward) to show that the main community structure and lateralization results are not sensitive to an arbitrary temporal alignment.

We agree with you that accounting for the varying delays between BOLD signals and pupillary dynamics is essential for ensuring the robustness of our results. We conducted a comprehensive lagged cross-correlation analysis to address it. Following established frameworks for linking BOLD signals with pupillometry (Yellin et al., 2015; Gonzalez-Castillo et al., 2022; Lloyd et al., 2023), we systematically shifted the pupil time series relative to the fMRI data by -3 TR to +3 TR (-3s to +3s) and evaluated the consistency of the community architecture across these lags using Dice coefficients.

As shown in Figure S5C, these results demonstrate that the core community organization remain stable across the tested range of physiological delays. This stability confirms that our findings are not sensitive to an arbitrary temporal alignment but instead reflect a robust neurobiological phenomenon that persists throughout the physiologically plausible lag window.

(2) Pupil diameter covaries with blinks, eye closure, and other factors that can covary with head motion and physiological noise. The Methods include substantial quality control and denoising, including motion regression and scrubbing, plus exclusions for eye closure.

We appreciate your attention to these potential confounding factors. While we implemented rigorous preprocessing including regressing out confounds on fMRI images, we agree that physiological noise and motion may influenced pupil signals.

To address this, we conducted an additional control analysis where we included head motion (framewise displacement, FD) and the global signal (defined as the mean signal across all gray matter voxels) as covariates when calculating the arousal–tvFC coupling. We then re-evaluated the similarity between the resulting community architecture and our original findings. As shown in Figure S4, the community structure remained stable after controlling for these variables.

Regarding eye closure, we intentionally did not regress this out, as extensive literature demonstrates that eye closure is itself a reliable physiological proxy for arousal levels (Sommer & Golz, 2010; Chang et al., 2016; Gonzalez-Castillo et al., 2022); regressing it out would likely remove the very arousal-related coupling effects we aim to investigate.

(3) The dataset is described in terms of runs retained (for example, 485 resting runs), and runs are treated as observations in clustering after z-scoring across runs. If multiple runs come from the same individuals, the manuscript would benefit from explicitly showing that results replicate at the participant level (for example, community structure stability within participant across runs, and participant-level summary statistics used for inference), rather than relying primarily on pooled run-level patterns.

We fully agree with you that it is essential to demonstrate that the observed hemispheric asymmetries reflect a stable neurobiological principle rather than an artifact of sampling variability or high-dimensional noise. To address this concern, we performed two rigorous validation analyses using 500-iteration resampling schemes, consisting of a split-half reliability test and a participant-level consistency assessment.

First, to ensure our findings do not depend on specific sample compositions, we conducted a split-half reliability test where the dataset was randomly partitioned into two independent subgroups over 500 iterations. As shown in Figure S1A, the community labels maintained high spatial consistency across iterations (as evidenced by the confusion matrix and Dice coefficient distributions), and our original findings—including network-pair community architecture (Fig. S2A), regional affiliation patterns (Fig. S3A-B), and arousal–tvFC coupling lateralization (Fig. S4A-B)—were consistently situated at the center of the iteration distributions.

Second, to account for potential within-participant dependencies in the HCP 7T dataset, we performed a participant-level resampling analysis (N = 139). By randomly selecting a different session for each participant across 500 iterations, we confirmed that the community architecture and hemispheric biases remain robust even under this strict control (Figure S1A, S2B, S3C-D and S4C-D). Collectively, these additional analyses provide strong evidence that the hemispheric lateralization we reported is not a byproduct of sampling bias, but instead represents a stable organizational principle of the arousal-modulated connectome.

(4) Time-resolved connectivity is estimated using a 30-second sliding window and 5 second step. It is reasonable to wonder whether the same conclusions hold with alternative estimators that do not rely on fixed windows. The Discussion acknowledges this limitation, but adding a small robustness analysis would make the paper more definitive.

To ensure that our findings are not artifacts of a specific analytical choice, we performed an exhaustive sensitivity analysis by repeating our entire pipeline across a wide range of window lengths (30s, 35s, 60s, and 90s) and step sizes (1s, 5s, and 10s). We then employed Dice coefficients to quantify the topological similarity between these alternative configurations and our original parameters (30s window, 5s step).

As shown in Figure S3, our results demonstrate high topological consistency, with Dice coefficients for community structures remaining consistently above 0.8 across all tested parameter combinations. Furthermore, the core hemispheric asymmetry patterns were robustly preserved regardless of the specific windowing configuration used. These results provide strong evidence that the arousal-modulated organizational principles we reported are inherent to the data and are stable across a broad range of temporal scales.

Reviewer #3 (Public review):

(1) A major limitation of the study is the limited discussion of subcortical regions, which play a central role in arousal regulation according to extensive prior literature. Although the current analyses focus primarily on cortical organization, the authors should include a brief discussion of how their findings relate to subcortical arousal systems.

We completely agree that subcortical structures are pivotal drivers of arousal regulation. While our study primarily utilized a symmetric cortical atlas to ensure a mathematically rigorous assessment of hemispheric lateralization, we recognize that the exclusion of subcortical regions limits the functional interpretation of the observed patterns.

In the revised manuscript, we have added a dedicated discussion part (page 20, lines 412-428) to address this point:

“First, to ensure a mathematically rigorous assessment of hemispheric asymmetry, our analysis was restricted to a symmetric cortical parcellation. Consequently, while we demonstrate that arousal-modulated connectivity follows a structured macroscopic architecture, we did not explicitly analyze the subcortical nuclei hypothesized to drive these patterns. We hypothesize that the presence of these low-dimensional cortical communities reflects coordinated motifs rather than a homogeneous gain modulation, potentially mirroring the differentiated projection patterns of subcortical neuromodulatory systems. For instance, the locus coeruleus–noradrenergic pathway (Chandler et al., 2014; Schwarz & Luo, 2015) and thalamus (Hwang et al., 2017; Shine, 2019; Müller et al., 2020; Shine et al., 2023) possess extensive yet non-uniform projections that may anchor the community-specific and hemispherically asymmetric patterns observed here. “

(2) While sliding window methods can capture temporal changes in functional organization, they have limitations in characterizing moment-to-moment neural fluctuations. In particular, results can be highly sensitive to window length and step size. The manuscript would benefit from (a) a clearer discussion of these methodological limitations, (b) justification for the chosen window length and step size, and (c) a sensitivity analysis demonstrating whether the main findings are robust across different parameter choices.

To ensure that our findings are not artifacts of a specific analytical choice, we performed an exhaustive sensitivity analysis by repeating our entire pipeline across a wide range of window lengths (30s, 35s, 60s, and 90s) and step sizes (1s, 5s, and 10s). We then employed Dice coefficients to quantify the topological similarity between these alternative configurations and our original parameters (30s window, 5s step).

As shown in Figure S5, our results demonstrate high topological consistency, with Dice coefficients for community structures remaining consistently above 0.8 across all tested parameter combinations. Furthermore, the core hemispheric asymmetry patterns were robustly preserved regardless of the specific windowing configuration used. These results provide strong evidence that the arousal-modulated organizational principles we reported are inherent to the data and are stable across a broad range of temporal scales.

(2) The authors use k-means clustering to identify groups of brain regions and refer to these groupings as "communities." However, in general, community detection typically refers to graph-based algorithms that identify modules based on connectivity structure (e.g., modularity maximization). The clusters derived from k-means in feature space are not necessarily equivalent to graph-theoretic communities. The authors should explicitly clarify this distinction and adjust terminology accordingly to avoid conceptual ambiguity.

We agree that the term "community detection" is often specifically associated with graph-based algorithms, such as modularity maximization, which define modules based on topological connectivity. In contrast, our implementation of k-means identifies groupings based on the similarity of arousal–FC coupling patterns within a high-dimensional feature space.

To avoid any conceptual ambiguity or potential confusion, we have explicitly clarified this distinction in the Methods (pages 24-25, lines 533-542) section of the revised manuscript:

“We employed the k-means clustering algorithm (Euclidean distance) to explore a range of cluster solutions from K = 2 to 15. To ensure the stability of the results and avoid local optima, each K was repeated 250 times with random initializations. The optimal number of clusters was determined by evaluating clustering quality and reproducibility (e.g., maximizing silhouette stability). It is important to clarify that "communities" in this context refer to clusters of edges that exhibit similar arousal-modulation motifs within a high-dimensional feature space, rather than topological modules typically derived from graph-theoretic algorithms like modularity maximization. This procedure consistently identified seven distinct communities, each representing a robust, arousal-sensitive connectivity motif that characterizes the large-scale organization of brain-pupil coupling.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) To strengthen confidence in the reported hemispheric effects, the authors should provide additional robustness analyses, such as subject-level consistency of lateralization measures, split-half or resampling reliability, and sensitivity to alternative preprocessing or analysis choices. Reporting the distribution of lateralization effects across individuals would help clarify whether the observed asymmetries reflect stable features or group-level averages driven by a subset of connections or participants.

We agree that establishing the individual-level stability of lateralization is essential. We have now provided extensive validation, including split-half reliability tests and participant-level consistency analyses (500 iterations). These results confirm that the reported asymmetries are robust and consistent across the sample. Please refer to Reviewer #1 Weakness2 for the full analysis and associated figures (Figure. S1-S4).

(2) The authors should examine whether arousal-connectivity coupling patterns are robust to plausible temporal delays between pupil diameter and BOLD signals. Lagged or time-shifted analyses would help establish that the findings do not depend on a specific zero-lag assumption.

We agree that validating the coupling between pupil dynamics and the time varying FC is essential. To address this, we conducted a lag sensitivity analysis by shifting the pupil-derived arousal signal within a physiologically plausible range (-3 to +3 TR). The community architecture remains highly consistent across these temporal offsets, showing high spatial correlation and Dice coefficients with our original findings. This stability confirms that the identified organizational motifs are robust and not dependent on a specific zero-lag assumption. For the full details of this validation and the associated figures, please refer to Reviewer #1 Weakness3 and Figure S5 in the Supplementary Material.

(3) Given reliance on a single sliding-window length, the authors should assess how key results vary across different window sizes. Demonstrating stability of the community structure and lateralization patterns across parameter choices would strengthen the methodological foundation of the study.

We have conducted an exhaustive sensitivity analysis across various window lengths (30s, 35s, 60s, 90s) and step sizes (1s, 5s, 10s). The high Dice coefficients (>0.8) confirm that our findings are not dependent on specific windowing choices. Please refer to Reviewer #1 Weakness3 and Figure S5 for the full results.

(4) The justification for the chosen number of connectivity communities would benefit from additional clustering evaluations. Complementary criteria such as measures of compactness and separation, model selection approaches for determining the number of clusters, and stability or reproducibility under resampling would help establish whether the reported community structure is robust rather than method-dependent.

To strengthen the mathematical basis for our partition, we have implemented a multi-metric evaluation and the L-method for objective K selection. These metrics consistently support the seven-community structure. Please refer to our response to Reviewer #1 Weakness5 and Figure S7 for the comprehensive evaluation.

(5) The manuscript would benefit from a clearer discussion of why ultra-high-field imaging was required for the present analyses and whether similar results are expected at standard field strengths. If feasible, validation using lower-field data or reference to existing datasets would substantially enhance generalizability.

We have expanded our discussion to clarify that 7T was instrumental for capturing the subtle, high-frequency arousal-tvFC coupling due to its superior SNR. We also explicitly discuss the potential and limitations of generalizing these findings to 3T datasets. Please refer to our response to Reviewer #1 Weakness2 for the full discussion (page 21, lines 447-456).

(6) The authors should more explicitly report exclusion related to pupil measurements and discuss how missing or noisy pupillometry may affect the applicability of the approach in other datasets or experimental settings.

We agree that transparency in data screening is essential for the reproducibility of our method. In the revised manuscript, we have clarified our quality control pipeline in the quality control section in Methods (page 23, lines 502-510):

“The final analyzed sample for the resting-state consisted of N = 139 healthy participants (mean age = 29.1±3.5 years, 77 female). Runs were excluded if (a) more than 20% of frames exceeded motion thresholds, (b) eye tracking did not cover the full fMRI time series, or (c) more than 90% of samples were classified as eye closure. After applying these criteria, 485 of the initial 723 scans were retained for analysis. The same quality-control pipeline was applied to the movie-watching dataset, yielding 513 usable scans out of the original 725. Detailed information on data retention and run distribution per participant is summarized in Figure S9.”

Furthermore, we have added a discussion regarding how noisy or missing pupillary signals might affect the generalizability of our approach (pages 20-21, lines 437-447):

“Fourth, the generalizability of our approach to external cohorts warrants caution regarding pupillary data integrity. In contexts where high-fidelity eye-tracking is technically demanding—such as in clinical settings involving patients with restricted compliance or in naturalistic fMRI studies—the prevalence of blink artifacts and signal dropouts may bias the estimation of arousal-modulated states. Excessive reliance on data interpolation in such cases could artificially smooth temporal fluctuations, leading to an overestimation of community stability. Future applications should therefore prioritize high-frequency sampling and potentially incorporate multi-modal physiological features (e.g., respiratory or cardiac signals) to cross-validate arousal dynamics when pupillary data is suboptimal (Meissner et al., 2023; Bolt et al., 2025; Weijs et al., 2025).”

(7) The authors should ensure that all data and analysis code necessary to reproduce the results are made publicly available in accordance with eLife policies, including clear documentation of preprocessing steps, parameter choices, and clustering procedures.

All analysis code and the necessary processed data required to reproduce our findings have been made publicly available through https://github.com/kongxy6478/Arousal-modulates-functional-connectivity. This repository includes documented pipelines for pupillometry cleaning and fMRI denoising, alongside the core Python scripts used for sliding-window connectivity calculation, k-means clustering, and hemispheric lateralization analysis.

Reviewer #2 (Recommendations for the authors):

(1) Add a lag sensitivity analysis between pupil-derived arousal and time-resolved connectivity, and report whether the seven community structure and key lateralization findings are stable across a plausible lag range.

We agree that validating the coupling between pupil dynamics and the time varying FC is essential. To address this, we conducted a lag sensitivity analysis by shifting the pupil-derived arousal signal within a physiologically plausible range (-3 to +3 TR). The community architecture remains highly consistent across these temporal offsets, showing high spatial correlation and Dice coefficients with our original findings. This stability confirms that the identified organizational motifs are robust and not dependent on a specific zero-lag assumption. For the full details of this validation and the associated figures, please refer to Reviewer #1 Weakness3 and Figure S5 in the Supplementary Material.

(2) Quantify and report the extent to which residual head motion, blink rate, eye closure segments, and global signal changes explain arousal connectivity coupling, for example, via partial correlation or regression controls, and show that key effects persist.

We agree that it is essential to demonstrate that the observed arousal-connectivity coupling is not driven by non-specific physiological or motion-related artifacts. As requested, we have quantified the influence of head motion (FD) and global signal on our primary results. By implementing partial correlation analyses, we confirmed that the identified arousal-modulated community structures persist even after strictly controlling for these variables. These results indicate that the arousal-tvFC coupling we report reflects a specific neuro-arousal process rather than a byproduct of motion or systemic physiological fluctuations. For the detailed quantitative results and control analysis figures, please refer to our response to Reviewer #2 Weakness3 and Figure S6 in the Supplementary Material.

(3) Add participant-level validation: demonstrate that community profiles and lateralization signatures are consistent within participants across runs, and consider participant-level statistical summaries rather than treating all runs as independent observations.

We agree that demonstrating participant-level consistency is vital. In response, we performed two rigorous 500-iteration resampling schemes: a split-half reliability test and a participant-level consistency assessment (N = 139). These analyses, which involved randomly partitioning the sample and selecting single sessions per participant, confirm that our community architecture and hemispheric biases are remarkably stable and not driven by sampling variability or high-dimensional noise. For a comprehensive description of these validations and the associated statistical distributions, please refer to our detailed response to Reviewer #2 Weakness3 and Figures S1–S4.

(4) Provide an alternative dynamic connectivity estimator robustness check, or at a minimum, vary the window length and step size to show stability of the primary conclusions.

We have conducted an exhaustive sensitivity analysis across various window lengths (30s, 35s, 60s, 90s) and step sizes (1s, 5s, 10s). The high Dice coefficients (>0.8) confirm that our findings are not dependent on specific windowing choices. Please refer to Reviewer #1 Weakness3 and Figure S5 for the full results.

(5) Consider validating the seven community solutions with at least one additional unsupervised approach, and report agreement with the main k-means solution.

We agree that validating the clustering scheme is essential. To this end, we implemented a multi-criteria evaluation (including Davies-Bouldin and Silhouette indices) and utilized the L-method (Salvador & Chan, 2004) to mathematically confirm K=7 as the optimal granularity (Figure S7A–B). Furthermore, we verified that the core topological features and hemispheric asymmetries remain robustly consistent across a range of granularities from K=5 to 9 (Figure S7C). These analyses demonstrate that our findings are not dependent on a specific K or subjective bias. For the full quantitative evaluation and stability maps, please refer to our response to Reviewer #2 Weakness5 and Figure S7.

(6) State explicitly, early in Results, what the main inferential unit is (run or participant) for each key analysis, and clarify how repeated runs per participant are handled.

We agree that defining the inferential unit is critical for methodological clarity. In the revised manuscript, we have explicitly stated at the beginning of the Results section (page 5, lines 113-116):

“While our primary inferential analyses were conducted at the run level to leverage the high-density sampling of the HCP 7T dataset, we further validated the robustness of these findings using participant-level statistical summaries and resampling to account for within-participant dependencies (see Figure. S1-S2 in Supplementary Materia).”

Specifically, all key findings—including community architecture and hemispheric asymmetries—were validated using participant-level statistics and resampling schemes (N = 139) to ensure that the results are not biased by within-participant dependencies.

(7) When introducing the integration and segregation indices, add a brief intuitive explanation of what a positive or negative value means in plain language before the equations.

We thank the reviewer for this suggestion to improve the accessibility of our methods. We have added brief, intuitive explanations for both indices in the Methods section (pages 26-27, lines 569-582):

“The integration index provides a measure of the overall hemispheric dominance of arousal-modulated connections. A positive value indicates that arousal-related edges are preferentially concentrated in the left hemisphere (including its internal and outgoing connections) compared to the right.” and “The segregation index assesses whether arousal preferentially modulates local, intra-hemispheric communication versus long-range, inter-hemispheric communication. A positive value reflects a "segregated" left-hemisphere bias, where arousal strengthens within-hemisphere connections more than it strengthens across-hemisphere communication for that same hemisphere. “

(8) In the Discussion, separate claims into "what we show" versus "what we hypothesize," especially when connecting findings to neuromodulatory pathways.

In the revised manuscript, we have carefully separated our direct empirical findings from our mechanistic hypotheses. we have utilized more cautious and speculative language (e.g., "suggesting a potential role of," "may be mediated by," and "we hypothesize that”) (page 17, lines 352-358):

“Specifically, we show the presence of low-dimensional, reproducible communities suggests that arousal modulates the connectome through coordinated motifs rather than homogeneous gain modulation. We hypothesize that this structured macroscopic architecture reflects the differentiated projection patterns of subcortical neuromodulatory systems, such as the locus coeruleus–noradrenergic pathway (Aston-Jones & Cohen, 2005; Jordan, 2024) and thalamus (Magnin et al., 2010; Lewis et al., 2015; Liu et al., 2018)”

(9) Provide a clear participant-level summary (number of participants contributing to the retained runs, demographics if available, and distribution of runs per participant), alongside the reported run counts retained after quality control.

We agree that clear reporting of participant-level data is essential. In the revised Methods section, we have added a detailed summary of participant demographics (age and sex) and clarified the sample composition (page 23, lines 502-503):

“The final analyzed sample for the resting-state consisted of N = 139 healthy participants (mean age = 29.1±3.5 years, 77 female).”

Furthermore, to provide a transparent view of the data retained after quality control, we have included Figure S9 to illustrate the distribution of valid runs per participant. This visualization confirms the amount of data contributing to our group-level inferences and accounts for exclusions due to motion or pupillary signal quality.

(10) Report the robustness of results to reasonable changes in pupil preprocessing choices (for example, smoothing parameters or interpolation rules), since pupil diameter is the key arousal index.

We agree that the robustness of pupil-derived arousal estimates is fundamental to our findings. To address this, we conducted an extensive validation analysis by comparing our original pupil preprocessing pipeline against 18 alternative combinations of parameters. These variations included different smoothing window sizes (100 ms, 200 ms, and 500 ms), interpolation methods (linear vs. cubic spline), and blink buffer durations (25 ms, 50 ms, and 100 ms). As shown in Figure S8, the pupil diameter time courses derived from these diverse pipelines remained highly correlated with our original estimates (all above 0.65). This demonstrates that our arousal-modulated connectivity results are remarkably robust to reasonable changes in pupil preprocessing choices.

Reviewer #3 (Recommendations for the authors):

I have two additional minor comments:

(1) Given the overall goal of this study to identify large-scale brain communities or clusters underlying arousal, the results may be sensitive to the choice of cortical parcellation. The authors should consider:

(a) including analyses using additional parcellation schemes, or

(b) discussing how the current findings might depend on the chosen parcellation and the implications for robustness and generalizability.

We have addressed this by adding a dedicated point in the Discussion (page 21, lines 456-465):

“Sixth, our findings were derived using a single high-resolution cortical parcellation. While the specific choice of atlas can influence fine-grained regional connectivity, it is important to note that our primary conclusions—such as hemispheric asymmetries and community-level preferences—were identified and interpreted at the macroscopic network and system level. By aggregating signals across broad functional systems, this approach likely mitigates the dependency on precise regional boundary definitions. Nevertheless, future studies employing alternative parcellation schemes would be valuable to further confirm that these organizational principles are not specific to the current atlas but represent a generalizable feature of the arousal-modulated connectome.”

(2) Some key details, such as the number of participants included in the study, as well as basic demographic information, are not reported.

We apologize for this omission. In the revised Methods section, we have now included a detailed summary of the participant demographics, including the final sample size (N = 139), age, and sex distribution (page 23, lines 502-503):

“The final analyzed sample for the resting-state consisted of N = 139 healthy participants (mean age = 29.1±3.5 years, 77 female)”

Furthermore, to ensure full transparency regarding data retention, we have added a new figure (Figure S9) illustrating the distribution of valid fMRI runs per participant following our quality-control procedures. We believe these additions provide a clear and complete overview of the study sample.

Reference

Aston-Jones, G., & Cohen, J. D. (2005). AN INTEGRATIVE THEORY OF LOCUS COERULEUS-NOREPINEPHRINE FUNCTION: Adaptive Gain and Optimal Performance. In Annual Review of Neuroscience (Vol. 28, Issue Volume 28, 2005, pp. 403–450). Annual Reviews. https://doi.org/10.1146/annurev.neuro.28.061604.135709

Bolt, T., Wang, S., Nomi, J. S., Setton, R., Gold, B. P., deB.Frederick, B., Yeo, B. T. T., Chen, J. J., Picchioni, D., Duyn, J. H., Spreng, R. N., Keilholz, S. D., Uddin, L. Q., & Chang, C. (2025). Autonomic physiological coupling of the global fMRI signal. Nature Neuroscience, 28(6), 1327–1335. https://doi.org/10.1038/s41593-025-01945-y

Chandler, D. J., Gao, W.-J., & Waterhouse, B. D. (2014). Heterogeneous organization of the locus coeruleus projections to prefrontal and motor cortices. Proceedings of the National Academy of Sciences, 111(18), 6816–6821. https://doi.org/10.1073/pnas.1320827111

Chang, C., Leopold, D. A., Schölvinck, M. L., Mandelkow, H., Picchioni, D., Liu, X., Ye, F. Q., Turchi, J. N., & Duyn, J. H. (2016). Tracking brain arousal fluctuations with fMRI. Proceedings of the National Academy of Sciences, 113(16), 4518–4523. https://doi.org/10/f8ktgg

Gonzalez-Castillo, J., Fernandez, I. S., Handwerker, D. A., & Bandettini, P. A. (2022). Ultra-slow fMRI fluctuations in the fourth ventricle as a marker of drowsiness. NeuroImage, 259, 119424. https://doi.org/10.1016/j.neuroimage.2022.119424

Hwang, K., Bertolero, M. A., Liu, W. B., & D’Esposito, M. (2017). The Human Thalamus Is an Integrative Hub for Functional Brain Networks. The Journal of Neuroscience, 37(23), 5594–5607. https://doi.org/10.1523/JNEUROSCI.0067-17.2017

Jordan, R. (2024). The locus coeruleus as a global model failure system. Trends in Neurosciences, 47(2), 92–105. https://doi.org/10.1016/j.tins.2023.11.006

Lewis, L. D., Voigts, J., Flores, F. J., Schmitt, L. I., Wilson, M. A., Halassa, M. M., & Brown, E. N. (2015). Thalamic reticular nucleus induces fast and local modulation of arousal state. eLife, 4, e08760. https://doi.org/10.7554/eLife.08760

Liu, X., De Zwart, J. A., Schölvinck, M. L., Chang, C., Ye, F. Q., Leopold, D. A., & Duyn, J. H. (2018). Subcortical evidence for a contribution of arousal to fMRI studies of brain activity. Nature Communications, 9(1), 395. https://doi.org/10.1038/s41467-017-02815-3

Lloyd, B., De Voogd, L. D., Mäki-Marttunen, V., & Nieuwenhuis, S. (2023). Pupil size reflects activation of subcortical ascending arousal system nuclei during rest. eLife, 12, e84822. https://doi.org/10.7554/eLife.84822

Magnin, M., Rey, M., Bastuji, H., Guillemant, P., Mauguière, F., & Garcia-Larrea, L. (2010). Thalamic deactivation at sleep onset precedes that of the cerebral cortex in humans. Proceedings of the National Academy of Sciences, 107(8), 3829–3833. https://doi.org/10.1073/pnas.0909710107

Meissner, S. N., Bächinger, M., Kikkert, S., Imhof, J., Missura, S., Carro Dominguez, M., & Wenderoth, N. (2023). Self-regulating arousal via pupil-based biofeedback. Nature Human Behaviour, 8(1), 43–62. https://doi.org/10.1038/s41562-023-01729-z

Müller, E. J., Munn, B., Hearne, L. J., Smith, J. B., Fulcher, B., Arnatkevičiūtė, A., Lurie, D. J., Cocchi, L., & Shine, J. M. (2020). Core and matrix thalamic sub-populations relate to spatio-temporal cortical connectivity gradients. NeuroImage, 222, 117224. https://doi.org/10.1016/j.neuroimage.2020.117224

Salvador, S., & Chan, P. (2004). Determining the number of clusters/segments in hierarchical clustering/segmentation algorithms. 16th IEEE International Conference on Tools with Artificial Intelligence, 576–584. https://doi.org/10.1109/ICTAI.2004.50

Schwarz, L. A., & Luo, L. (2015). Organization of the Locus Coeruleus-Norepinephrine System. Current Biology, 25(21), R1051–R1056. https://doi.org/10.1016/j.cub.2015.09.039

Shine, J. M. (2019). Neuromodulatory Influences on Integration and Segregation in the Brain. Trends in Cognitive Sciences, 23(7), 572–583. https://doi.org/10.1016/j.tics.2019.04.002

Shine, J. M., Lewis, L. D., Garrett, D. D., & Hwang, K. (2023). The impact of the human thalamus on brain-wide information processing. Nature Reviews Neuroscience, 24(7), 416–430. https://doi.org/10.1038/s41583-023-00701-0

Sommer, D., & Golz, M. (2010). Evaluation of PERCLOS based current fatigue monitoring technologies. 2010 Annual International Conference of the IEEE Engineering in Medicine and Biology, 4456–4459. https://doi.org/10.1109/IEMBS.2010.5625960

Weijs, M. L., Missura, S., Potok-Szybińska, W., Bächinger, M., Badii, B., Carro-Domínguez, M., Wenderoth, N., & Meissner, S. N. (2025). Modulating cortical excitability and cortical arousal by pupil self-regulation. Nature Communications, 16(1), 4552. https://doi.org/10.1038/s41467-025-59837-5

Yellin, D., Berkovich-Ohana, A., & Malach, R. (2015). Coupling between pupil fluctuations and resting-state fMRI uncovers a slow build-up of antagonistic responses in the human cortex. NeuroImage, 106, 414–427. https://doi.org/10.1016/j.neuroimage.2014.11.034

Author response:

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

Reviewer #1 (Public review):

(1) Figure 1A and B: Although a trend is evident, it does not appear that the absolute number of cNK cells at day 14 is significantly changed from day 6.5?

We thank the reviewer for this careful observation. We had not originally performed a statistical comparison between the number of cNK cells present at gds 6.5 and 14.5. We have now conducted the appropriate statistical analysis for this dataset and found that the absolute number of cNK cells at day 14.5 is in fact significantly different from day 6.5 (p = 0.0005; unpaired t test, Mann-Whitney correction). The figure and corresponding legend have been updated to reflect this analysis. Please see Figure 1B:

“Statistics were calculated using unpaired t tests with the Mann-Whitney correction. Error bars indicate SEM; *** p < 0.001.”

(2) Figure 2E: The authors state, "This reduction of uterine trNK cells was accompanied by a concomitant increase in the absolute number and frequency of CD49b+Eomes+ cNK cells within the pregnant uterus of TGF-βRIINcr1Δ dams (Figure 2 D, E). The number of cNK cells appears relatively low (visually ~1,000-1,300), and although the difference is statistically significant, its physiological relevance is unclear. More importantly, this modest increase does not correlate with the marked decrease in trNK and ILC1 populations, as cNK cells do not appear to accumulate. In my opinion, the conclusion "Collectively, these findings indicate that a TGF-β-driven differentiation pathway directs the conversion of peripheral cNK cells into uterine trNK cells during murine pregnancy" should be slightly toned down.

We thank both reviewers for this suggestion. Regarding the absence of cNK cell accumulation in the absence of TGF-β signaling, we suggest that this may be related to the normal passage of cNK cells circulating in the placenta, i.e., these cells may not have acquired signals to remain in the uterus and are simply continuing to pass through and not accumulating. Nonetheless, we have rephrased our wording in to address this concern as follows:

“This reduction of uterine trNK cells was accompanied by a small increase in the absolute number and frequency of CD49b⁺ Eomes⁺ cNK cells within the pregnant uterus of TGF-βRII^Ncr1∆ dams (Figure 2 D, E). Collectively, these findings suggest that a TGF-β–driven differentiation pathway directs the conversion of peripheral cNK cells into uterine trNK cells during murine pregnancy.”

“The absence of cNK cell accumulation in the gravid uterus in the setting of impaired TGF-β signaling suggests a defect in tissue retention rather than recruitment. In the absence of TGF-β–mediated cues, circulating cNK cells that enter the uterine vasculature may fail to acquire the molecular programs required for residency and instead continue to transit through the tissue. This is consistent with a model in which TGF-β signaling promotes not only phenotypic conversion but also the acquisition of retention signals necessary for persistence within the uterine microenvironment, reinforcing that acquisition of tissue-residency in the gravid uterus is an actively instructed process [29,32].”

(3) Figures 2-4: It is unclear whether the littermate controls are floxed mice or floxhet-Ncr1iCre mice? This distinction is important, as Ncr1iCre expression itself could potentially lead to a phenotype.

To address these concerns, we characterized the uterine innate lymphoid cell compartment in the pregnant uterus of Ncr1^icre dams at gestational day 6.5. We did not observe a difference in the absolute number and frequency of trNK cells, cNK cells, and ILC1s in the gravid uterus of Ncr1^icre dams compared to wildtype CD45.1 C57BL/6 mice. Additionally, the number of implantation sites and resorption rates in Ncr1^icre dams was comparable to wildtype CD45.1 C57BL/6 mice. Together these data indicate that Ncr1^icre expression itself does not influence the phenotype we report in TGF-βRII^Ncr1∆ dams. These additional findings have been included in Supplementary Figure 1 and in the text as follows:

“To ensure we exclude a confounding effect of Ncr1^iCre expression, we profiled the uterine innate lymphoid compartment in pregnant Ncr1^iCre dams at gestational day 6.5. No differences were observed in the absolute number of trNK cells, cNK cells, or ILC1s relative to wildtype controls (Figure S1 A-D), and implantation site number and resorption rates were likewise unchanged (Figure S1 E-F). These data indicate that Ncr1^iCre expression alone does not perturb uterine ILC composition or early pregnancy outcomes.”

Reviewer #1 (Recommendations for the authors):

(1) Figure 1C &D: The adoptive transfer experiment is convincing. As a minor point, why is the gate setting for Eomes different between panels 1C and 1D?

To clarify the phenotype of the adoptively transferred cNK cells, we included two additional gates depicting the expression of CD49a and CD49b in unlabeled (non-vascular) trNK cells and cNK cells in the pregnant uterus Please see the revised Figure 1C and revised figure legend:

“(C) Concatenated flow plots of implantation sites showing that adoptively transferred cNK cells in pregnant uterus of wildtype dams upregulate CD49a and down regulate CD49b by gd 10.5, acquiring a CD49a⁺ CD49b^- Eomes⁺ phenotype characteristic of uterine trNK cells (C57BL/6 dams n=4). Here, 2.5x10⁶ CD45.2⁺ CD3^- CD19^- NK1.1⁺ NKp46⁺ CD49b⁺ splenic cNK cells were adoptively transferred into pregnant C57BL/6-CD45.1 dams at gd 0.5, and the receptor profile of these cells was subsequently assessed at gd 10.5. Gating strategy: Live, Single Cells; CD3^- CD19^- CD45.1^- CD45.2–PE-Cy7^- CD45.2–PE⁺ NK1.1⁺ NKp46⁺ cells.”

(2) Figure 3: Has the pup ratio male/female changed?

We did not observe a statistically significant difference in the female-to-male pup ratio between groups.

Reviewer #2 (Public review):

(1) The authors suggest cNK extravasation and local differentiation into iv- trNK. Can it be estimated how much this process contributes to the trNK pool vs. a potential local proliferation of already existing trNK? How do absolute numbers of CD49a+ Eomes+ trNK change during pregnancies? (In Figure 1A, the cell numbers of CD49a+ Eomes+ trNK seem to go down dramatically between gd 6.5 and 14.5). The plot in 1B could also include absolute numbers of ILC1s and trNKs. Would recruited cNK cells compensate for a potential loss of CD49a+ Eomes+ trNK?

Our prior work as well as others have tracked the changes in uterine trNK cells, cNK cells, and ILC1s over the course of murine pregnancy. Consistent with these studies, the absolute number of uterine CD49a⁺ Eomes⁺ trNK cells peaks during early pregnancy (roughly between gds 5.5 7.5) and subsequently declines until term. The decrease in uterine trNK cells between gd 6.5 and gd 14.5 observed in Figure 1A is therefore consistent with the known physiological contraction of the decidual NK compartment as pregnancy progresses. Thus, it is unlikely that cNK cells recruited within the uterine tissue compensate for the loss of CD49a⁺ Eomes⁺ trNK cells observed. To address the reviewer’s request, we have now included the absolute number of uterine trNK cells and ILC1s in Figure 1–please see updated Figure 1C and D and corresponding figure legend (provided below). With respect to the relative contribution of cNK cells extravasation vs local proliferation of trNK cells, our data do not allow us to quantitatively distinguish between these mechanisms. Moreover, previous studies have demonstrated that uterine trNK cells express Ki67, suggesting that they exhibit proliferative activity during this period. Thus, we hypothesize that both local proliferation of existing trNK cells and recruitment of circulating cNK cells contribute to the population of uterine trNK cells during early pregnancy.

“(C) Concatenated flow plots of implantation sites showing that adoptively transferred cNK cells in pregnant uterus of wildtype dams upregulate CD49a and down regulate CD49b by gd 10.5, acquiring a CD49a⁺ CD49b^- Eomes⁺ phenotype characteristic of uterine trNK cells (C57BL/6 dams n=4). Here, 2.5x10⁶ CD45.2⁺ CD3^- CD19^- NK1.1⁺ NKp46⁺ CD49b⁺ splenic cNK cells were adoptively transferred into pregnant C57BL/6-CD45.1 dams at gd 0.5, and the receptor profile of these cells was subsequently assessed at gd 10.5. Gating strategy: Live, Single Cells; CD3^- CD19^- CD45.1^- CD45.2–PE-Cy7^- CD45.2–PE⁺ NK1.1⁺ NKp46⁺ cells. (D) Proportion of uterine ILC subsets derived from adoptively transferred splenic cNK cells in the pregnant uterus of wildtype dams. Statistics were calculated using unpaired t tests with the Mann-Whitney correction. Error bars indicate SEM; ***p < 0.001.”

Barahona, J.D., Yang, L. and Yokoyama, W.M., 2025. Eomesodermin defines uterine NK cells crucial for pregnancy success in mice. The Journal of Immunology, 214(10), pp.2549-2556.

Filipovic, I., Chiossone, L., Vacca, P., Hamilton, R.S., Ingegnere, T., Doisne, J.M., Hawkes, D.A., Mingari, M.C., Sharkey, A.M., Moretta, L. and Colucci, F., 2018. Molecular definition of group 1 innate lymphoid cells in the mouse uterus. Nature Communications, 9(1), p.4492.

(2) Figure 1C: 2.5 Mio cNK cells have been transferred, but only very few cells can be detected within the uterus (concatenated FACS plot shown). What may represent the limit to generate uterine trNK out of cNK? Is the niche supporting cNK-trNK differentiation limited? Is it only a specific subset of (splenic) cNK capable of differentiating into trNK? Is gd 0.5 the optimal timepoint for the transfer? Is there continuous recruitment of cNK into the uterus and differentiation into trNK, or is it enhanced at specific timepoints of pregnancy? Could there be local proliferation of cNK-derived trNK? This could be studied by proliferation dye dilution of WT cNK cells in this transfer-setup.

We recognize that transferring cNK cells at gestational day 0.5–prior to placental formation–may partially account for the low uterine reconstitution observed. At this time point, the local signals necessary for efficient recruitment and retention of cNK cells in the uterus may not yet be fully established, potentially resulting in preferential homing to peripheral tissues such as the spleen and liver. Consistent with this possibility, we do observe a robust population of adoptively transferred cNK cells in the spleen and liver of our pregnant dams. We decided to transfer cNK cells at gestational day 0.5 to ensure that the cells were present at throughout most of early pregnancy, particularly during implantation and the initial stages of decidualization. We also did not transfer cells before mating to minimize the number of mice that did not get pregnant. Additionally, performing the transfer at this early time point minimized repeated manipulation of pregnant dams, as procedural stress itself has been shown to affect physiological processes of gestation and could thereby confound the pregnancy outcomes we were assessing. Furthermore, Filipovic et al. 2018 previously showed that both trNK cells and cNK cells in the pregnant uterus expressed Ki67 at gestational 9.5, suggesting that there could be local proliferation of cNK-derived trNK cells in the gravid uterus that could limit the migration of circulating cNK cells into this microenvironment. We have discussed in more depth in our discussion section as follows:

“Interestingly, the inability to fully reconstitute the uterine trNK cell compartment following adoptive transfer suggests that only a subset of circulating cNK cells may be capable of differentiating into trNK cells during pregnancy, or alternatively that trNK cells already present in the virgin uterus may undergo in situ proliferation in the gravid uterus. Previous studies from our lab as well as others show that trNK cells within the pregnant murine uterus express marked levels of Ki67, supporting a model in which local proliferation of uterine trNK cells is a major contributor to the uterine trNK cell pool during pregnancy [7,32]. Prior studies have also described hematopoietic precursors within endometrial and decidual tissues that generate uterine trNK cells, suggesting that the compartment may be also sustained by local precursor differentiation [33-35]. Together, these findings suggest that uterine trNK cell ontogeny may be more complex than a single-source model and raise the possibility that distinct developmental pathways may operate at different stages of reproductive life. Therefore, defining the relative contribution and developmental timing of hematogenous versus locally maintained sources in vivo could provide relevant insights into the developmental trajectories and transcriptional programs that underlie decidual NK cell heterogeneity.”

Zhai, Q.Y., Wang, J.J., Tian, Y., Liu, X. and Song, Z., 2020. Review of psychological stress on oocyte and early embryonic development in female mice. Reproductive Biology and Endocrinology, 18(1), p.101.

Wiebold, J.L., Stanfield, P.H., Becker, W.C. and Hillers, J.K., 1986. The effect of restraint stress in early pregnancy in mice. Reproduction, 78(1), pp.185-192.

Sánchez-Rubio, M., Abarzúa-Catalán, L., Del Valle, A., Méndez-Ruette, M., Salazar, N., Sigala, J., Sandoval, S., Godoy, M.I., Luarte, A., Monteiro, L.J. and Romero, R., 2024. Maternal stress during pregnancy alters circulating small extracellular vesicles and enhances their targeting to the placenta and fetus. Biological Research, 57(1), p.70.

Filipovic, I., Chiossone, L., Vacca, P., Hamilton, R.S., Ingegnere, T., Doisne, J.M., Hawkes, D.A., Mingari, M.C., Sharkey, A.M., Moretta, L. and Colucci, F., 2018. Molecular definition of group 1 innate lymphoid cells in the mouse uterus. Nature Communications, 9(1), p.4492.

(3) The authors should consider inducible Tgfbr2 deletion (e.g. with Tamoxifen-inducible Cre) to enable development of the uterine NK compartment in virgin mice and only ablate trNK differentiation during pregnancy. This could help to estimate the turnover of cNK into trNK, or to understand if constant cNK recruitment is required to form the uterine trNK compartment during pregnancy.

Thank you for this suggestion. We did initially consider incorporating a mouse model with a tamoxifen-inducible deletion of the TGF-βRII to examine the differentiation of peripheral cNK cells into uterine trNK cells more precisely. However, the administration of tamoxifen during murine pregnancy has well-established deleterious effects on implantation, fetal viability, and placentation, which would confound our interpretations of any adverse pregnancy outcome observed in our studies. Because our goal was to assess NK cell-specific contributions to murine gestation without introducing additional pregnancy-related perturbations, we elected to use an Ncr1^iCre – based mouse model in our studies.

Ved, N., Curran, A., Ashcroft, F.M. and Sparrow, D.B., 2019. Tamoxifen administration in pregnant mice can be deleterious to both mother and embryo. Laboratory animals, 53(6), pp.630-633.

Sun, M.R., Steward, A.C., Sweet, E.A., Martin, A.A. and Lipinski, R.J., 2021. Developmental malformations resulting from high-dose maternal tamoxifen exposure in the mouse. PLoS One, 16(8), p.e0256299.

Ilchuk, L.A., Stavskaya, N.I., Varlamova, E.A., Khamidullina, A.I., Tatarskiy, V.V., Mogila, V.A., Kolbutova, K.B., Bogdan, S.A., Sheremetov, A.M., Baulin, A.N. and Filatova, I.A., 2022. Limitations of tamoxifen application for in vivo genome editing using Cre/ERT2 system. International Journal of Molecular Sciences, 23(22), p.14077.

(4) Did the authors consider transfer of Tgfbr2-floxed Ncr1-Cre cNK in the same setup as in Fig. 1C? This experiment could confirm the requirement of Tgfbr-dependent signaling for cNK to trNK conversion during pregnancy versus effects of Tgfb signals on trNK numbers in the uterus at steady state (before pregnancy).

We thank the reviewer for this mechanistically insightful suggestion. We did consider performing reciprocal transfer experiments using TGF-βRII^fl/fl Ncr1^icre cNK cells in the same adoptive transfer system as in Figure 1C. Our current adoptive transfer experiments already directly address this question. Transfer of congenically labeled wild-type splenic cNK cells into TGF-βRII^Ncr1Δ dams at gestational day 0.5 resulted in partial reconstitution of the uterine trNK compartment and, importantly, this was sufficient to rescue the adverse pregnancy outcomes observed at midgestation. These findings indicate that TGF-β–competent cNK cells can differentiate and function appropriately within the pregnant uterine environment, supporting a requirement for TGF-β–dependent signaling in cNK-to-trNK conversion during pregnancy. Because restoration of TGF-β–sufficient cNK cells rescues these pregnancy outcomes, we believe this experiment functionally demonstrates the importance of TGF-β signaling in this process and therefore did not pursue reciprocal transfer of TGF-βRII–deficient cNK cells.

“Partial reconstitution of uterine trNK cells restores midgestational pregnancy outcomes in TGF-βRII^Ncr1∆ dams

To determine whether restoring uterine trNK cells could rescue the midgestational pregnancy defects observed in TGF-βRII^Ncr1∆ dams, we adoptively transferred wildtype, congenically labeled splenic cNK cells into pregnant TGF-βRII^Ncr1∆ dams at gd 0.5. By gd 10.5, donor cNK cells were detected in the pregnant uterus, where a subset upregulated CD49a and downregulated CD49b, consistent with acquisition of a uterine trNK cell phenotype (Figure 5 A). However, adoptively transferred splenic cNK cells only partially reconstituted the uterine trNK cell population in the gravid uterus of TGF-βRII^Ncr1∆ dams, as evidenced by reduced absolute number and frequency of donor-derived trNK cells in reconstituted TGF-βRII^Ncr1∆ dams (Figure 5 A-C). Notably, this partial reconstitution was sufficient to rescue the gestational defects caused by impaired TGF-β–mediated uterine trNK cell differentiation. Reconstituted TGF- βRII^Ncr1∆ dams exhibited implantation site numbers and fetal resorption rates at gd 10.5 comparable to those observed in littermate controls (Figure 5 D, E). Together, these findings suggest that even partial restoration of the uterine trNK cell in pregnant TGF-βRII^Ncr1∆ dams is sufficient to restore pregnancy outcomes at midgestation, supporting a central role for uterine trNK cells as the principal NK cell subset required for successful murine pregnancy.”

(5) Figures 2D/E: The authors should state that ILC1s are reduced in the virgin uterus of female Tgfbr2-floxed or Tgfb1-floxed Ncr1-Cre mice and cite the relevant work (the Ref #29 discussed in this context did not show that?). It would be helpful to include an analysis of all three uterine ILC subsets in steady state. This could help to answer the question if the cNK cell changes are pregnancy-specific or a general phenomenon in Tgfbr2-floxed Ncr1-Cre mice.

We thank the reviewer for this important comment and for noting the miscitation. We regret the error and have corrected the reference in the revised manuscript to cite the appropriate study demonstrating reduced ILC1s in the virgin uterus of Tgfb1^fl/fl Ncr1^iCre mice {Sparano, C. et al. 2024. Autocrine TGF-β1 drives tissue-specific differentiation and function of resident NK cells. Journal of Experimental Medicine, 222(3), p.e20240930}. Please see Line 148. Importantly, the steady-state ILC compartment in virgin Tgfb1^fl/fl Ncr1^iCre mice has already been carefully characterized in the previously published work, including analysis of all three uterine ILC subsets. Because the steady-state uterine ILC landscape in this mouse model has already been established by Sparano, C. et al. 2024, our study focuses specifically on the pregnancy-associated changes in the uterine ILC landscape occurring in the absence of TGF-β signaling in Ncr1-expressing cells and their subsequent effects on gestational outcomes. In the absence of TGF-β signaling there appears to be a higher frequency of cNK cells in both the virgin uterus and pregnant uterus, suggesting that this is more of a general phenomenon.

“However, in the pregnant uterus, CD49a⁺ Eomes^- ILC1s were markedly reduced in implantation sites of TGF-βRII^Ncr1∆ dams, paralleling the reduction of ILC1s previously reported in the virgin uterus of TGF-βRII^Ncr1∆ female mice [26].”

(6) Figure 2E: Please phrase more carefully about the "concomitant increase" of cNKs, since this increase is much less pronounced compared to the very strong reduction (absence) of trNKs in Tgfbr2-floxed Ncr1-Cre mice. Do the authors suggest that cNKs are halted at this stage and cannot differentiate into trNK, based on these data?

We thank both reviewers for this suggestion, and we have rephrased our wording to address this concern as follows:

“This reduction of uterine trNK cells was accompanied by a small increase in the absolute number and frequency of CD49b⁺ Eomes⁺ cNK cells within the pregnant uterus of TGF-βRII^Ncr1∆ dams (Figure 2 D, E). Collectively, these findings suggest that a TGF-β–driven differentiation pathway directs the conversion of peripheral cNK cells into uterine trNK cells during murine pregnancy.”

Please also see our response to Reviewer #1, Comment #2.

(7) Can the reduced litter size and the abnormal spiral artery formation be rescued by transfer of WT cNK into Tgfbr2-floxed Ncr1-Cre mice?

We thank the reviewers for this interesting question. In subsequent experiments, we transferred congenically labeled, splenic cNK cells from wildtype female mice into TGF-βRII^Ncr1∆ dams at gestational day 0.5. We only observed partial reconstitution of uterine trNK cell population; however, the number of viable implantation sites and resorption rates in reconstituted TGF-βRII^Ncr1∆ dams were comparable to the number of viable implantation sites and resorption rates in HBSS-treated littermate controls at gestational day 10.5. Given that partial reconstitution of the uterine trNK cell compartment in reconstituted TGF-βRII^Ncr1∆ dams was sufficient to rescue the defects in implantation site number and fetal resorption rates observed at midgestation, we hypothesize that this level of restoration may permit patrial but functionally sufficient spiral artery remodeling to reestablish maternal-fetal blood flow adequate to support fetal viability, although spiral artery remodeling was not directly assessed in this transfer study.

“Partial reconstitution of uterine trNK cells restores midgestational pregnancy outcomes in TGF-βRII^Ncr1∆ dams

To determine whether restoring uterine trNK cells could rescue the midgestational pregnancy defects observed in TGF-βRII^cr1∆ dams, we adoptively transferred wildtype, congenically labeled splenic cNK cells into pregnant TGF-βRII^Ncr1∆ dams at gd 0.5. By gd 10.5, donor cNK cells were detected in the pregnant uterus, where a subset upregulated CD49a and downregulated CD49b, consistent with acquisition of a uterine trNK cell phenotype (Figure 5 A). However, adoptively transferred splenic cNK cells only partially reconstituted the uterine trNK cell population in the gravid uterus of TGF-βRII^Ncr1∆ dams, as evidenced by reduced absolute number and frequency of donor-derived trNK cells in reconstituted TGF-βRII^Ncr1∆ dams (Figure 5 A-C). Notably, this partial reconstitution was sufficient to rescue the gestational defects caused by impaired TGF-β–mediated uterine trNK cell differentiation. Reconstituted TGF-βRII^Ncr1∆ dams exhibited implantation site numbers and fetal resorption rates at gd 10.5 comparable to those observed in littermate controls (Figure 5 D, E). Together, these findings suggest that even partial restoration of the uterine trNK cell in pregnant TGF-βRII^Ncr1∆ dams is sufficient to restore pregnancy outcomes at midgestation, supporting a central role for uterine trNK cells as the principal NK cell subset required for successful murine pregnancy.”

Reviewer #2 (Recommendations for the authors):

(1) Figure 1C: The shown gate seems to "cut" into the CD49b staining; staining for all transferred cells should be shown; have cNK cells been stained in parallel with the same panel to provide a positive and compensation control?

To clarify the phenotype of the adoptively transferred cNK cells, we included two additional gates depicting the expression of CD49a and CD49b in unlabeled (non-vascular) trNK cells and cNK cells in the pregnant uterus Please see the revised Figure 1C.

“(C) Concatenated flow plots of implantation sites showing that adoptively transferred cNK cells in pregnant uterus of wildtype dams upregulate CD49a and down regulate CD49b by gd 10.5, acquiring a CD49a⁺ CD49b^- Eomes⁺ phenotype characteristic of uterine trNK cells (C57BL/6 dams n=4). Here, 2.5x10⁶ CD45.2⁺ CD3^- CD19^- NK1.1⁺ NKp46⁺ CD49b⁺ splenic cNK cells were adoptively transferred into pregnant C57BL/6-CD45.1 dams at gd 0.5, and the receptor profile of these cells was subsequently assessed at gd 10.5. Gating strategy: Live, Single Cells; CD3^- CD19^- CD45.1^- CD45.2–PE-Cy7^- CD45.2–PE⁺ NK1.1⁺ NKp46⁺ cells.”

(2) Figure 2A: The authors could include an isotype control or a staining in a genetic knockout as a control staining.

Thank you for this suggestion. As suggested, we included staining in a genetic TGF-βRII^Ncr1∆ knockout as additional control staining. Please see the revised Figure 2A.

“Representative histograms depicting TGF-β Receptor II expression on splenic NK cells from virgin TGF-βRII^Ncr1∆ and wildtype mice as well as splenic and uterine NK cell subsets from pregnant wildtype mice at gd 10.5 (virgin TGF-βRII^Ncr1∆ mice, n=2; virgin mice: C57BL/6, n=5; gd 10.5: C57BL/6 dams, n=8, implantation sites n=8). MFI, median fluorescent intensity. Gating strategy: Live, Single Cells; CD3^- CD19^- CD45.1^- CD45.2⁺ NK1.1⁺ NKp46⁺ cells.”

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors generated mouse and zebrafish models for DeSanto-Shinawi Syndrome, caused by loss-of-function variants in the WAC gene. Using these vertebrate systems, they demonstrate conserved craniofacial and social-behavioral phenotypes that parallel human clinical features, along with deficits in GABAergic markers. They observe increased seizure susceptibility and male-biased brain volumetric changes in Wac mutant mice. Together, these findings begin to define the biological consequences of Wac haploinsufficiency and provide valuable resources for future mechanistic studies.

Strengths:

WAC is a high-confidence neurodevelopmental disorder gene and one of the genes identified by large-scale exome sequencing efforts, including the Satterstrom et al. (2020) autism spectrum disorder cohort. This study establishes the first vertebrate Wac models, addressing a major gap in the understanding of DeSanto-Shinawi Syndrome, and provides a framework for studying other syndromic forms of autism. The models generated will be impactful and useful to the community to study and understand DeSanto-Shinawi Syndrome.

The cross-species analysis is important and well executed, and reveals both conserved and divergent phenotypes. The behavioral and anatomical assays are rigorously executed and well-controlled, and the inclusion of RNA-sequencing analyses adds valuable insights into the mechanisms underlying brain function in Wac mutants. Notably, the RNA-seq data reveal upregulation of several clustered protocadherins, genes central to neuronal identity and cell-cell interactions, which are known to be regulated by dynamic developmental regulation of chromatin architecture. This observation provides an intriguing hint that could link Wac function to higher-order chromatin organization and neuronal connectivity.

Weaknesses:

The evidence is solid, but the study remains incomplete in its mechanistic depth and molecular interpretation. The authors compellingly describe behavioral, anatomical, and transcriptomic phenotypes associated with WAC loss, yet do not explore how WAC mechanistically regulates chromatin or transcription. Given prior evidence that WAC interacts with the RNF20/40 ubiquitin ligase complex and promotes histone H2B ubiquitination and transcriptional elongation, the paper would benefit from a discussion of these functions as a potential link between Wac haploinsufficiency and the observed changes in neuronal gene expression. Similarly, the authors mention WAC's WW and coiled-coil domains but do not consider how these domains could mediate nuclear interactions or recruitment of transcriptional cofactors that shape gene regulation and chromatin organization in neurons.

We agree that many mechanisms underlying how both animal model phenotypes and human symptoms that are caused by the Wac gene still need to be worked out. Due to the need to generate a great deal of data to first describe these models in this manuscript this will be expanded upon later. In lieu of this, we plan to follow up with mechanistic papers later to fully address the gap that remains. We have now added a paragraph in the discussion to bring up these important points regarding the roles of Wac during transcription and how its protein domains might be involved in these processes.

The transcriptomic analysis is rich but largely descriptive. Although the upregulation of clustered protocadherins is particularly intriguing, these findings are not validated or localized to specific neuronal populations. The study would be strengthened by independently validating the most significant RNA-seq changes, such as protocadherin gamma genes, using in situ hybridization methods to confirm the spatial and cellular specificity of expression changes.

We have greatly expanded the analyses of the bulk RNA-seq data, including a more rigorous look into the differences in gene expression between sexes, which has additionally revealed males to be more impacted by Wac loss of function. We have also added new western blot data for pan protocadherin alpha, which is now validated to be upregulated in the cortex (new Figure 7I and 7J). We are holding back any additional data from this report as we have single nucleus RNA-seq data that will be reported on in follow-up papers with targeted conditional deletion models.

Finally, while the behavioral and MRI results add valuable breadth, their interpretation would be improved by clearer reporting of sample sizes, statistical corrections, and effect sizes to support claims of sex-specific and regional brain volume differences.

Some additional details have been added to the methods section. In addition, we have now provided sample sizes assessed in each figure legend.

Reviewer #2 (Public review):

The authors describe the first deep neurological characterization of WAC mutation in two vertebrate species (zebrafish and mouse). They examine these at various levels, guided by the work in humans that has associated a heterozygous WAC mutation with DeSantos Shinawi Syndrome (DESSH). Therefore, they investigate the animals for a variety of phenotypes, following a template for what is seen when characterizing a new mouse/fish model of a developmental disability gene. Investigations include analysis of skull and jaw for abnormalities(both species), MRI of brain structure(in mice), electrophysiology(mice), assessment of signaling pathways (by Western blot, in mice), cell counts (both, more in mice), transcriptomics (mice), and behavior (both).

Generally, this describes an important first characterization of the consequences of the mutation. Most of the studies appear well-conducted and reasonably powered, thus solid or convincing. However, there are a few places where the data presentation could be improved for clarity, and a few concerns about some choices in analytical approach for a couple of the experiments, where improved statistical approaches could improve their sensitivity and/or better rule out false positives, and thus the support of some of these claims is currently incomplete. There is also some lack of clarity about the rationale for some decisions regarding the fish genetics. Nonetheless, this is an important and useful first characterization of many phenotypes of these lines. Such experiments form a baseline for future mechanistic studies in the same lines and a platform to test approaches to reverse phenotypes.

Individual claims and their strength & weaknesses:

(1) The authors developed mouse and zebrafish models of WAC deletion

They used the existing KOMP floxed WAC line to generate a null allele. For the mouse, there is a Western showing that it is indeed null for the protein. The fish data is less robustly validated - they don't confirm the allele in null at the protein or RNA level, and fish have two paralogs (waca and wacb), and this paper only characterizes one of these. So this evidence is less clear. The evaluated mice are heterozygous (Het), similar to patients, while the fish appear to be evaluated as homozygous mutants.

We agree with the reviewer’s comments on zebrafish genetics. Since antibodies against zebrafish Wac proteins are not available, we could not examine protein levels in zebrafish. We predicted frameshift mutations due to DNA analyses in waca and wacb KO zebrafish. We made waca KO, wacb KO, and waca/wacb double KO zebrafish. waca/wacb double KO zebrafish showed a lethal phenotype, similar to homozygous mice mutants. Since wacb KO zebrafish did not show any detectable phenotype we do not report those here. However, we now show examples of the wacb and dKO zebrafish in Figure S1. Since waca KO zebrafish showed craniofacial and behavioral phenotypes that are comparable to mice Het and human patients, they are focused on in this report.

(2) The authors show that both species show altered craniofacial features

These data appear well powered, and the findings are robust.

We appreciate this confirmation.

(3) Each model altered GABAergic neurons

In mice, the authors stained with PV antibodies and saw a decrease in cells positive for this staining. A second marker, Lhx6, does not show a difference, suggesting this might be a change in PV expression rather than cell number. They could maybe look into the literature to see if this loss of just the protein also occurs in other models. Overall, the sample size here is a bit smaller than other parts of the paper (n=3), and the methods on the cell counts were less clear, so it is not as clear that this finding is as robust. The authors counted several other broad classes of cells, and those appear normal. Interestingly, there might also be some TBR1 mislocalization in layer 6 that might be significant with added power.

Thank you for these suggestions. Yes, other models also show this lack of PV expression even when MGE-lineage interneurons are present at normal levels. We mention in the discussion a previous study on the ASD gene CTNNAP2 that showed this. We also agree that there is a trend going on in the Tbr1 population. We assessed another WT and Het pair for Tbr1 laminar distribution and were able to determine that these changes held up and are now significantly different; the person counting these numbers was blind to the genotypes. Finally, we added more details to the methods to describe how the counting was performed.

The fish data is based on an in situ hybridization for GAD. The measure shown is the width of the positive area in the forebrain. This measure is not one I have seen much before, and has potential to be driven by something unrelated to GABA (e.g., if the whole forebrain were simply a bit smaller). So this analysis could use a couple of other approaches (density of signal?) and/or a control probe for some other brain gene showing the measure is normal, and thus it is not just a size issue.

To compare altered GABAergic neurons in mice and zebrafish, we tried to isolate zebrafish PV genes and examined their expression by whole-mount in situ hybridization, now included Figure S3 but found no differences. However, we could not find any zebrafish PV gene useful for GABAergic neurons. We chose to examine gad1b expression in the positive area of the forebrain in WT and waca KO zebrafish and then found differences in the brain area with gad1b expression. Since WT and waca KO brain sizes are generally the same we believe this measurement is reasonable to make this conclusion and have added text to the results section to justify.

(4) Mice were more susceptible to the seizure-inducing agent PTZ

These data appear well powered, and the findings are robust. The authors also did a fair amount of useful electrophysiology that was all normal, but appeared to be well executed.

Thank you, we appreciate this confirmation.

(5) Mice had changes in brain volume that interact with sex

The authors conducted an MRI on a good number of mice and reported a slight increase in global volume just in males. Sample size is fair, but the statistical approach here may be better if it puts males and females in the same model (to boost power and explicitly test for sex by genotype interaction that they report), and there is some chance that the brain region level differences that they report could include some false positives. They tested many regions, and it is not clear whether or not they corrected for the number of tests. Often, an FDR correction would be used in such imaging studies. It may be that only the most robust regional findings will survive those corrections. It is interesting data either way, but the analysis could be improved.

Given the 80 regions (bilaterally) that we used and the number of mice, i.e. 6-7, we are underpowered to robustly undertake FDR types of corrections. In the data presented we used t-tests between sex and regions to illuminate putative regional changes. However, we did revisit our MRI data and found three data sets where the results were not normally distributed. We thus changed our statistical test to Mann Whitney for male retrosplenial cortex, male parietal cortex and female corpus callosum, which are now reflected in the figures and differential statistics noted in figure legends.

(6) Several behaviors are altered in the mice as well

These studies were fairly well-powered (n=15,16), and they found several positive and negative results, including alterations in memory and sociability in both species. There is a minor statistical flaw in the three-chamber analysis (they don't actually compare the Hets directly to the wildtypes in their statistical testing - a common mistake in neuroscience that should be addressed. But the data look like they will probably still be significant when correctly analyzed. In the supplement, the authors could do a bit more with the data they have to look at hyperactivity (i.e., show total motion in open field, not just time in center vs. periphery), and adding sex to their model might improve sensitivity for genotype effects.

Thank you for these suggestions. We have done several things to address this behavioral paradigm. First, we added more n’s and also switched from comparing the mouse vs. object to just comparing genotypes as a variable. In addition, we switched to quantifying a discrimination index, described in Phiilips et al., 2019 PMID: 31112129 for our measurement. These new data are shown in Figure 3A. Open field total distance traveled has now been added to Figure S2A. For all other measurements, we did first assess for sex differences but found none and thus compiled both sexes for the graphs.

(7) Some biochemical signaling pathways are altered in the brain

These are n=4 immunoblots, and show altered phospho ERK, but no changes in other signaling events predicted from prior WAC literature like H2B ubiquitination. They appear well done, and the authors share the full blots in the supplement.

Thank you, we appreciate this confirmation. Since Wac is an adaptor protein we needed to test these reported molecular changes in neurons that were previously only reported in cell lines and drosophila. We were not surprised that some of these previously reported changes would not be the same in brain cells. However, it is possible that these changes might arise in more discrete brain regions or at different times during development, which will be tested in our future conditional knockout models.

(8) WAC deletion also alters gene expression in the brain

These studies were well-powered for RNAseq, with 10 and 14 samples, using neonates (P2), just the forebrain. The sequencing quality metrics all looked good, and the approach to analysis was okay. It would be stronger to again include sex in the model, rather than separate by sex. There were some typos in this part of the paper that made part of the conclusions unclear, but the RNAseq nicely confirmed the mutation of the mice, and discovered many differentially expressed genes, consistent with the role of this gene as a regulator of transcription. The presentation could be expanded to make more use of the data. Overall, though, this is a useful first characterization of the transcriptome in the line.

Thank you for the suggestions. We have greatly expanded our assessments of the RNA-seq data. Upon analyzation of the data we found many differences between males and females and now show combined and sex-separated data. Our new data isolate several more extreme and some unique changes in males that are better shown as stand alone figure panels. In addition to these edits, we have also reworked all the text in this section of the results for better reading.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The cause and timing of lethality in the homozygous Wac knockout should be reported or discussed. Investigating Wac homozygous knockout embryos, if viable at early stages, could provide valuable insight into the developmental origins of the neuroanatomical and behavioral phenotypes described in the heterozygous animals. Even a brief histological or transcriptomic characterization of embryonic brains would strengthen the mechanistic understanding of Wac function during neurodevelopment.

We agree and have collected embryos as early as embryonic day 12.5 from multiple litters but never detected a knockout. We have added this text to the animal methods sections to let readers understand effort had been done to determine when death occurs. While we don’t currently explore this further in mice we now include zebrafish waca; wacb double knockouts. Notably, while we were able to generate a few of these mutants, most died. However, some zebrafish were aged long enough to observe lethal deficits in heart formation and swim bladder development, suggesting that early loss of Wac could impact these critical organs that leads to death.

(2) A better description of the data reported in Supplementary Tables 3 through 5 is needed. Supplementary Table 3 does not report any statistically significantly differentially expressed genes in the FDR column, and Supplementary Table 5 reports only two, and the reader should understand what the columns are indicating.

We have now added figure legend text to the supplementary file to explain each Table mentioned here.

Reviewer #2 (Recommendations for the authors):

(1) Page 3, last paragraph. The description of wacb is confusing. I recommend that the authors provide the unshown data they mention and also further explanation of the breeding scheme and result. Indeed, if wacb is homozygous lethal, does that make it more like the mouse WAC gene, and thus potentially the more relevant paralogue to study? Are both waca and wacb expressed in the same tissues? How does that compare to mouse and human WAC expression? Such figures about gene expression (even when adapted with permission from public resources like Allen brain atlas or GTEX) are common in this sort of paper, as they can be helpful to understand when and where the gene is thought to act. For waca vs. wacb, they may help determine which gene is more relevant to the brain (for example, if only one is expressed in the brain).

First, this is a great question and we have now added whole mount in situ for the waca and wacb genes as Figure S1. These data show low to no wacb expression in brain regions while waca is highly expressed there. Since the waca mutants showed phenotypes relevant to DESSH but wacb mutants did not, this correlates with observed expression patterns without fully excluding wacb from any role. Thus, we also made waca/wacb double KO zebrafish that showed a lethal phenotype, similar to homozygous mice mutants. Only a few waca; wacb double knockouts survived a little through development and are now shown in Figure S1. Since wacb KO zebrafish did not show any detectable phenotype on their own, we did not include the data since there are already several figures/tables in this manuscript. However, the waca KO zebrafish did show phenotypes similar to humans with DESSH and are the ones we focused on.

(2) Why did the authors cross the mice into the outbred CD1 background? Usually, most labs keep the lines on an inbred background. Was there a particular rationale here? I am not saying that they could not outcross them. It is just a bit puzzling why. Perhaps a sentence of explanation in the methods section would be warranted.

This is a great question and we have now added text to the animal methods section. Many labs that study development, especially on genes critical for survival/life like the Wac gene, use a more robust strain like CD-1. By doing this, we have a better chance of evaluating mutants at more mature ages and getting enough progeny to do more reproducible studies.

(3) A typical first experiment in a new knockout (fish or mouse) is to establish that the deletion does indeed result in a loss of RNA and protein. In the absence of this, the rest of the paper cannot be as confidently interpreted.

We did this for the mouse model and found reduced protein expression in the constitutive Het, however this datum is part of the western blots in figure 5. We now mention this in the early results section that protein levels were reduced in the Hets but maintain that the presentation of the western blot is better suited in Fig. 5 to compare to the other western blots. For zebrafish this was attempted but was more difficult. Available antibodies don’t work in zebrafish. RNA expression was attempted in both models and due to Wac being a critical gene for life, there are checks in place to upregulate faulty and normal RNA in the waca model. We screened for frameshift mutations in multiple KO lines and confirmed it by genomic DNA sequencing. In making many KOs and large-scale mutagenesis in zebrafish, we usually depend on phenotype-genotype segregation in Mendelian inheritance for many generations.

(4) Are these new lines indeed knockouts? I did find a WAC western as part of a later figure for the mouse. The authors may want to mention that earlier, or present at least that data right away. What about in the fish? Is there a way to confirm at the RNA or protein level that it is indeed a null allele?

Yes, as mentioned in the above response we have now mentioned our Wac western blot results early when introducing the mouse mutants and the issues with doing this in fish are presented above as well.

(5) Why are fish used that are KO while mice are Hets? Are WAC homozygous mice not viable? This should be mentioned. Regardless, the rationale for examining heterozygous mice and homozygous mutant fish should be provided. Each kind of experiment is useful, but they are interpreted in different ways. Hets will genocopy the patients, who are generally hets, while KOs are often useful for a study of the essential roles of the genes, even if they are not really modeling the patient gene dose.

Wac homozygous mice in our hands are embryonic lethal, now mentioned in the animal methods section, but we found early on that the Hets mimic several human DESSH patients. In zebrafish it is more complicated. We analyzed waca and wacb hets in zebrafish but found no phenotypes. This could be in part due to some complementation between the waca and wacb genes. It is also possible that a full waca KO could resemble a human DESSH individual since wacb may complement somewhat, even though deleting wacb entirely does not have a measurable phenotype. We have added more text to the discussion to explore these complexities. We also made waca/wacb double KO (dKO) zebrafish but they showed lethal phenotype, similar to homozygous mice mutants and suggesting some complementation by the wacb gene even though alone it did not exhibit phenotypes.

(6) Figure 3A: It does not appear that the authors are directly statistically comparing the two groups (genotypes) that they are drawing conclusions about. This is an unfortunately common mistake in the neuroscience literature across papers. There is a nice older review about it here. https://pubmed.ncbi.nlm.nih.gov/21878926/. To draw conclusions about the differences between the mouse genotypes, they need to compare the two genotypes directly with a statistical test. See Nygard et al for a recommended approach, like comparing social preference indexes

(https://onlinelibrary.wiley.com/doi/abs/10.1002/aur.2154).

Thank you for this information. Previous reviewers at a different journal asked for this particular evaluation. We have now made changes to address the assessment, and graphs now reflect comparisons of genotypes instead of a single genotype between time with a mouse or object. We have also moved to using a social discrimination index to compare the genotypes, similar to the study mentioned.

(7) MRI - it is a bit weird to separate the male and female brains just for the MRI. Was there a premise from human data to do so? If not, the authors should probably pool them. If they are concerned there are sex effects (or, more likely, a sex by genotype interaction) I recommend that they use a two-factor ANOVA and simply put both sex and genotype into the model. This will also have the advantage of increasing their statistical power for genotype effects a bit. If their current results are robust, they will still show up as a significant sex x genotype interaction.

All data in the manuscript initially compared the sexes to each other. We have now added this text to the animal section of the methods: For MRI, some zebrafish behaviors and now the RNA-seq data, sex was a difference and due to this observation, sex was (or now is) presented independently for these measurements. We now state that if no sex differences were observed the data were pooled.

(8) Also, did the authors correct for multiple testing in the MRI analysis? Since they are testing many regions, there is a risk of false positives if they do not. This could be confounded further by their splitting the data by sex, thus doubling the number of tests.

As noted above we did not do multiple corrections given the large number of regions and low number of replicates.

(9) How many images per animal were analyzed for the cell counts? This detail is absent from the methods and would help with evaluating the robustness of these findings. What other approaches were used to make sure the counting was unbiased?

We analyzed 3-4 images per animal for counts and counted hundreds of cells per image. In addition, the person counting was blinded to avoid any bias. These details have now been updated in the methods.

(10) As with the MRI, for the DEG analysis, I recommend the authors simply put sex and genotype into the same model as two factors (with an interaction), to increase their sensitivity to genotype effects, as well as be able to report on robust genotype x sex differences, if there are any. They may also consider testing the model with and without excluding the three outlier animals on their PCA. It may be that the noise of those outliers is detracting from their sensitivity for DEGs somewhat.

We greatly expanded our analyses and found more robust and unique changes in males that are now added to Figure 7 and supplemental files. After considering the data, decided to highlight the sex differences separately.

(11) A few more relatively simple things could readily be done with the RNAseq data to add some depth and interpretation. For example, do the hits here overlap other published IDD/autism DEG lists from mouse knockouts studies of genes like FoxP2, Chd8, Dnmt3a, Myt1l, Tcf4, etc? Do autism genes show up in the lists of hits here? And if so, more than expected by chance? Can they provide some visualization of their GO results in the main figure?

When we looked into the sex differences more we found that only the males showed significant upregulation of other autism risk genes increase that was previously unappreciated when the sexes were assessed together. Yes, several autism genes do show up but is heavily biased to males. Our main Figure 7 and new supplemental files show new GO term analyses and provide additional data looking not only autism but other factors.

(12) It appears the IMPC has phenotyped this mouse somewhat, including craniofacial abnormalities. They also report on some blood cell differences. Anyway, if no one has written about that data yet (as it was generated in the context of a big consortium effort), their guidelines may allow you to include some of their data as Supplementary Figures here with proper attribution. It might help to at least summarize useful findings from there in your discussion.

Due to the large number of figures/tables already in this report we don’t think this will be helpful. However, we do refer readers to the consortium in the animal methods section so they can explore data already generated by the IMPC.

(13) Minor/Typos:

(a) Figure 2K: I am confused by the description of three genotypes in the legend, but only two in the panel?

Corrected.

(b) I found it a little distracting that some results figures were embedded in the introduction.

We have moved the figures further in the manuscript to start in the results section.

(c) I don't understand this sentence: "Due to reduced sample size, sex-stratified DE was performed without model corrections at FDR < 0.1, 7 and found genes significantly upregulated and downregulated, respectively;" The sample size here seemed robust, so I am not sure what they were referring to? Are there missing numbers form this sentence? What is the 7? I think there are enough typos here that I am not sure how to evaluate this claim. Thus, the writing and clarity of this part could be improved.

This section had several typos that have now been corrected.

(d) "Marwan Shinawi, (unpublished results)" is a bit atypical of a citation. Are these results being reported with his permission? If so, then it should say 'personal communication' (if the journal permits this - some do not). If not, they should not report someone else's unpublished results without their explicit permission. It might upset some people to have their results presented this way.

We have changed unpublished results to personal communication. Marwin Shinawi is an author on this manuscript and has approved of everything we have reported.

(e) In all figures, consider shape or color coding for sex, even when pooling the data (e.g, the data points in the behavior figures).

This is a good idea but since we found no difference when analyzing the data we don’t see how this extra work will make a difference. Since we now mention that sex differences were only presented as separate graphs when observed in the methods we think this should be acceptable.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The behaviour of cells expressing constitutively active HRas is examined in mosaic monolayers, both in MCF10a breast epithelial and Beas2b bronchial epithelial cell lines, mimicking the potential initial phase of development of carcinoma. Single HRas-positive cells are excluded from MCF10a but not Beas2b monolayers. Most interestingly, however, when in groups, these cells are not excluded, but rather sharply segregated within a MCF10a monolayer. In contrast, they freely mix with wt Beas2b cells. Biophysical analysis identifies high tension at heterotypic interfaces between HRas and wild-type cells as the likely reason for segregation of MCF10a cells. The hypothesis is supported experimentally, as myosin inhibition abolishes segregation. The probable reason for lack of segregation in the bronchial epithelium is to be found in the different intrinsic properties of these cells, which form a looser tissue with lower basal actomyosin activity. The behaviour of single cells and groups is recapitulated in a vortex model based on the principle of differential interfacial tension, under the condition of high heterotypic interfacial tension.

Strengths:

Despite being long recognized as a crucial event during cancer development, segregation of oncogenic cells has been a largely understudied question. This nice work addresses the mechanics of this phenomenon through a straightforward experimental design, applying the biophysical analytical approaches established in the field of morphogenesis. Comparison between two cell types provides some preliminary clues on the diversity of effects in various cancers.

Weaknesses:

Although not calling into question the main message of this study, there are a few issues that one may want to address:

(1) One may be careful in interpreting the comparison between MCF10a and Beas2b cells as used in this study. The conditions may not necessarily be representative of the actual properties of breast and bronchial epithelia. How much of the epithelial organization is reconstituted under these experimental conditions remains to be established. This is particularly obvious for bronchial cells, which would need quite specific culture conditions to build a proper bronchial layer. In this study, they seemed to be on the verge of a mesenchymal phenotype (large gaps, huge protrusions, cells growing on top of each other, as mentioned in the manuscript).

As an alternative to Beas2b, comparison of MCF10a with another cell line capable of more robust in vitro epithelial organization, but ideally with different adhesive and/or tensile properties, would be highly interesting, as it may narrow down the parameters involved in segregation of oncogenic cells.

(2) While the seminal description of tissue properties based on interfacial tensions (Brodland 2002) is clearly key to interpreting these data, the actual "Differential Interfacial Tension Hypothesis" poses that segregation results from global differences, i.e., juxtaposition of two tissues displaying different intrinsic tensions. On the contrary, the results of the present work support a different scenario, where what counts is the actual difference in tension ALONG the tissue boundary, in other words, that segregation is driven by high HETEROTYPIC interfacial tension. This is an important distinction that should be clarified.

(3) Related: The fact that actomyosin accumulates at the heterotypic interface is key here. It would be quite informative to better document the pattern of this accumulation, which is not clear enough from the images of the current manuscript: Are we talking about the actual interface between mutant and wt cells (membrane/cortex of heterotypic contacts)? Or is it more globally overactivated in the whole cell layer along the border? Some better images and some quantification would help.

(4) In the case of Beas2b cells, mutant cells show higher actin than wt cells, while actin is, on the contrary, lower in mutant MCF10a cells (Figure 2b). Has this been taken into account in the model? It may be in line with the idea that HRas may have a different action on the two cell types, a possibility that would certainly be worth considering and discussing.

Comments on revisions:

There is still one last point that should be made even clearer:

The system is being modelled based on the principle of INTERFACIAL TENSION, a description pioneered by the works of Steinberg and of Harris, and nicely conceptualized by Brodland (2002). Now the observed behaviour is a perfect case of sorting based on higher interfacial tension AT the boundary between cell types (with nice additional documentation of local actin and myosin enrichment in the revised manuscript). What needs to be made crystal clear it that this is NOT equivalent to the model of DITH ("DIFFERENTIAL INTERFACIAL TENSION HYPOTHESIS)" (Brodland 2002, Krieg et al 2008). It is important to stop using DITH in this context, as it leads to confusion and misinterpretations. Indeed, DITH predicts cell/tissue sorting based on differences in interfacial tension WITHIN the two cell types. While DITH accounts for relative POSITIONING (one tissue engulfing the other), it is now established that this is not the motor for cell sorting and tissue segregation, the key parameter is being heterotypic tension at the heterotypic interface. I thus invite the authors to avoid the terms "differential"/DITH, and rather use either "interfacial tension", or specifically to "HIGH HETEROTYPIC INTERFACIAL TENSION".

Related: the authors correctly cite Canty et al NatComm2017 when discussing this phenomenon. I suggest to add an additional key supporting reference "D.M. Sussman, J.M. Schwarz, M.C. Marchetti, M.L. Manning, Soft yet sharp interfaces in a vertex model of confluent tissue, Phys. Rev. Letters 120 (2018) 058001". One may also include another pioneer work in Drosophila is "M. Aliee, J.C. Roper, K.P. Landsberg, C. Pentzold, T.J. Widmann, F. Julicher, C. Dahmann, Physical mechanisms shaping the Drosophila dorsoventral compartment boundary, Curr. Biol. 22 (2012) 967-976."

We thank the reviewer for this important clarification. We fully agree that the mechanism underlying the observed segregation in our system is best described in terms of elevated heterotypic interfacial tension, rather than the classical Differential Interfacial Tension Hypothesis (DITH). As the reviewer correctly points out, DITH in its original formulation refers to differences in intrinsic interfacial tensions within each cell population, which primarily governs relative positioning (e.g., tissue engulfment), rather than the local sorting dynamics we observe here.

In contrast, our experimental and modeling results support a scenario in which segregation is driven by increased tension specifically at heterotypic interfaces between HRasV12 and wild-type cells. We agree that continued use of the term “Differential interfacial tension” in this context may lead to conceptual ambiguity.

Accordingly, we have revised the manuscript throughout to replace references to “differential interfacial tension” with more precise terminology, namely “interfacial tension” or “heterotypic interfacial tension”, wherever appropriate. We have also updated the Discussion to explicitly clarify this distinction and its implications for interpreting our results.

We thank the reviewer for suggesting additional relevant literature which have now included.

Reviewer #2 (Public review):

Summary:

The authors investigate the behavior of oncogenic cells in mammary and bronchial epithelia. They observe that individual oncogenic cells are preferentially excluded from the mammary epithelium, but they remain integrated in the bronchial epithelium. They also observe that clusters of oncogenic cells form a compact cluster in mammary epithelium, but they disperse in the bronchial epithelium. The authors demonstrate experimentally and in the vertex model simulations that the difference in observed behavior is due to the differential tension between the mutant and wild-type cells due to a differential expression of actin and myosin.

Strengths:

Very detailed analysis of experiments to systematically characterize and quantify differences between mammary and bronchial epithelia

Detailed comparison between the experiments and vertex model simulations to identify the differential cell line tension between the oncogenic and wild-type cells as one of the key parameters that are responsible for the different behavior of oncogenic cells in mammary and bronchial epithelia

Weaknesses:

It is unclear what is the mechanistic origin of the shape-tension coupling, which is used in the vertex model, and how important that coupling is for the presented results. Authors claim that the shape-tension coupling is due to the anisotropic distribution of stress fibers when cells are under external stress. It is unclear why the stress fibers should affect an effective line tension on the cell boundaries and why the stress fibers should be sensitive to the magnitude of the internal isotropic cell pressure. In experiments, it makes sense that stress fibers form when cells are stretched. Similar stress fibers form when cytoskeleton or polymer networks are stretched. It is unclear why the stress fibers should be sensitive to the magnitude of internal isotropic cell pressure. If all the surrounding cells have the same internal pressure, then the cell would not be significantly deformed due to that pressure and stress fibers would not form. Authors should better justify the use of the shape-tension coupling in the model, since most of the observed behavior is already captured by the differential tension even if there is no shape-tension coupling.

We thank the reviewer for this comment. We agree that we did not provide a mechanistic origin for the shape-tension coupling. In our model, stress fiber formation, along with actin ring formation, indicated that cells at the interface were elongated. Hence, we hypothesised that an interfacial force could induce nematic alignment at the interface. However, such an activity would only be feasible if the interface interaction were sufficiently high. Thus, the isotropic pressure at the heterotypic interface served as a proxy for cell-cell interactions in our model. However, inspired by recent work [1], we have tested whether activation of cells at the interface by shear stress would produce similar results. Exploring this aspect will require additional simulations.

(1) Pérez-Verdugo, F., Maniou, E., Galea, G. L., & Banerjee, S. (2026). Mechanosensitive feedback organizes cell shape and motion during hindbrain neuropore morphogenesis. Current Biology.

The observed difference of shape indices between the interfacial and bulk cells in simulations in the absence of differential line tension is concerning. This suggests that either there are not enough statistics from the simulations or that something is wrong with the simulations. For all presented simulation results, the authors should repeat multiple simulations and then present both averages and standard deviations. This way it would be easier to determine whether the observed differences in simulations are statistically significant.

The observed differences in shape indices between interfacial and bulk cells in simulations in the zero-line-tension case (Lambda=0) remain non-zero at the zero-stress threshold because the interface cells are still subject to the shape-dependent contribution gamma_ij, since the current model treats gamma_ij as independent of Lambda. We are exploring the possible relationship between Lambda and gamma_ij, and we will update this in the next version of the manuscript.

Recommendations for the authors:

The editor recommends considering the new comment made by reviewer #1 in his/her report:

"There is still one last point that should be made even more clear:

The system is being modelled based on the principle of INTERFACIAL TENSION, a description pioneered by the works of Steinberg and of Harris, and nicely conceptualized by Brodland (2002). Now the observed behaviour is a perfect case of sorting based on higher interfacial tension AT the boundary between cell types (with nice additional documentation of local actin and myosin enrichment in the revised manuscript). What needs to be made crystal clear it that this is NOT equivalent to the model of DITH ("DIFFERENTIAL INTERFACIAL TENSION HYPOTHESIS)" (Brodland 2002, Krieg et al 2008). It is important to stop using DITH in this context, as it leads to confusion and misinterpretations. Indeed, DITH predicts cell/tissue sorting based on differences in interfacial tension WITHIN the two cell types. While DITH accounts for relative POSITIONING (one tissue engulfing the other), it is now established that this is not the motor for cell sorting and tissue segregation, the key parameter is being heterotypic tension at the heterotypic interface. I thus invite the authors to avoid the terms "differential"/DITH, and rather use either "interfacial tension", or specifically to "HIGH HETEROTYPIC INTERFACIAL TENSION".

Related: the authors correctly cite Canty et al NatComm2017 when discussing this phenomenon. I suggest to add an additional key supporting reference "D.M. Sussman, J.M. Schwarz, M.C. Marchetti, M.L. Manning, Soft yet sharp interfaces in a vertex model of confluent tissue, Phys. Rev. Letters 120 (2018) 058001". One may also include another pioneer work in Drosophila is "M. Aliee, J.C. Roper, K.P. Landsberg, C. Pentzold, T.J. Widmann, F. Julicher, C. Dahmann, Physical mechanisms shaping the Drosophila dorsoventral compartment boundary, Curr. Biol. 22 (2012) 967-976."

Please see response to Reviewer 1

Reviewer #2 (Recommendations for the authors):

The authors have improved the manuscript and addressed some of my concerns. However, some of the questions were not adequately addressed.

(1) I appreciate additional justification regarding the need for the shape-tension coupling in the vertex model. However, the authors have not answered my question regarding why the shape-tension coupling model should be sensitive to the magnitude of the internal isotropic cell pressure. In experiments, it makes sense that stress fibers form when cells are stretched, but it is unclear why the stress fibers should be sensitive to the magnitude of internal isotropic cell pressure. If all the surrounding cells have the same internal pressure, then the cell would not be significantly deformed due to that pressure, and stress fibers would not form.

We thank the reviewer for pointing this out. We agree that we did not provide a mechanistic origin for the shape-tension coupling. In our model, stress fiber formation, along with actin ring formation, indicated that cells at the interface were elongated. Hence, we hypothesized that an interfacial force could induce nematic alignment at the interface. However, such an activity would only be feasible if the interface interaction were sufficiently high. Thus, the isotropic pressure at the heterotypic interface served as a proxy for cell-cell interactions in our model.

However, inspired by recent work [1], we have tested whether activation of cells at the interface by shear stress would produce similar results. Exploring this aspect will require additional simulations.

(1) Pérez-Verdugo, F., Maniou, E., Galea, G. L., & Banerjee, S. (2026). Mechanosensitive feedback organizes cell shape and motion during hindbrain neuropore morphogenesis. Current Biology.

(2) I appreciate that the authors provided additional statistics related to simulations. I am still very concerned about the observed difference in the shape indices between the cells at the interface and the bulk, when the interfacial line tension is exactly zero (Lambda=0). In that case, the cells at the interface and at the boundary are identical, and there should be no difference in the shape indices. Are cells at the interface for the zero-line tension case (Lambda=0) still subject to the shape dependent contribution gamma_ij? If that contribution is still included for the cells at the interface, then this could explain why cells at the interface are still different from cells in the bulk even when Lambda=0.

The observed differences in shape indices between interfacial and bulk cells in simulations in the zero-line-tension case (Lambda=0) remain non-zero at the zero-stress threshold because the interface cells are still subject to the shape-dependent contribution gamma_ij, since the current model treats gamma_ij as independent of Lambda. We are exploring the possible relationship between Lambda and gamma_ij, and we will update this in the next version of the manuscript.

(3) Authors included several additional supplemental figures (Figs. S4, S5, S6, S7) , but they are not discussed in the manuscript text. These new supplemental figures were only discussed in the rebuttal letter. These figures should also be discussed in the manuscript text.

We have cited the new supplementary figures in the main text.

(4) Authors have answered in the rebuttal letter what experimental data was used in Fig. 4c. This information also needs to be provided in the manuscript text.

We have added this information in the caption of Figure 4

(5) Supplementary Figure 3 is missing. That figure got moved to the appendix.

This has been rectified in the Supplementary file and the citations have been updated accordingly in the main text.

(6) At the end of section 4 in the main text, the authors introduced a new sentence regarding simulations of the vertex model with interfacial tension and mechanochemical feedback. The details of that model are described in the appendix, but it would be helpful to add a sentence or two already in the main text describing what is the mechanism of the mechanochemcial feedback.

We have added a line describing the mechanism of mechanochemical feedback.

(7) In the definition of the eccentricity, 'a' should be the minor axis and 'b' the major axis, i.e., 'a' and 'b' should be swapped.

We have corrected this.

(8) There is a typo at the end of the vertex model description in the methods section. "The details of the shape-tension coupling is described in the interface." The word interface should be an appendix.

We have fixed the typo.

(9) In the appendix section describing the shape-tension coupling, the authors should explain how the cell's director n is defined.

We have added a line in the appendix section describing shape-tension coupling explaining how the cell’s director n is defined.

(10) In Appendix Fig. 1, the two angles are defined as theta and theta' but the figure caption is defining angles theta_1 and theta_2. These angles need to be consistent.

This has been fixed.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors reveal that the availability of extracellular asparagine (Asn) represents a metabolic vulnerability for the activation and differentiation of naive CD4+ T cells. To deplete extracellular Asn, they employed two orthogonal approaches: activating naive CD4+ T cells in either PEGylated asparaginase (PEG-AsnASE)-treated medium or custom-formulated RPMI medium specifically lacking Asn. Importantly, they demonstrate that depletion not only impaired metabolic reprogramming associated with CD4+ T cell activation but also reduced CD4+ helper T cell lineage-specific cytokine production, thereby ameliorating the severity of experimental autoimmune encephalomyelitis.

Strengths:

The experiments presented here are comprehensive and well-designed, providing compelling evidence for the conclusions. The conclusions will be important to the field.

We thank the reviewer for their assessment of our work and enthusiasm towards our findings.

Weaknesses:

(1) EAE is the prototypic T cell-mediated autoimmune disease model, and both Th1 and Th17 cells are implicated in its pathogenesis. In contrast, Th2 and Treg cells and their associated cytokines (such as IL-4 and IL-10) have been shown to play a role in the resolution of EAE, and potentially in the modulation of disease progression. Thus, it will be important to determine whether Asn depletion affects the differentiation of naive CD4+ T cells into corresponding subsets under Th2 and Treg polarization conditions, as well as the expression of lineage-specific transcription factors and cytokine production.

We appreciate that the reviewer recognizes the functional relevance of our findings showing that Asn is important for proper Th17 differentiation and promotion of EAE (Figure 5 E-J, Figure 6). Given that multiple CD4+ T cell subsets play a role in both the initiation and resolution of EAE, we agree that it would be valuable to further support these findings with complementary Th2 and Treg differentiation experiments.

To address this, we examined the effects of asparagine depletion during in vitro iTreg and TH2 differentiation. We found that the frequencies of FOXP3+ iTreg and GATA3+ Th2 cells were reduced when cultures were grown in asparagine-deficient media. These results have been added to Supplementary Figure 5.

(2) EAE is characterized by inflammation and demyelination in the central nervous system (CNS), leading to neurological deficits. Myelin destruction is directly correlated with the severity of the disease. For Figure 6, did the authors perform spinal cord histological analysis by hematoxylin and eosin (H&E) or Luxol fast blue (LFB) staining? This is important to rigorously examine pathological EAE symptoms.

We agree with the reviewer that histopathology including H&E and/or LFB staining is a useful indicator of EAE disease severity. However, we are no longer able to obtain PEGAsnASE (Oncaspar) to perform these studies.

Reviewer #2 (Public review):

While the importance of asparagine in the differentiation and activation of CD8+ T cells has been previously reported, its role in CD4+ T cells remained unclear. Using culture media containing specific amino acids, the authors demonstrated that extracellular asparagine promotes CD4+ T cell proliferation. Consistent with this, depletion of extracellular asparagine using PEG-AsnASE suppressed CD4+ T cell activation. Proteomic analysis focusing on asparagine content revealed that, during the early phase of T cell activation, most asparagine incorporated into proteins is derived from extracellular sources. The authors further confirmed the importance of extracellular asparagine in vivo, demonstrating improved EAE pathology.

While the data are well organized and convincing, the mechanism by which asparagine deficiency leads to altered T cell differentiation remains unclear. It is also necessary to investigate the transporters involved in asparagine uptake. In particular, elucidating whether different T cell subsets utilize the same or distinct transport mechanisms would provide important insight into the immunoregulatory role of asparagine.

(1) The finding that asparagine supplementation promotes T cell proliferation under various amino acid conditions is highly significant. However, the concentration at which this effect occurs remains unclear. A titration analysis would be necessary to determine the dosedependency of asparagine.

Our studies indicate that the concentration of asparagine present in conventional RPMI lymphocyte media is sufficient to support CD4+ T cell activation and proliferation in vitro (Figure 1, Supplementary Figure 1 & Figure 2). This concentration was consistently used throughout our studies. In line with the reviewer’s comments, however, we have not yet determined the dose dependency of Asn during CD4+ T cell activation.

To address this, we performed a titration experiment in which asparagine was supplemented at varying concentrations in DMEM and Asn-deficient RPMI. Activation markers were measured 24 hours after TCR stimulation under these culture conditions. We found that the critical asparagine concentration lies between 37.8 and 3.78 uM. This concentration range is consistent with the physiological concentration of asparagine in murine plasma, which is approximately 50 uM (PMID: 24842860; PMID: 23853755). These data have been added to Supplementary Figure 1.

(2) The effects of asparagine deficiency occur during the early phase of T cell activation. Thus, it is likely that the transporters responsible for asparagine uptake are either rapidly induced upon activation or already expressed in the resting state. Since this is central to the focus of the manuscript, it is interesting to identify the transporter responsible for asparagine uptake during early T cell activation. A recent paper (DOI: 10.1126/sciadv.ads350) reported that macrophages utilize Slc6a14 to use extracellular asparagine. Is this also true for CD4+ T cells?

While a comprehensive characterization of the amino acid transporter network is certainly of interest, it is beyond the scope of the present study. As the reviewer notes, others have explored asparagine transport in lymphocytes. For example, Wu et al. (PMID: 33420490) determined that the asparagine transporter, Slc1a5, is significantly upregulated in CD8+ T cells upon activation, based on qRT-PCR measurements comparing mRNA from naïve and activated CD8+ T cell. They further validated the functional role of Asn transporters in CD8+ T cells by measuring N15-labeled asparagine uptake in the presence of siRNAs targeting the asparagine transporters Slc1a5 or Slc38a2 and found that inhibition of either transporter significantly reduced intracellular N15-Asn accumulation.

To gain additional insight into Asn transporters in distinct CD4+ T cell subsets, we reanalyzed a published RNA-seq dataset (Thakore et al., 2024; PMID: 39009838). We quantified the expression of transporters Slc1a5, Slc38a2, and Slc6a14 in naïve and activated CD4+ T cells polarized under Th1, npTh17, or pTh17 conditions at various time points. We observed that Slc1a5 expression increased upon activation in all subsets. Similarly, Slc38a2 expression increased during early activation stage, but subsequently returned to basal levels similar to naïve cells. In contrast, Slc6a14 showed relatively low basal expression in naïve cells compared to the other transporters investigated, and its expression decreased over the differentiation period in all CD4+ T cell subsets examined. These results indicate that Asn transporters Slc1a5 and Slc38a2 are expressed in CD4+ T cells during early activation and differentiation. These data have been included in Supplementary Figure 3.

(3) Given that depletion of extracellular asparagine impairs differentiation of Th1 and Th17 cells, it is possible that TCR signaling is compromised under these conditions. This point should be investigated by targeting downstream signaling molecules such as Lck, ZAP70, or mTOR. Also, does it affect the protein stability of master transcription factors such as Tbet and RORgt?

We agree with the reviewer that asparagine deprivation could impact several aspects of T cell function. In our study, we demonstrate that asparagine is crucial for CD4+ T cell protein synthesis and the expression of activation markers (Figure 1B-K, Figure 2K-L, and Figure 3AC). We also highlight its importance in promoting CD4+ T cell subset differentiation and lineage-defining cytokine production (Figure 5B-J). Other studies have reported a role for asparagine in early activation marker expression in CD8+ T cells and in enhancing LCK function (PMID: 33822775; PMID: 33420490). Given its proposed function as a promoter of LCK signaling function in CD8+ T cells, it will be important to determine if a similar mechanism operates during CD4+ T cell activation in future studies.

We appreciate the reviewer’s inquiry regarding the stability of critical transcription factors defining Th1 and Th17 subsets. We have examined the expression of the transcription factors RORγT and Tbet in Th17 and Th1 polarized cells and observed reduced expression in the absence of asparagine. We have included these findings in Supplementary Figure 5.

(4) Is extracellular asparagine also important for the differentiation of helper T cell subsets other than Th1 and Th17, such as Th2, Th9, and iTreg?

Please see our response to Reviewer 1 regarding iTreg and TH2. Investigation of Th9 cells is beyond the scope of the present study.

(5) Asparagine taken up from outside the cell has been shown to be used for de novo protein synthesis (Figure 3E), but are there any proteins that are particularly susceptible to asparagine deficiency? This can be verified by performing proteome analysis, and the effects on Th1/17 subset differentiation mentioned above should also be examined.

The investigation of specific proteins that exhibit asparagine dependency would indeed be interesting. Given our results showing that global protein synthesis is blunted with asparagine deprivation (Figure 3A-C), it would be particularly compelling to identify proteins with a specific requirement for asparagine. However, this level of analysis is beyond the scope of our study.

(6) While the importance of extracellular asparagine is emphasized, Asns expression is markedly induced during early T cell activation. Nevertheless, the majority of asparagine incorporated into proteins appears to be derived from extracellular sources. Does genetic deletion of Asns have any impact on early CD4+ T cell activation? The authors indicated that newly synthesized Asns have little impact on CD8+ T cells in the Discussion section, but is this also true for CD4+ T cells? This could be verified through experiments using CRISPR-mediated Asns gene targeting or pharmacological inhibition.

We appreciate the reviewer’s consideration of the contribution of endogenous asparagine to CD4 +T cell function. However, genetic perturbation of Asns is beyond the scope of our study, which is specifically focused on defining the requirements for extracellular asparagine and its role in CD4+ T cell activation.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors set out to define how arginine availability regulates lipid metabolism and to explore the implications of this relationship in pancreatic ductal adenocarcinoma (PDAC), a tumor type known to exist in an arginine-poor microenvironment. Using a combination of rigorous genetic and metabolomic approaches, they uncover a previously underappreciated role for arginine in maintaining lipid homeostasis. Importantly, they demonstrate that arginine deprivation sensitizes PDAC cells to ferroptosis through lipidome perturbations, which can be exploited therapeutically via co-treatment with aESA and ferroptosis inducers (FINs). These findings have meaningful implications for the field. They not only shed light on the metabolic vulnerabilities created by nutrient restriction in PDAC, but also suggest a practical avenue for combination therapies that exploit ferroptosis sensitivity. This is particularly relevant in the context of pancreatic cancer, which is notoriously resistant to conventional treatments. The methods employed are broadly applicable to other nutrient-stress contexts and may inspire similar investigations in other solid tumor types.

Strengths:

One of the major strengths of the study is the use of complementary and well-controlled approaches-including metabolomic profiling, genetic perturbations, and in vivo models-to support the central hypothesis. The experiments are thoughtfully designed and clearly presented, and the conclusions are, for the most part, well supported by the data. The findings provide mechanistic insight into nutrient-lipid crosstalk and identify a potential therapeutic strategy for targeting arginine-deprived tumors.

We thank the reviewer for their positive assessment of our manuscript.

Weaknesses:

A key weakness of the study lies in the mechanistic connection between arginine levels and SREBP1 activation. While the authors show that arginine restriction leads to reduced SREBP1 expression, the magnitude of this effect appears modest relative to the substantial changes observed in the lipidome. The study would benefit from a deeper analysis of SREBP1 regulation-particularly whether nuclear translocation or activation is affected. This could be addressed by examining the nuclear pool of SREBP1, using either subcellular fractionation or improved immunofluorescence imaging in both cell lines and tissue samples.

We thank the reviewer for this comment and in our revised manuscript have undertaken several new studies to assess how the nuclear pool of SREBP1 is regulated by arginine starvation. We further identified one mechanism by which arginine starvation suppresses SREBP1 protein levels, namely GCN activation. We believe these additional studies strengthen the manuscript and appreciate the reviewer suggesting these studies.

Another area where additional context would strengthen the manuscript is in the transcriptomic profiling of PDAC cells cultured in a tumor interstitial fluid mimic (TIFM). While the study emphasizes lipid-related pathways, highlighting the most significantly upregulated and downregulated pathways in Figure 1B would give readers a broader perspective on how arginine restriction reprograms the PDAC transcriptome. For instance, because polyamines are downstream of arginine and are known to influence lipid metabolism, it would be worth discussing whether these metabolites contribute to the phenotypes observed. Similarly, an evaluation of whether Dgat1/2 expression is altered could help delineate the full scope of lipid metabolic rewiring.

We thank the reviewer for suggesting this change to our manuscript and we now provide much more extensive analysis of our transcriptomic analyses in Figure 1 – Figure supplement 1, which we think will make our manuscript more useful to readers.

Finally, it is worth noting that the KPC mouse model used in this study is based on conditional deletion of p53, which leads to faster-growing tumors and a distinct tumor microenvironment compared to models harboring the p53^R172H point mutation. Including a brief discussion of this distinction would help readers contextualize the translational relevance of the findings.

We have revised the manuscript to include a discussion of this point.

Reviewer #2 (Public review):

This study by Jonker et al. examines how the metabolic adaptations to the microenvironment by pancreatic ductal adenocarcinomas (PDAC) present vulnerabilities that could be used for therapeutic purposes. The evidence supporting the claims of the authors is mostly solid, and the multiplicity of models used, as well as the combination of in vitro and in vivo work, are appreciated, but some conclusions would benefit from additional substantiation. This work would be of interest to biologists working on the impact of microenvironment and metabolism in cancer, and especially those investigating pancreatic cancer.

We thank the reviewer for their positive assessment of our manuscript.

In this study, the authors use mostly "doublings per day" as an indicator of cell death, notably for Figures 4 to 6. However, proliferative arrest (or a decrease in the proliferative rate) is not necessarily synonymous with cell death. It might be nice to complement these experiments with a true measure of cell death (e.g., PI uptake).

We thank the reviewer for this important comment and have performed extensive additional experiments to measure cell death directly via viability markers in addition to our indirect measurements of cell number at the start and end of experiments. We believe these additions strengthen our claims that PUFAs cause arginine starved PDAC cells to undergo ferroptotic cell death.

The composition of Tumor Interstitial Fluid Medium (TIFM) was published previously, but nonetheless a reminder of the composition of this medium in a Supplemental file of this study might be helpful. In particular, at the start of the Results section, the nature of serum/lipids in the different media should be specifically noted, especially given that the subsequent focus of the work is on lipids/SREBP. It is known that differences in the extracellular availability of lipids can profoundly alter de novo lipid biosynthesis pathways.

We thank the reviewer for this comment. We have edited the text to provide additional context on the composition of TIFM, especially lipid availability. We further have provided a supplemental file with the composition of TIFM. We hope this will make the manuscript more useful and readily interpretable for readers.

Reviewer #3 (Public review):

This important study investigates the impact of nutrient stress in the tumor microenvironment (TME), focusing on lipid metabolism in pancreatic ductal adenocarcinoma (PDAC).

Understanding TME composition is crucial, as it highlights cancer vulnerabilities independent of intracellular mutations, particularly because PDAC tumors are often exposed to limited nutrient availability due to reduced perfusion.

By utilizing a medium that mimics the nutrient conditions of PDAC tumors, the authors convincingly show that TME nutrient stress suppresses SREBP1, leading to reduced lipid synthesis, with low arginine levels identified as a key driver of this suppression. Importantly, mice with arginine-starved pancreatic tumors respond to a polyunsaturated fatty acid-rich diet. This discovery uncovers a synthetic lethal interaction in the tumor microenvironment that could be leveraged through dietary interventions.

The conclusions of this paper are mostly well supported by data; however, below are some aspects that could be further clarified.

We thank the reviewer for their positive assessment of our manuscript.

This study uses PDAC cells from the LSL-Kras G12D/+ ; Trp53 ; Pdx-1-Cre PDAC model. The authors convincingly demonstrate that the cell-extrinsic stimuli of low arginine availability suppress lipid synthesis and thus exert a dominant effect over the cell-intrinsic oncogenic Ras mutation, which is known to enhance fatty acid synthesis. Could the effect of low arginine on lipid synthesis be specific for certain mutations in PDAC? It would be interesting to investigate or discuss whether different mutations show the same SREBP1 reduction caused by low arginine levels, and whether these low SREBP1 levels can be ameliorated by arginine re-supplementation. Here, Jonker et al. show that human PDAC cells cultured in TIFM have reduced SREBP1 levels (Figure 1 - Figure supplement 1C). It would be further supportive of their conclusions if the authors could show that arginine re-supplementation is sufficient to restore SREBP1 levels in human PDAC cells.

We thank the reviewer for this comment. In response, we have now shown that arginine supplementation increases SREBP1 levels and fatty acid synthesis in human PDAC cells (Figure 2 – Figure supplement 2). Further, we have also updated the manuscript to discuss that using the LSL-Kras G12D/+; Trp53; Pdx-1-Cre PDAC model limits our ability to assess how genetic differences influence the response to arginine starvation. We additionally discuss the genetic diversity of the human PDAC cell lines used in these studies, which do include different oncogenic mutations. We believe that these results provide some data that the findings we have made regarding arginine deprivation and SREBP in our genetically defined murine PDAC cell line are applicable to human PDAC cells with more diverse oncogenic lesions.

The authors demonstrate that mPDAC cells cultured in RPMI and subsequently implanted into an orthotopic mouse model exhibit reduced expression of SREBP target genes when compared to in vitro cultured mPDAC-RPMI cells. This finding is in line with the observation that culturing PDAC cells in TIFM downregulates SREBP target genes compared to PDAC cells cultured in RPMI. However, caution is needed when directly comparing mPDAC-RPMI cultured cells to those in the orthotopic model, as the latter may include non-tumor cells and additional factors that could confound the results. The authors should explicitly acknowledge this limitation in their study.

We thank the reviewer for this important caveat and we have revised to text to address this point. Importantly, we note that for all comparisons between in vitro and in vivo cultures, we carefully sort malignant cancer cells from orthotopic tumors prior to analysis. We believe this approach mitigates the impact of stromal contamination on our analyses.

The in vivo evidence demonstrating that PUFA-rich tung oil reduces tumor size is compelling. However, the specific in vitro findings regarding its impact on doubling rates per day, particularly in the context of arginine-dependent PUFA supplementation, require further explanation. To enhance the robustness of their data and conclusions, the authors could consider conducting additional cell viability and proliferation assays. Moreover, it would be valuable to assess whether the observed effects on doubling rates per day remain significant after normalizing the data to the initial doubling time prior to PUFA supplementation. This is in particular important regarding the statement that "Addition of arginine significantly decreases sensitivity to a-ESA" as these cells already start with a higher doubling rate prior to a-ESA treatment.

We thank the reviewer for this important comment and have performed additional experiments to measure cell death directly via viability markers in addition to our indirect measurements of cell number at the start and end of experiments. Furthermore, to address the issue of different rates of cell growth in cultures affecting the response to perturbations, we also used growth rate corrected metrics (PMID: 27135972) to ensure that affects of perturbations on cell growth and viability are not confounded by the baseline proliferative kinetics of the cells under various media conditions. We believe these additions strengthen our claims that arginine starvation sensitizes PDAC cells to PUFAs.

Overall, this paper presents a compelling study that significantly enhances our understanding of the PDAC tumor microenvironment and its complex interactions with the tumor lipid metabolism.

We again thank the reviewer for their positive assessment of our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

In this study, the authors employ rigorous genetic and biochemical (metabolomic) approaches to uncover a previously unappreciated role for arginine in regulating lipid homeostasis. They further demonstrate the relevance of this pathway in pancreatic tumors, a solid tumor type often characterized by limited access to extracellular arginine. The authors present compelling evidence that arginine deprivation creates a metabolic liability, rendering tumors more susceptible to lipidome perturbations. This vulnerability can be therapeutically exploited through co-treatment with aESA and FIN to induce ferroptosis. Overall, the conclusions are convincing, the manuscript is well-written, and the figures are clearly presented.

We again thank the reviewer for their positive assessment of our manuscript.

The key weakness of the study lies in the mechanistic link between arginine levels and SREBP1 expression. While the data support the authors' argument, the observed changes in SREBP1 expression following arginine restriction appear modest relative to the more pronounced changes in the lipidome. To strengthen this connection, the authors may consider performing cellular fractionation to focus their analysis on the nuclear (active) pool of SREBP1. Improved immunofluorescence imaging and quantification of nuclear SREBP1 levels in tissues would also provide additional support for their model.

We thank the reviewers for this helpful comment. To strengthen this study, we both examined the nuclear levels of SREBP1 in TIFM cultured cells and worked to identify the mechanistic link connecting arginine levels of SREBP1 expression.

First, we found that arginine starvation does not lead to nuclear exclusion of SREBP1. We believe this finding strengthens our conclusion that arginine starvation regulates SREBP1 at the level of protein expression. We do agree with the reviewer that the change in SREBP1 protein level is modest, but we do show the effects of arginine on PDAC cell lipid metabolism are SREBP1 dependent (Figure 3O-P, Figure 5F, Figure 5 – Figure supplement 2D). Thus, we interpret these data that even the relatively modest change in SREBP1 protein levels are sufficient to cause large changes in the output of this transcription factor and the cellular lipidome.

Second, we determined if the arginine-responsive GCN2 signaling pathway, which is known to regulate SREBP1, could contribute to the suppression of SREBP1 observed in PDAC cells. We found that GCN2 signaling is activated in PDAC cells in TIFM culture by arginine starvation and is active in animal tumors. We further found that activation of GCN2 is in part responsible for suppression of SREBP1, which is consistent with prior literature describing a role for GCN2 activation in suppressing SREBP1 translation (PMID: 17276353). Thus, while other mechanisms are at play in transducing arginine starvation to reduced SREBP1 protein levels, we have identified one mechanism (activation of GCN2) by which arginine starvation suppresses SREBP1, leading to the lipidomic changes we observed upon starvation of this amino acid.

In addition, it would be helpful for the authors to highlight the most significantly upregulated and downregulated pathways in Figure 1B to give a more comprehensive view of transcriptomic changes in PDAC cells cultured under TIFM conditions. For example, since polyamines are downstream of arginine and known to regulate lipid metabolism, could some of the observed effects be attributed to changes in polyamine levels? Similarly, do arginine levels affect the expression of Dgat1 or Dgat2?

We have added an additional Figure supplement to Figure 1 that include a comprehensive list of up- and downregulated gene sets in PDAC cells cultured in TIFM via GSEA analysis. We also added additional KEGG metabolic pathway analysis via GATOM (PMID: 35639928). We hope these additions will be useful for readers and point their attention to other metabolic pathways that are significantly altered by nutrient stress, such as the TCA cycle and oxidative phosphorylation, beyond those related to lipid metabolism that we investigated here.

From this analysis, we did not specifically note strong changes in the expression of polyamine metabolic enzymes or DGATs.

Finally, the KPC model used in this study involves conditional deletion of p53, which is known to produce tumors with a faster progression and a distinct tumor microenvironment compared to the more commonly used p53^R172H knock-in model. Including this point in the discussion would help contextualize the findings.

We thank the reviewers for mentioning this limitation of our study. In the results section of the test, we now included a discussion of the limitations of the mouse model used in the discussion of the work. We also highlight in the text now that in addition to our studies using the murine p53 deletion model that our studies make use of human PDAC lines that contain p53 mutations. We believe that these results provide some data that the findings we have made regarding arginine deprivation and SREBP in our genetically defined murine PDAC cell line are applicable to human PDAC cells with more diverse oncogenic lesions.

Minor comments to improve clarity:

(1) In Figure 3C, it would be helpful to annotate the PE-linked TG for clarity.

We do not understand exactly what PE-linked TGs refers to. We note in Fig. 3C that ether-linked triglycerides are labeled in orange and annotated as O-TG and vinyl ether-linked triglycerides are labeled in grey and annotated as P-TG.

(2) Is Figure 3P mislabeled? Both conditions are labeled as +Arg / -lipid.

We thank the reviewers for pointing out this mistake in the figure and have updated it to correctly label these samples as sgSREBP1 and sgNTG transduced PDAC cell lines.

Reviewer #2 (Recommendations for the authors):

(1) Figure 1B: Misspelling in Y axis "Normalized enrichment score".

We thank the authors for catching this mistake and have corrected this error.

(2) Figure 1B: Could the authors elaborate on why they decided to focus specifically on these three hits, which are not the most downregulated genes (the "top hits") appearing in the GSEA?

We chose to focus on lipid metabolism as multiple transcriptomic analysis tools, namely GSEA and GATOM, which specifically focuses on enrichment in KEGG annotated metabolic pathways, highlighted lipid synthesis as being the most transcriptionally regulated metabolic pathway in TIFM. To make this apparent to readers, we added an additional Figure supplement to Figure 1 that includes a comprehensive list of up- and downregulated gene sets in PDAC cells cultured in TIFM from GSEA and GATOM analysis. We hope these additions will make the logic for our focus on lipid synthesis clear and will be useful for readers in highlighting other metabolic pathways that are significantly altered by nutrient stress, such as the TCA cycle and oxidative phosphorylation.

(3) Figure 1: It might improve the clarity of the text if the three pairs of murine cell lines (mPDAC1, mPDAC2, mPDAC3) were introduced in a bit more detail in the main text and not just in the figure legend.

We have added more detail describing the three mouse cell lines used in the main text.

(4) Figure 1E: The authors may wish to comment on why they chose to perform transcriptomic analyses with the mPDAC3 derived models, and not mPDAC1 or mPDAC2, given that mPDAC3 appears to exhibit the most distinct phenotype of the three, according to the results presented in Figure 1 J-L.

The transcriptional analysis described in Fig. 1E was performed on a previously acquired dataset using mPDAC3 cell lines (PMID: 37254839), which is why this line was used. We have revised the text to make it clear that this transcriptional analysis uses pre-existing data from a previous publication.

(5) Figure 1L: The authors may wish to clarify why they only show relative palmitate to assess global fatty acid biosynthesis in these cell lines. There is a decrease in labeled palmitate of mPDAC3 cells cultured in TIFM in comparison to the cells cultured in RPMI media, showing a decrease in the lipid biosynthesis of these cells in these conditions. However, there also seems to be lower palmitate levels in the TIFM-cultured mPDAC3 cells specifically, in comparison to their mPDAC1 and mPDAC2 counterparts. Why is that? Could the authors comment on this result?

We thank the reviewers for this helpful observation. In Figure 1L (now Figure 1N), we wanted to show how culture conditions (RPMI/TIFM) affected both the total amount of palmitate in PDAC cells but also the fraction that is labeled (i.e. arising from de novo synthesis). We think this provides more information for readers by allowing them to assess both changes in pool size of palmitate and changes in the fraction of palmitate that is synthesized. We like this presentation as it shows clearly that while total palmitate levels behave differently across cell lines (with TIFM culture reducing levels in mPDAC1-2 but increasing levels in mPDAC3) the amount of palmitate that is synthesized de novo is decreased in all three cell lines when cultured in TIFM. To highlight this, we also present the fraction of palmitate that is labeled in Fig. 1O.

We are unsure why TIFM culture reduces total palmitate levels in some PDAC cell lines, while others are able to maintain total palmitate pools. We assume that TIFM cultures increase lipid uptake to compensate for lack of synthesis, and potentially differences in lipid scavenging capacity between the lines could explain this difference. We are currently working on experiments to test these hypotheses and will present the results in a future study.

(6) Figure 2 - Figure Supplement 1A: It would be informative and appreciated to know which nutrients are actually represented and correspond to certain points on the graph, in particular for the ones that are the most differentially present in the two different media.

We have now updated this graph to highlight key metabolites that are most differentially abundant between the two media. We also now provide as a Supplementary file the composition of TIFM, which provides readers with all the information needed to understand which metabolites are differentially abundant in TIFM and any media they wish to compare.

(7) Figure 2 - Related to Figure supplement 1D: It would be useful to know how or why arginine was selected for further investigation from the subset of amino acids. The authors could elaborate on this, by showing or highlighting the data that drew attention to this amino acid initially.

We thank the reviewers for this note. We have tried to make Figure 2 – Figure supplement 1 more clear as to how arginine was selected for further investigation. We have updated the figure to improve clarity for the comparisons of different media that enabled us to identify differences in amino acids between RPMI and TIFM as driving the difference in lipid metabolism. We have also highlighted in Figure 2 – Figure supplement 1A that arginine is the most differentially abundant amino acid and editing the text to explain the logic that this high degree of differential abundance is why we focused on arginine amongst all the amino acids as a likely candidate for regulation of SREBP1.

(8) The legends for Figures 2G and 2H could be improved, i.e., making clearer that 2H shows incorporation in the circulating fatty acids, unlike 2G.

We have updated the figure with improved labeling as the reviewer suggested to denote which panels correspond to which sample type.

(9) Figure 3E and 3G: The heatmaps displayed here show that the addition of arginine to TIFM culture medium restores fatty acid synthesis; however, it appears that the nature of the lipids synthesized in this condition may differ from the ones synthesized in RPMI cultured conditions.

We have added additional text highlighting that arginine supplementation to TIFM and RPMI culture led to induction of different SREBP1-target genes, but that both lead to activation of fatty acid synthesis and desaturation genes, which contributes to the focus of our study on de novo synthesis of saturated and monounsaturated fatty acids in the study.

(10) Figure 3O: The SREBP1 immunoblot still seems to show some residual bands for the cells transduced with SREBP1 targeting sgRNAs, therefore, the authors may want to be more nuanced and present this model as a KD, instead of a KO, as mentioned in the text?

We agree with the reviewer’s suggestion, and we have changed the text to describe these as knockdowns rather than full knockouts.

(11) Figure 3P: Is it possible that there is an error in the legend of the figure (Lipids + for the first bar and - for the second one?). The figure could also be improved by a legend that explains what the different colored bars represent.

We thank the reviewers for pointing out this mistake in the figure and have updated it to correctly label these samples as sgSREBP1 and sgNTG transduced PDAC cell lines.

(12) Figure 4: The authors are stating in Figure 4 - Figure supplement 1A-F, that argininerestricted mPDAC cells are not sensitized to xCT or GPX4 inhibitors that trigger ferroptosis and that therefore SREBP1 suppression by arginine restriction in the TME does not sensitize PDAC cells to ferroptosis inducers. However, this does not appear to be so clear with the data shown. This might be due to the limitations associated with the population doubling measurements instead of the lethality measures noted above. Likewise, later it is proposed that arginine restriction sensitizes both mPDAC cells and human PDAC cells to α-ESA induced ferroptosis. These results would benefit from a direct measure of cell death. Related to the above point, it would be useful to better understand why cells cultured in arginine-deprived TIFM do not appear to be sensitized to ferroptosis inducers, but these same cells die from ferroptosis when treated with α-ESA. It would be useful to present some thoughts.

We thank the reviewers for bringing up this important point. To the reviewers first point, we repeated xCT and GPX4 inhibitor treatment experiments to include both growth corrected (PMID: 27135972) proliferation assays and Sytox-based viability assays. In both cases, we did not find consistent sensitization to xCT or GPX4 inhibitors across multiple PDAC lines when cultured in TIFM. In contrast, we found consistent sensitization to PUFA treatment across multiple murine and human PDAC cell lines cultured in TIFM. Together, this analysis suggests that arginine starvation specifically sensitizes PDAC cells to PUFAs, but not other ferroptosis inducers.

We agree with the reviewer that this is an interesting and unexpected observation. We do not have a mechanistic understanding as to why this is the case. However, we believe this is quite interesting and suggests that PUFAs maybe a better method of inducing ferroptosis in certain conditions than other ferroptosis inducing approaches. We have added text to the discussion to highlight this interesting and unexplained observation.

(13) Figure 6: The authors mention that α-ESA is used here at sublethal doses, which do not affect viability or proliferation, but this is not shown in either the main or supplementary data. These data should be provided somewhere. It might also be nice to mention in the main text (not just in the legend) the dose of α-ESA used for the combination treatments.

We thank the reviewers for this helpful suggestion. To illustrate that α-ESA is used at a sublethal dose, we altered each panel to be on a linear rather than logarithmic x-axis, therefore including the DMSO control arm for each ferroptosis inducer in combination with α-ESA. We hope this now clearly illustrates that this dose α-ESA is not perturbing cell growth or viability in these assays.

(14) Figure 6B: Fer-1 treatment does not seem to rescue the phenotype very clearly. This could again be because cell death is being conflated (to degree) with effects on proliferation, and Fer-1 is not expected to affect cell proliferation. Again, measuring cell death directly would be better than measuring population doublings.

We thank the reviewers for this helpful comment. To address this concern, we have added Sytox-based viability assays to figure 6. These assays indicate that Fer-1 treatment rescues the viability of PDAC cells treated with ferroptosis inducers, α-ESA, or the two in combination.

Reviewer #3 (Recommendations for the authors):

General notes:

(1) It would be easier for the reader if one condition were consistently placed in the same position throughout the graphs. For example, RPMI results should always appear first and TIFM second. Currently, this is inconsistent throughout the manuscript (e.g., Figure 1 - Figure Supplement 1: RPMI is first and TIFM second; Figure 2 - Figure Supplement 1: TIFM is first and RPMI second).

We thank the reviewers for this note. We have updated the figures to remain consistent in their ordering throughout the manuscript.

(2) Please briefly explain the differences between PDAC1-3 and clarify why most follow-up experiments were conducted using PDAC1. Presumably, this was because PDAC1 showed the most robust effect on fatty acid synthesis.

We have added additional text in the results section of the manuscript describing the different murine PDAC lines used in this study. We performed most studies with mPDAC1 as this line has robust differences in fatty acid synthesis between culture conditions. However, murine PDAC lines recapitulate the transcriptional subtype diversity of PDAC (PMID: 29364867), so we critically repeat key experiments in multiple mPDAC lines to determine if a given finding is translatable to other PDAC subtypes.

(3) Are only SREBP1 protein levels affected or are SREBP1 RNA levels also decreased in low arginine TME?

We appreciate this important comment. We have added SREBP1 RNA levels to Figure 1 to show that RNA levels do not differ between conditions, whereas protein levels of SREBP1 change significantly.

(4) What was the rationale for investigating lipid metabolism even though it was not the top changed metabolic gene signature? It would be interesting to briefly discuss which pathways were the most enriched.

We chose to focus on lipid metabolism as multiple transcriptomic analysis tools, namely GSEA and GATOM, which specifically focuses on enrichment in KEGG annotated metabolic pathways, highlighted lipid synthesis as being the most transcriptionally regulated metabolic pathway in TIFM. To make this apparent to readers, we added an additional Figure supplement to Figure 1 that includes a comprehensive list of up- and downregulated gene sets in PDAC cells cultured in TIFM from GSEA and GATOM analysis. We hope these additions will make the logic for our focus on lipid synthesis clear and will be useful for readers in highlighting other metabolic pathways that are significantly altered by nutrient stress, such as the TCA cycle and oxidative phosphorylation.

Further comments:

(1) Figure 1 Supplement 1A: It is not clear which SREBP target genes are significant. Please indicate this more clearly.

The analysis in this section was done on expression level of all the indicated genes between groups (tumor/normal) rather testing for significance of individual genes between the two groups. We have updated both the text and the figure legend to clarify this as the statistical analysis that was performed.

(2) Figure 1J and 2C: The Western blot loading control (Actin) does not appear equal across all samples. It would be helpful to include a quantification normalized to the Actin loading control.

We have included quantification of each western blot to help interpret these immunoblots.

(3) Supplementary Figure 2: How often has this experiment been performed? The TIFM results appear to consistently show the same values. If this is the case, it needs to be labeled appropriately.

Thank you for pointing out that how we presented the data was confusing as to how the experiment described was performed. Initially, we performed multiple separate experiments to identify arginine starvation as the TIFM-driver of SREBP1 suppression. To compare across all the separate media conditions, we performed one experiment with all the relevant media conditions together, which is the experiment that is described in the manuscript. Thus, there was one set of control TIFM/RPMI conditions to which we compared all of the different media conditions. As we initially presented the data, it appeared as if we had performed multiple experiments in which the TIFM/RPMI controls had exactly the same behavior, which is not the case. We have updated the data presentation in this figure to make it clear that this was the experimental design for the data presented.

(4) Figure 3P: Please add a legend for this panel.

We thank the reviewers for point out this mistake in the figure and have updated it to correctly label these samples as sgSREBP1 and sgNTG transduced PDAC cell lines.

(5) Figure 4 - Figure Supplement 1: Please review the legend carefully. The legend currently includes only circles, but some of the graphs (A and F) display squares.

Thank you for catching this mistake. We have updated the panels and legends for this figure so they are concordant.

(6) Figure 4D: The effect of a-ESA treatment on the doubling delta of arginine-treated versus non-treated TIFM cells looks similar. It looks like the difference is because cells treated with arginine start at higher doubling values from the beginning. I would suggest looking at the delta and subsequently tone down the statement: "Addition of arginine significantly decreases sensitivity to a-ESA."

Thank you for this helpful comment. To avoid any confounding effects of differences in basal growth rate between mPDAC cells grown in different media, we have converted all of our data to GR values as described in (PMID: 27135972) which enables us to take into account the basal growth rates of cultures when calculating the effects of treatments/perturbations on culture growth and viability. We hope this addition makes the effect that arginine has on α-ESA sensitivity clear beyond the impact that arginine has on basal growth rate.

In addition, we also measured the viability of α-ESA treated mPDAC cells with and without supplemental arginine (current Fig. 5E) by Sytox-exclusion assay. We believe this new data supports the claim that arginine makes PDAC cells resistant to the addition of exogenous PUFAs.

Author response:

We appreciate the constructive feedback from the reviewers and are currently working diligently to address all concerns raised in both the public reviews and the recommendations for the authors. Below, we outline the revisions planned for the revised manuscript.

(1) We acknowledge the limitations of the current modeling framework regarding spatial integration, and we agree that the present model does not account for the short lifetime of the dot stimuli.

For spatial integration, our current data suggest a relatively narrow, center-weighted integration function in zebrafish, compared to a broader integration function in medaka. While incorporating such spatial weighting into the model would improve its completeness, we do not expect it to substantially alter our current interpretation of the underlying mechanisms.

Regarding the responses to short-lifetime dot stimuli, we hypothesize that medaka may possess local retinal receptive units that function as low-pass filters, as illustrated schematically in Figure 3e. At present, however, we believe that explicitly modeling this component would remain largely uninformative and would not substantially increase the explanatory power of the model.

In the revised manuscript, we will discuss these limitations and the possible neural implementations more explicitly in the Discussion section.

(2) We appreciate the reviewer’s comments regarding the clarity of data presentation and statistical descriptions.

In the revised manuscript, we will improve the clarity of the figures and legends and provide more explicit explanations of the statistical analyses and summary metrics used throughout the study. We will also revise several sections of the text to improve the framing and interpretation of the results.

Author response:

We thank the editors and reviewers for their constructive feedback on our manuscript. We accept the reviewers' recommendations and will implement them fully in our revised manuscript and include all of the suggested literature references. Below, we highlight several key points raised during the evaluation and outline exactly how we will address them. We will also explicitly address every other point and minor recommendation raised by the reviewers in our final, comprehensive point-by-point response.

Population-level quantification and statistical thresholds: The reviewers noted that our manuscript relied on single-neuron examples without fully demonstrating how widespread these patterns are across the recorded population. To address this, we will add population-level quantification across the recorded units using standard False Discovery Rate (FDR) corrections for multiple comparisons. We will include summary tables in the text and add statistical threshold lines to the distribution figures to report the proportion of significant neurons per region.

Identifying amodal neurons: Reviewers raised concerns that our classification of amodal language neurons required a more direct test. We will provide additional measures of modality and, in particular, we will implement a cross-modal generalization analysis where our encoding models are trained on one modality (e.g., listening) and evaluated on the other (e.g., reading). This additional procedure will classify neurons as amodal if their cross-modal predictive performance exceeds a baseline null model.

Isolating linguistic features from sensory confounds: A point was raised regarding whether some neurons were tracking low-level sensory properties (like sound amplitude or visual text size) rather than language features. We will address this by running encoding analyses that include additional basic acoustic envelopes and visual baseline properties as control variables. This will allow us to evaluate the unique variance explained by linguistic features after accounting for these low-level sensory baselines.

Evaluating the "Compositional Code" in the Fusiform Gyrus: Reviewers pointed out that our claim regarding a "compositional code" (neurons tracking a combination of letter identity and position) was supported primarily by individual examples. To provide population-level context, we will perform a model comparison across our fusiform gyrus neurons. We will compare a baseline letter-only model against a model that includes letter-by-position interactions to report how many neurons statistically support this compositional structure.

TRF Feature and procedure explanation: Reviewers requested clarification on the construction of our TRF features. We will update the Methods section to explicitly detail how the features were constructed for both modalities. We will also include a feature correlation matrix in the Supplementary Materials. Furthermore, in order to contrast low-level possible confounds and high-level linguistic features, we will also conduct a control analysis tracking, e.g., specific affixes across different structural roles – for example, comparing how neurons respond to the phoneme /-s/ when it functions as a plural number marker versus when it appears as part of a lexical item (e.g., pass) or a third-person verb agreement. We will conduct such analyses in addition to fitting the main TRF models with these additional confounds included, ensuring a clear dissociation between high and low-level features.

Author response:

Reviewer #1 (Public Review): 

The medial reticular formation (MRF) in the brainstem has long been implicated in the regulation of locomotion. One common - albeit very simple - model often presents the MRF as a major relay station receiving inputs from MLR circuits, among other brain regions, that together convey locomotor signals through efferent projections targeting the caudal brainstem and the spinal cord. Yet, the MRF is a particularly large brain area whose cellular complexity is far from understood. How molecularly distinct MRF ensembles contribute to the regulation of locomotor behaviors is largely unknown. Here, the authors apply focal activation of either glutamatergic, GABAergic, or serotonergic neurons throughout the MRF using a chemogenetic gain-of-function approach to uncover the putative modulatory properties of these neuronal ensembles during walking. Using kinematic analysis of mice limbs during self-paced over-ground walkway locomotion, the authors find that activation of GABAergic MRF neurons can selectively slow down walking, whereas activation of glutamatergic neurons can induce a specific "shuffle" limb trajectory, altogether revealing that distinct MRF populations may retain the capability to engage divergent walking signatures, whose behavioral relevance are not yet clear. In contrast, the activation of serotonergic neurons did not affect walking signatures as described for the other two subgroups but led to an increase of locomotor speed. Interestingly, MRF neurons in each regional activation "hotspots" appear to target different domains in the lumbar spinal cord, suggesting that distinct circuit mechanisms are at play for the slowmo vs shuffle effects. 

Major points: 

(1) While the experiments are carefully done and the results are well analyzed and clearly presented in a series of beautiful figures, several aspects of the methodology remain very confusing. 

A) In particular, the initial choice for the injection coordinates is not justified and the authors don't leverage the mapping of spinal projection neurons to drive their chemogenetic screen. 

Thank you for pointing this out. To clarify this, we now start the results with an extra paragraph and accompanying figures (Figure 2 and its supplementary figures) in which we define the region of interest (ROI) within the mRF. The ROI is based upon the distribution of reticulospinal neurons in the brainstem mRF that connect directly with the lumbosacral enlargement (whether or not this ROI projects to other CNS sites), which contains the main networks important for hindlimb control during locomotion, including walking gait. Reticulospinal neurons in the mRF in the caudal pons and medulla oblongata form longitudinal columns that together occupy up to more than half of the entire brainstem. While the morphology of the medulla and caudal pons varies little from level to level, in contrast to rapid changes at the midbrain level, this doesn’t necessarily mean that the neuronal populations, even within neurotransmitter classes, are homogeneous in connectivity and function. We have now clearly denoted the rostrocaudally extensive field with its dorsoventral and mediolateral dimensions that comprises the anatomical region of interest in the new figure. While this dataset is rather basic, it allows us to directly refer back to it and clarify additional queries that came up related to the anatomy (i.e. that the hotspots for slomo- and shuffle-like gaits only cover a small portion of the reticulospinal field).

We then included detailed anatomical mapping of the spinal projections for the identified hotspots for changes in walking quality (phenomenology), the central theme of the study, and immediately adjacent regions to highlight contrasting location-connectivity-functional properties between these adjacent sites. To better incorporate these mapping results we now present it directly following the walking function based transfection site mapping, but before delving into the details of the walking gait phenotypes. We did not systematically include mapping results from all sites in the mRF ROI into this manuscript as this was beyond the scope of this already very large functional-anatomical study. 

B) Similarly, the authors group very different injection schemes (unilateral or bilateral targeting of MRF neurons), that should be analyzed separately. 

We now clarify early in the results section how uni- and bilateral groups were composed and what the rationale was for this. As pilot data suggested that the slomo gait style was only seen following bilateral activation in VGaT-cre mice, but not in all bilateral cases, we designed the VGaT cohort to contain mainly bilateral injections, spread across the mRF region of interest, with a smaller group of unilateral injections to verify the pilot data. 

For the shuffle gait style, pilot data suggested that both uni- and bilateral activation of VGluT2 neurons could elicit this style, but only in a subset of uni- and bilateral cases. Therefore we mainly included unilateral injections in this group with a smaller bilateral cohort for verification.  This approach served the main goal of the study, which was to map the walking style changes to subregions in the mRF.

However, laterality is indeed very important when it comes to locomotor control. The effects of laterality on the walking gait styles generated from the hotspots were included in supplemental figures and accompanying Tables. We have now better highlighted these in the body of the text and we have added analyses of the motor tests for uni- or bilateral groups. 

Furthermore, it should be noted that the uni- and bilateral groups are heterogeneous when it comes to rostrocaudal and dorsoventral placement within the mRF ROI. As such, we were not able to rigorously compare uni- versus bilateral activation effects while at the same time separating cases out by dorsoventral and rostrocaudal location (which would be needed to do justice to the functional anatomical organization of the mRF) as we do not have sufficient power in each of the subgroups (i.e. 3 rostrocaudal levels, with each a dorsal, intermediate and ventral region to target, which each would have to be injected unilaterally and bilaterally). This was beyond the scope of this already very large study. Further studies designed to balance ipsi- and contralateral groups will be necessary to map out the hotspots for mobility phenotypes that may be driven by the mRF beyond the slomo- and shuffle-hotspots or to systematically study the impact of laterality on mobility from the mRF.  

To summarize, analyses of uni- vs bilateral stimulation demonstrate that bilateral inhibition within the slomo hotspot is necessary to create the slomo walking phenotype, and that unilateral inhibition within the shuffle hotspot is sufficient to create the shuffle walking phenotype (with bilateral stimulation not enhancing the phenotype further). Unilateral activation of the slomo hotspot did not induce asymmetries in gait or a reduction in motor performance, whereas unilateral activation of the shuffle hotspot induced an asymmetry in swing time but not stride length, with laterality affecting horizontal ladder but not other motor tests. Mice with transfection sites within the mRF region of interest but outside of the slomo and shuffle hotspots did not display these walking phenotypes but did display slowed walking without qualitative changes. The connectivity to spinal and other supraspinal substrates differed between these sites, providing clues for the substrates that mediate these differential functions.

C) The choice of Z score cutoff that dictates the in-depth analysis of the chemogenetic phenotypes appears arbitrary and is not grounded in a set of objective criteria. 

We are sorry that the Z score cutoff appeared arbitrary as that was not our intention. 

The values to separate mice with and without a significant change were simply set at 2 standard deviations from the population mean in the control mice (i.e. Z=2). Two standard deviations from the population mean is widely used in all types of statistical analyses. We have now included the rationale for the cutoff of Z=2 in the text. Where group size allowed, to increase contrast between positive and negative groups in terms of gait characteristics, other behavioral assays and mapping, we used data from Z scores >3 (or < -3), but can assure that all moderately positive data (i.e. from mice with gait style Z scores between 2 and 3, and between -3 and -2) was reported as well in the statistical tables or supplementary figures. We have now included the links to theses supplementary tables and figures in the text, rather than only in the figure legends.

The Z scores for the different gait styles indeed appear to map to discrete sites, but the Z score cutoff was not informed by these sites or by anatomical data. Similarly, Z scores for changes in tonic muscle activity elicited by activation of inhibitory neurons also mapped to a hotspot in the same rostrocaudal column as the slomo gait style, but further caudally. This further demonstrates the strength of function-based mapping. 

(2) One issue that arise from the work presented here is that we don't know if these MRF neurons are active during locomotion in normal, unperturbed conditions. Knowing the recruitment profile of these MRF neurons would clarify whether the chemogenetic activation boosts the firing of neurons that are already active during walking, or activate neurons that are otherwise silent. Disentangling between these possibilities may have a profound impact on the overall interpretation of the results. 

We agree that this knowledge would improve our ability to interpret and apply the findings of the current study. It is indeed important to learn when these mRF sites are being recruited, whether part of normal modulatory strategies in order to navigate through a complex environment or as part of specialized behavioral modules or both.  Another question is how loss of function in these sites impacts behavior and function. This concept has been added to the discussion and these questions can now be pursued in future experiments. 

(3) The results should be discussed in the broader context of historic stimulation experiments, notably in cats and other species, as well as more recent circuit mapping approaches in rodents. For instance, the notion that focal stimulation of distinct area within the MRF can elicit or modify the pattern of locomotion is not really new, so is the notion that some of these modulations are phase-specific and can influence the duration of single muscle activation during stance or swing phases. This last point has for instance already been assessed through individual muscle recordings paired with MRF stimulation in cats. Perhaps better introducing these key studies and a thorough discussion of what the results presented in this manuscript bring in terms of novelty will help readers ground this work into a more comprehensive and larger body of work. 

There is indeed a rich series of meticulous work done in cats, which included effects from stimulation of inhibitory and excitatory neurons on limb EMG, and rodent work focusing on excitatory mRF neurons. These studies show that distinct neurons or sites within the mRF drive distinct changes in motor readouts, albeit not described in terms of modulation of walking gait as we do here in terms of gait signatures. Despite this solid body of prior work, the notion of phase specificity and separate modulation of swing versus stance phase metrics has been underappreciated and therefore deserves to be emphasized. We have expanded the discussion to better highlight prior work and the interpretation of phase specificity has been enriched.  

Reviewer #2 (Public Review): 

This paper is an interesting conceptual work where certain hotspot areas were found to induce unique gait patterns. These patterns differed from a classic change in speed or gait pattern from a walk to a gallop. From this, a hypothesis was formed that these areas could be important for possible alternative walking patterns seen, for example, during pathologies such as Parkinson's disease or perhaps related to stalking behaviors. 

While I liked the work and found it interesting, it remains descriptive in that the actual behaviors observed can't be causally related to a particular behavior such as stalking or shuffling. If the necessity or sufficiency of this region was related to a specific hunting behavior, for example, its interest to the field would be greater. 

Nevertheless, this paper does contribute to growing evidence that specific behaviors can be triggered by specific neuronal populations within the brainstem. 

We thank the reviewer for their thoughtful comments. We agree that more studies are necessary to understand how the slomo and shuffle hotspots serve behavioral repertoires (such as stalking or other internally driven activities) and adaptations (such as object avoidance or more subtle adjustments to terrain or internal cues). The experimental details of the present study leave ample leads for the research community to pursue these new directions.

Author response:

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

Reviewer #1.

We appreciate the constructive comments, which greatly improved this manuscript.

Reviewer #2.

We appreciate Reviewer #2's thorough analysis of our manuscript. However, we are concerned that the reviewer criticized a conclusion different from the one we claim in the manuscript. Although Reviewer #2's public comment stated, "Such an approach is insufficient to unequivocally support the central claim that DNA methylation increases accessibility of H2A.Z-containing nucleosomes", we did not draw such a bold conclusion. In the Abstract, we cautiously described that the impact of DNA methylation we observed was subtle and based on satellite II-derived DNA sequences. We made a nuanced proposal regarding this observation, stating, "Altogether, we propose that SRCAP drives the biased association of H2A.Z to unmethylated DNA, while additional mechanisms, potentially taking advantage of the subtle DNA methylation-induced physical effects, further assist the exclusion of H2A.Z from methylated DNA". We believe our analysis will contribute valuable insights into the mechanistic basis behind the antagonism between DNA methylation and H2A.Z.

Reviewer #3.

We appreciate the constructive comments, which greatly improved this manuscript.

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

eLife Assessment

This study provides valuable mechanistic insight into the mutually exclusive distributions of the histone variant H2A.Z and DNA methylation by testing two hypotheses: (i) that DNA methylation destabilizes H2A.Z nucleosomes, thereby preventing H2A.Z retention, and (ii) that DNA methylation suppresses H2A.Z deposition by ATP-dependent chromatin remodeling complexes. Through a series of well-designed and carefully executed experiments, findings are presented in support of both hypotheses. However, the evidence in support of either hypothesis is incomplete, so that the proposed mechanisms underlying the enrichment of H2A.Z on unmethylated DNA remain somewhat speculative.

We would like to thank the editor and reviewers for their critical assessments of our manuscript. While we do acknowledge the limitations of our work, we believe that our results provide important mechanistic insights into the long-standing question of how H2A.Z is preferentially enriched in hypomethylated genomic DNA regions. First, our structural and biochemical data suggest that DNA methylation increases the openness and physical accessibility of H2A.Z, albeit the effect is relatively subtle and is sequence-dependent. Second, using Xenopus egg extracts and synthetic DNA templates, we provide the first clear and direct evidence that DNA methylation-sensitive H2A.Z deposition is due to the H2A.Z chaperone SRCAP-C, corroborated by our discovery that SRCAP-C binding to DNA is suppressed by DNA methylation. Although the molecular details by which DNA methylation inhibits binding of SRCAP-C is an important area of future study, in our current manuscript, we do provide evidence that directly links the presence of SRCAP-C to the establishment of the DNA methylation/H2A.Z antagonism in a physiological system. Thanks to criticisms by the reviewers, we realized that we did not clearly state in our Abstract that the impact of DNA methylation on intrinsic H2A.Z nucleosome stability is relatively subtle, although we did explain these observations and limitations in the main text. In our revised manuscript, we are willing to edit the text to better clarify the criticisms raised by the reviewers.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors considered the mechanism underlying previous observations that H2A.Z is preferentially excluded from methylated DNA regions. They considered two non-mutually exclusive mechanisms. First, they tested the hypothesis that nucleosomes containing both methylated DNA and H2A.Z might be intrinsically unstable due to their structural features. Second, they explored the possibility that DNA methylation might impede SRCAP-C from efficiently depositing H2A.Z onto these DNA methylated regions.

Their structural analyses revealed subtle differences between H2A.Z-containing nucleosomes assembled on methylated versus unmethylated DNA. To test the second hypothesis, the authors allowed H2A.Z assembly on sperm chromatin in Xenopus egg extracts and mapped both H2A.Z localization and DNA methylation in this transcriptionally inactive system. They compared these data with corresponding maps from a transcriptionally active Xenopus fibroblast cell line. This comparison confirmed the preferential deposition or enrichment of H2A.Z on unmethylated DNA regions, an effect that was much more pronounced in the fibroblast genome than in sperm chromatin. Furthermore, nucleosome assembly on methylated versus unmethylated DNA, along with SRCAP-C depletion from Xenopus egg extracts, provided a means to test whether SRCAP-C contributes to the preferential loading of H2A.Z onto unmethylated DNA.

Strengths:

The strength and originality of this work lie in its focused attempt to dissect the unexplained observation that H2A.Z is excluded from methylated genomic regions.

Weaknesses:

The study has two weaknesses. First, although the authors identify specific structural effects of DNA methylation on H2A.Z-containing nucleosomes, they do not provide evidence demonstrating that these structural differences lead to altered histone dynamics or nucleosome instability. Second, building on the elegant work of Berta and colleagues (cited in the manuscript), the authors implicate SRCAP-C in the selective deposition of H2A.Z at unmethylated regions. Yet the role of SRCAP-C appears only partial, and the study does not address how the structural or molecular consequences of DNA methylation prevent efficient H2A.Z deposition. Finally, additional plausible mechanisms beyond the two scenarios the authors considered are not investigated or discussed in the manuscript.

Although we acknowledge the limitations of our study and are willing to expand our discussion to more thoroughly discuss these points, we believe our manuscript provides several important mechanistic insights which this reviewer may not have fully appreciated.

Our first conclusion that H2A.Z nucleosomes on methylated DNA are more open and accessible compared to their unmethylated counterparts is supported by both our cryo-EM study and the restriction enzyme accessibility assay. Although the physical effect of DNA methylation is relatively subtle and is likely sequence dependent, as we clearly noted within the manuscript, the difference does exist and is valuable information for the chromatin field at large to consider.

The second major conclusion of our manuscript is that SRCAP-C exhibits preferential binding to unmethylated DNA over methylated DNA, and that SRCAP-C represents the major mechanism that can explain the biased deposition of H2A.Z to unmethylated DNA in Xenopus egg extracts. Furthermore, our experiments using Xenopus egg extract clearly demonstrated that H2A.Z is deposited by both DNAmethylation sensitive and insensitive mechanisms. Depletion of SRCAP-C almost completely eliminated the levels of DNA-methylation-sensitive H2A.Z deposition and reduced the total level of H2A.Z on chromatin to less than half of that seen in non-depleted extract. This result demonstrated that DNA methylation-sensitive H2A.Z loading is primarily regulated by SRCAP-C, at least in our experimental context where transcription, replication, and other epigenetic modifications are not involved. It is likely that additional mechanisms do further contribute, implicated by our sequencing experiments, particularly at regions with active transcription, and we have noted these possibilities and the rationale for their existence in the Discussion.

Our study also suggests that a SRCAP-independent, DNA methylation-insensitive mechanism of H2A.Z loading exists, which we suspect to be mediated by Tip60-C. In line with this possibility, our data suggest that Tip60-C binds DNA in a DNA methylation-insensitive manner in Xenopus egg extract. Since antibodies to deplete Tip60-C from Xenopus egg extract are currently unavailable, we were unable to directly test that hypothesis and decided not to include Tip60-C into our final model as we lacked experimental evidence for its role. However, whether or not Tip60-C is the complex responsible for the DNA methylation-insensitive pathway does not influence our final conclusion that SRCAP-C plays a major role in DNA methylation-sensitive H2A.Z loading. We are planning to edit our manuscript to more comprehensively discuss these points.

Please note that while Berta et al reported that DNA methylation increases at H2A.Z loci in tumors defective in SRCAP-C, they selected those regions based off where H2A.Z is typically enriched within normal tissues (Berta et al., 2021). They did not show data indicating whether H2A.Z is still retained specifically at those analyzed loci upon mutation of SRCAP-C subunits. Thus, although we greatly admire their work and are pleased that many of our findings align with theirs, their paper did not directly address whether SRCAP-C itself differentiates between DNA methylation status nor the impact that has on H2A.Z and DNA methylation colocalization. In contrast, our Xenopus egg extract system, where de novo methylation is undetectable (Nishiyama et al., 2013; Wassing et al., 2024) offers a unique opportunity to examine the direct impact of DNA methylation on H2A.Z deposition using controlled synthetic DNA substrates. Corroborated with our demonstration that DNA binding of SRCAP-C is suppressed by DNA methylation, we believe that our manuscript provides a specific mechanism that can explain the preferential deposition of H2A.Z at hypomethylated genomic regions.

Reviewer #2 (Public review):

This manuscript aims to elucidate the mechanistic basis for the long-standing observation that DNA methylation and the histone variant H2A.Z occupy mutually exclusive genomic regions. The authors test two hypotheses: (i) that DNA methylation intrinsically destabilizes H2A.Z nucleosomes, thereby preventing H2A.Z retention, and (ii) that DNA methylation suppresses H2A.Z deposition by ATPdependent chromatin-remodelling complexes. However, neither hypothesis is rigorously addressed. There are experimental caveats, issues with data interpretation, and conclusions that are not supported by the data. Substantial revision and additional experiments, including controls, would be required before mechanistic conclusions can be drawn. Major concerns are as follows:

We appreciate the critical assessment of our manuscript by this reviewer. Although we acknowledge the limitations of our study and will revise the manuscript to better describe them, we would like to respectfully argue against the statement that our "conclusions […] are not supported by the data".

(1) The cryo-EM structure of methylated H2A.Z nucleosomes is insufficiently resolved to address the central mechanistic question: where the methylated CpGs are located relative to DNA-histone contact points and how these modifications influence H2A.Z nucleosome structure. The structure provides no mechanistic insights into methylation-induced destabilization.

The fact that the DNA resolution in the methylated structure was not high enough to resolve the positions of methylated CpGs despite a high overall resolution of 2.78 Å implies that 1) the Sat2R-P DNA was not as stably registered as the 601L sequence, requiring us to create two alternative Sat2R-P atomic models to account for the variable positioning in our samples, and 2) that the presence of DNA methylation increases that positional variability. We understand that one may prefer to see highly resolved density around each methylation mark, but we do believe that our inability to accomplish that is actually a feature rather than a weakness and has important biological implications. The decrease in local DNA resolution on the methylated Sat2R-P structure compared to its unmethylated counterpart is meaningful and suggests to us that DNA methylation weakens overall DNA wrapping and positioning on the nucleosome, supported by the increased flexibility seen at the linker DNA ends as well as an increase in the population of highly shifted nucleosomes amongst the methylated particles. Additionally, one major view in the DNA methylation/nucleosome stability field is that the presence of DNA methylation can make DNA stiffer and harder to bend, causing opening and destabilization of nucleosomes (Ngo et al., 2016). The increased opening of linker DNA ends and accessibility of methylated H2A.Z nucleosomes in our hands also aligns with such an idea, again suggesting decreased histone-DNA contact stability on methylated DNA substrates. We plan to revise the writing in our manuscript to better reflect these ideas.

The experimental system also lacks physiological relevance. The template DNA sequence is artificial, despite the existence of well-characterised native genomic sequences for which DNA methylation is known to inhibit H2A.Z incorporation. Alternatively, there are a number of studies examining the effect of DNA methylation on nucleosome structure, stability, DNA unwrapping, and positioning. Choosing one of these DNA sequences would have at least allowed a direct comparison with a canonical nucleosome. Indeed, a major omission is the absence of a cryo-EM structure of a canonical nucleosome assembled on the same DNA template - this is essential to assess whether the observed effects are H2A.Z-specific.

The reviewer raises a fair question about whether canonical H2A would experience the same DNA methylation-dependent structural effects. We had considered solving the H2A structures, however, ultimately decided against it for a few reasons. First, there already exists crystal structures of canonical H2A nucleosomes using a DNA sequence highly similar to our Sat2R-P with and without the presence of DNA methylation (PDB: 5CPI and 5CPJ). The authors of this study did not see any physical differences present in their structures (Osakabe et al., 2015). Additionally, we had included canonical H2A conditions within our restriction enzyme accessibility assay and did not see a significant impact of DNA methylation on those samples (Fig 3). Because of the previous report and our own negative data, we expected that only limited additional insights would be obtained from the canonical H2A structures and decided not to pursue that analysis.

One of the primary reasons we chose the Sat2R-P sequence was, as noted above, that there already was a published study examining how DNA methylation affects nucleosome structure using a variant of this sequence which we could compare to our results, as the reviewer has suggested. We did have to modify the sequence, namely by making it palindromic, in order to increase the final achievable resolution. We viewed the Sat2R-P sequence as an attractive candidate because it is physiologically relevant; the initial sequence was taken directly from human satellite II. Several modifications were made for technical reasons, including making the sequence palindromic as described above and also ensuring that each CpG is recognizable by a methylation-sensitive restriction enzyme so that we could be certain about the degree of methylation on our substrates. These practical concerns outweighed the necessity of maintaining a strict physiological sequence to us. However, we still believe the final Sat2R-P more closely mimics physiological sequences than Widom 601. Additionally, human satellite II is a highly abundant sequence in the human genome that is known to undergo large methylation changes on the onset of many disorders, like cancer, as well as during aging. Thus, there are interesting biological questions surrounding how the methylation state of this particular sequence affects chromatin structure.

Furthermore, it has been reported that satellite II is devoid of H2A.Z (Capurso et al., 2012). Beyond those reasons, the satellite II sequence is generally interesting to our lab because we have been studying genes involved in ICF syndrome, where hypomethylation of satellite II sequences forms one of the hallmarks of this disorder (Funabiki et al., 2023; Jenness et al., 2018; Wassing et al., 2024). We understand that sequence context plays a large role in nucleosome wrapping and stability. This is why we strived to test multiple sequences in each of our assays. We do agree that it would be interesting to use DNA sequences where H2A.Z binding has already been described to be affected in a DNA methylation-dependent manner, forming an exciting future study to pursue.

Furthermore, the DNA template is methylated at numerous random CpG sites. The authors' argument that only the global methylation level is relevant is inconsistent with the literature, which clearly demonstrates that methylation effects on canonical nucleosomes are position-dependent. Not all CpG sites contribute equally to nucleosome stability or unwrapping, and this critical factor is not considered.

We did not argue that only the global methylation level is relevant. We also would appreciate it if the reviewer could provide specific references that "clearly demonstrates that methylation effects on canonical nucleosomes are position-dependent". We are aware of a series of studies conducted by Chongli Yuan's group, including one testing the effect of placing methylated CpGs at different positions along the Widom 601 sequence. In that study (Jimenez-Useche et al., 2013), they did find that positioning of mCpGs has differential impacts on the salt resistance of the nucleosomes, with 5 tandem mCpG copies at the dyad causing the most dramatic nucleosome opening whereas having mCpGs only at the DNA major grooves, but not elsewhere, increased nucleosome stability. However, they did also find that methylation of the original Widom 601 sequence also caused destabilization, albeit to a lesser degree, and another study by the same group (Jimenez-Useche et al., 2014) also found that CpG methylation decreased nucleosome-forming ability for all tested variants of the Widom 601 sequence, regardless of CpG density or positioning.

Other studies monitored how distribution of methylated CpGs correlates with nucleosome positioning (Collings et al., 2013; Davey et al., 1997; Davey et al., 2004). However, these studies assessed the sequence-dependent effects specifically on nucleosome assembly during in vitro salt dialysis, which is a different physical process than the one our manuscript focuses on, especially when considering the fact that H2A.Z is deposited onto preassembled H2A-nucleosome. Our cryo-EM analysis examines the structural changes induced by DNA methylation on already formed nucleosomes rather than the process of formation. Thus, probing accessibility changes using a restriction enzyme was the more appropriate biochemical assay to verify our structures.

We do very much agree that DNA context can influence nucleosome stability under different conditions. A study of molecular dynamics simulations concluded that the "combination of overall DNA geometrical and shape properties upon methylation" makes nucleosomes resistant to unwrapping (Li et al., 2022), while another modeling study suggests that DNA methylation impacts nucleosome stability in a manner dependent on DNA sequence, where "[s]trong binding is weakened and weak binding is strengthened" (Minary and Levitt, 2014). While G/C-dinucleotides are preferentially placed at major groove-inward positions in the nucleosomes in vivo (Chodavarapu et al., 2010; Segal et al., 2006) and G/C-rich segments are excluded from major groove-outward positions in Widom 601-like nucleosomes (Chua et al., 2012), methylated CpG dinucleotides are preferably, if not exclusively, located at major groove-outward positions in vivo. Mechanisms behind this biased mCpG positioning on the nucleosome remain speculative, likely caused by a combination of multiple factors, but the fact that we did not observe clear structural impacts using the Widom 601L sequence, where mCpGs are located at the major groove-outward and -inward positions ((Chua et al., 2012) and our structure), deserves a space for discussion. On the other hand, positioning of mCpG on satellite II-derived sequences that we used in this study was based on a physiological sequence, and thus it may not be appropriate to say that those CpGs are placed at multiple "random" positions. Although we decided not to discuss the position of 5mC on our Sat2R nucleosome structure due to ambiguous base assignments, neither of our two atomic models is consistent with an idea that DNA methylation repositions the CpG to the outward major grooves. As the potential contribution of how DNA methylation affects the nucleosome structure via modulating DNA stiffness has been extensively studied (Choy et al., 2010; Li et al., 2022; Ngo et al., 2016; Perez et al., 2012), we believe that it is appropriate to consider overall DNA properties along the whole DNA sequence, though we are willing to discuss potential positional effects in the revised manuscript.

Perhaps one of the most important points that we did not emphasize enough in our original manuscript was that in contrast to the subtle intrinsic effect of DNA methylation that was DNA sequence dependent, we observed SRCAP-dependent preferential H2A.Z deposition to unmethylated DNA over methylated DNA in both 601 and satellite II DNAs. In the revised manuscript, we will make the value of comparative studies on 601 and satellite II in two distinct mechanisms.

Finally, and most importantly, the reported increase in accessibility of the methylated H2A.Z nucleosome is negligible compared with the much larger intrinsic DNA accessibility of the unmethylated H2A.Z nucleosome. These data do not support the authors' hypothesis and contradict the manuscript's conclusions. Claims that methylated H2A.Z nucleosomes are "more open and accessible" must therefore be removed, and the title is misleading, given that no meaningful impact of DNA methylation on H2A.Z nucleosome stability is demonstrated.

We respectfully disagree with this reviewer's criticism. We investigated the potential impact of DNA methylation on nucleosome stability to the best of our abilities through complementary assays and reported our observations. The effect of DNA methylation is smaller than the difference between H2A.Z and H2A, but we were able to see an effect. It is also not uncommon for small differences to have functional impacts in biological systems. We agree that further testing is required to determine whether this subtle effect is functionally important, and it remains the subject of future research due to the many technical challenges associated with addressing said question. We would like to note that 18 years have passed since Daniel Zilberman first reported the antagonistic relationship between H2AZ and DNA methylation (Zilberman et al., 2008) but very few studies have since directly tested specific mechanistic hypotheses. We believe that our study lays the groundwork for exciting future investigation that better elucidates the pathways that contribute to this antagonism and will have meaningful impacts on the field in general. However, thanks to the reviewer's criticism, we realized that we did not clearly state in the Abstract the relatively subtle effect of DNA methylation on the intrinsic H2A.Z nucleosome stability. Therefore, we will accordingly revise the Abstract to make this point clearer.

(2) The cryo-EM structures of methylated and unmethylated 601L H2A.Z nucleosomes show no detectable differences. As presented, this negative result adds little value. If anything, it reinforces the point that the positional context of CpG methylation is critical, which the manuscript does not consider.

We believe the inclusion and factual reporting of negative data is important for the scientific community as one of the major issues currently in biology research is biased omission of negative data. We considered eLife as a venue to publish this work for this reason. We understand that the reviewer believes our 601L structures may detract from the overall message of our manuscript. We believe this data rather emphasizes the importance of DNA sequence context, something that the reviewer also rightfully notes. It is standard practice in the nucleosome field to use the Widom 601 sequence, along with its variants. Our experience has shown that use of an artificially strong positioning sequence may mask weaker physical effects that could play a physiological role. Thus, we were careful to validate all further assays with multiple DNA sequences and believed it important to report these sequence-dependent effects on nucleosome structure.

(3) Very little H3 signal coincides with H2A.Z at TSSs in sperm pronuclei, yet this is neither explained nor discussed (Supplementary Figure 10D). The authors need to clarify this.

Our H3 signal, which represents the global nucleosome population, is more broadly distributed across the genome than H2A.Z, which is known to localize at specific genomic sites. Since both histone types were sequenced to similar read depths, H3 peaks are generally shallower than H2A.Z and peak heights cannot be directly compared (i.e. they should be represented in separate appropriate data ranges).

(4) In my view, the most conceptually important finding is that H2A.Z-associated reads in sperm pronuclei show ~43% CpG methylation. This directly contradicts the model of strict mutual exclusivity and suggests that the antagonism is context-dependent. Similarly, the finding that the depletion of SRCAP reduces H2A.Z deposition only on unmethylated templates is also very intriguing. Collectively, these result warrants further investigation (see below).

(5) Given that H2A.Z is located at diverse genomic elements (e.g., enhancers, repressed gene bodies, promoters), the manuscript requires a more rigorous genomic annotation comparing H2A.Z occupancy in sperm pronuclei versus XTC-2 cells. The authors should stratify H2A.Z-DNA methylation relationships across promoters, 5′UTRs, exons, gene bodies, enhancers, etc., as described in Supplementary Figure 10A.

We agree that the substantial presence of co-localized H2A.Z and DNA methylation specifically in the sperm pronuclei samples and the changes in pattern between nuclear types are highly interesting and require further investigation. However, we faced technical challenges in our sequencing experiments that made us refrain from conducting a more detailed analysis for fear of over-interpreting potential artifacts. These challenges mainly stemmed from the difficulties in collecting enough material from Xenopus egg extracts and Tn5’s innate bias towards accessible regions of the genome. Because of this, open regions of the genome tend to be overrepresented in our data (as noted in our Discussion), making it challenging to rigorously compare methylation profiles and H2A.Z/H3 associated genomic elements.

While the degree of separation seems to be dependent on nuclei type, we still believe the antagonism exists in both the sperm pronuclei and XTC-2 samples when comparing H2A.Z methylation profiles to the corresponding H3 condition. Our study also demonstrates that H2A.Z is preferentially deposited to hypomethylated DNA in a manner dependent of SRCAP-C (the loss of SRCAP only reduces H2A.Z on unmethylated substrates) but an additional methylation-insensitive H2A.Z deposition mechanism also exists. We realized that this interesting point was not clearly highlighted in Abstract, so we will revise it accordingly.

(6) Although H2A.Z accumulates less efficiently on exogenous methylated substrates in egg extract, substantial deposition still occurs (~50%). This observation directly challenges the strong antagonistic model described in the manuscript, yet the authors do not acknowledge or discuss it. Moreover, differences between unmethylated and methylated 601 DNA raise further questions about the biological relevance of the cryo-EM 601 structures.

As depicted in Figure 6 and described in the Discussion, we clearly indicated that both methylation-sensitive and methylation-insensitive pathways exist to deposit H2A.Z within the genome. We also directly stated in our Discussion that a substantial proportion of H2A.Z colocalizes with DNA methylation both in our study as well as in previous reports, which is of major interest for future study. Additionally, we further discussed how the absence of transcription in Xenopus eggs is a likely reason for the more limited effect of DNA methylation restricting H2A.Z deposition in our egg extract system.

As noted in our response to (2), the lack of a clear impact on our 601L structures implies that this is due to the extraordinarily strong artificial nucleosome positioning capacity of the 601 sequence and its variants. Since 601 is heavily used in chromatin biology, including within DNA methylation research, such negative data are still useful to include and publish.

(7) The SRCAP depletion is insufficiently validated i.e., the antibody-mediated depletion of SRCAP lacks quantitative verification. A minimum of three biological replicates with quantification is required to substantiate the claims.

We are willing to address this concern. However, please note that our data showed that methylation-dependent H2A.Z deposition is almost completely erased upon SRCAP depletion, indicating functionally effective depletion. The specificity of the custom antibody against Xenopus SRCAP was verified by mass spectrometry. Additionally, we have obtained the same effect using another commercially available SRCAP antibody, though we did not include this preliminary result in our original manuscript. Due to its relatively low abundance and high molecular weight, SRCAP western blot signals are weak, making it challenging to quantify the degree of depletion. We also believe that the value of quantification in this context, with the points noted above, is rather limited. In the past, our lab has published papers on depleting the H3T3 kinase Haspin from Xenopus egg extracts (Ghenoiu et al., 2013; Kelly et al., 2010) but were never able to detect Haspin via western blot. This protein was only detected by mass spectrometry specifically on nucleosome array beads with H3K9me3 (Jenness et al., 2018). However, depletion of Haspin was readily monitored by erasure of H3T3ph, the enzymatic product of Haspin. In these experiments, it was impossible, and not critical, to quantitatively monitor the depletion of Haspin protein in order to investigate its molecular functions. Similarly, in this current study, the important fact is that depletion of SRCAP suppressed methylation-sensitive H2A.Z deposition and quantifying the degree of SRCAP depletion would not have a major impact on this conclusion.

(8) It appears that the role of p400-Tip60 has been completely overlooked. This complex is the second major H2A.Z deposition complex. Because p400 exhibits DNA methylation-insensitive binding (Supplementary Figure 14), it may account for the deposition of H2A.Z onto methylated DNA. This possibility is highly significant and must be addressed by repeating the key experiments in Figure 5 following p400-Tip60 depletion.

We are aware that the Tip60 complex is a very likely candidate for mediating DNA methylation insensitive H2A.Z deposition, which is why we tested whether DNA binding of p400 is methylation sensitive. Therefore, the reviewer's statement that we "completely overlooked" Tip60-C’s role does not fairly report on our efforts. We wished to test the potential contribution of Tip60-C, but, unfortunately, the antibodies we currently have available to us were not successful in depleting the complex from egg extract. Since we had no direct experimental evidence indicating the role Tip60-C plays, we decided to take a conservative approach to our model and leave the methylation-insensitive pathway as mediated by something still unidentified. While further investigating Tip60-C’s contribution to this pathway is of definite value, we do not believe that it impacts our major conclusion that SRCAP-C is the main mediator responsible for H2A.Z deposition on unmethylated DNA and thus remains a subject for future study.

(9) The manuscript repeatedly states that H2A.Z nucleosomes are intrinsically unstable; however, this is an oversimplification. Although some DNA unwrapping is observed, multiple studies show that H3/H4 tetramer-H2A.Z/H2B interactions are more stable (important recent studies include the following: DOI: 10.1038/s41594-021-00589-3; 10.1038/s41467-021-22688-x; and reviewed in 10.1038/s41576-02400759-1).

We understand that the H2A.Z stability field is highly controversial. We have introduced the many conflicting reports that have been published in the field but can further expand on the controversies if desired. We also understand that the term “nucleosome stability” is broad and encompasses many physical aspects. As noted in a prior response, we will better specify our use of the term within the manuscript. In our assays, we are most focused on the DNA wrapping stability of the nucleosome and have consistently seen in our hands that H2A.Z nucleosomes are much more open and accessible compared to canonical H2A on satellite II-derived sequences, regardless of methylation status. However, we do understand that many groups have observed the opposite findings while others have obtained results similar to us. We reported on our findings of the general H2A.Z stability with the hopes to help clarify some of the field’s controversies.

In summary, the current manuscript does not present a convincing mechanistic explanation for the antagonism between DNA methylation and H2A.Z. The observation that H2A.Z can substantially coexist with DNA methylation in sperm pronuclei, perhaps, should be the conceptual focus.

We appreciate this reviewer’s advice. However, please note that the first author who led this project has already successfully defended their PhD thesis primarily based on this project, making it impractical and unrealistic to completely change the focus of this manuscript to include an entirely new avenue of research. We believe that our data provide important insights into the mechanisms by which H2A.Z is excluded from methylated DNA, particularly via the DNA methylation-sensitive binding of SRCAP-C, which has never been described before. We agree that many questions are still left unanswered, including the exact molecular mechanism behind how DNA methylation prevents SRCAP-C binding. We have preliminary data that suggest none of the known DNA-binding modules of SRCAP-C, including ZNHIT1, by themselves can explain this sensitivity. This implies that domain dissection in the context of the holo-SRCAP complex is required to fully address this question. We believe this represents a very exciting future avenue of study; however, it does not negate our finding that SRCAP-C itself is important for maintaining the DNA methylation/H2A.Z antagonism. Therefore, we respectfully disagree with this reviewer's summary statement, which misleadingly undermines the impact of our work.

Reviewer #3 (Public review):

Summary:

Histone variant H2A.Z is evolutionarily conserved among various species. The selective incorporation and removal of histone variants on the genome play crucial roles in regulating nuclear events, including transcription. Shih et al. aimed to address antagonistic mechanisms between histone variant H2A.Z deposition and DNA methylation. To this end, the authors reconstituted H2A.Z nucleosomes in vitro using methylated or unmethylated human satellite II DNA sequence and examined how DNA methylation affects H2A.Z nucleosome structure and dynamics. The cryo-EM analysis revealed that DNA methylation induces a more open conformation in H2A.Z nucleosomes. Consistent with this, their biochemical assays showed that DNA methylation subtly increases restriction enzyme accessibility in H2A.Z nucleosomes compared with canonical H2A nucleosomes. The authors identified genome-wide profiles of H2A.Z and DNA methylation using genomic assays and found their unique distribution between Xenopus sperm pronuclei and fibroblast cells. Using Xenopus egg extract systems, the authors showed SRCAP complex, the chromatin remodelers for H2A.Z deposition, preferentially deposit H2A.Z on unmethylated DNA.

Strengths:

The study is solid, and most conclusions are well-supported. The experiments are rigorously performed, and interpretations are clear. The study presents a high-resolution cryo-EM structure of human H2A.Z nucleosome with methylated DNA. The discovery that the SRCAP complex senses DNA methylation is novel and provides important mechanistic insight into the antagonism between H2A.Z and DNA methylation.

We are grateful that this reviewer recognizes the importance of our study.

Weaknesses:

The study is already strong, and most conclusions are well supported. However, it can be further strengthened in several ways.

(1) It is difficult to interpret how DNA methylation alters the orientation of the H4 tail and leads to the additional density on the acidic patch. The data do not convincingly support whether DNA methylation enhances interactions with H2A.Z mono-nucleosomes, nor whether this effect is specific to methylated H2A.Z nucleosomes.

The altered H4 tail orientation and extra density seen on the acidic patch were incidental findings that we thought could be interesting for the field to be aware of but decided not to follow up on as there were other structural differences that were more directly related to our central question. We do believe that the above two differences are linked to each other because we used a highly purified and homogenous sample for cryo-EM analysis and the H4 tail/acidic patch interaction is a well characterized contact that mediates inter-nucleosome interactions. Additionally, other groups have reported that the presence of DNA methylation causes condensation of both chromatin and bare DNA (cited within our manuscript), though the mechanics behind this phenomenon remain to be elucidated. We believed that our structure data may also align with those findings. However, the reviewer is fair in pointing out that we do not provide further experimental evidence in verifying the existence of these increased interactions. We can revise our writing to clarify that these points are currently hypotheses rather than validated results.

(2) It remains unclear whether DNA methylation alters global H2A.Z nucleosome stability or primarily affects local DNA end flexibility. Moreover, while the authors showed locus-specific accessibility by HinfI digestion, an unbiased assay such as MNase digestion would strengthen the conclusions.

We would like to thank the reviewer for bringing up these issues. Although our current data cannot explicitly clarify these possibilities, we favor an idea that DNA methylation specifically alters histone to DNA contacts and that this effect is felt globally across the entire nucleosome rather than only at specific locations. The intrinsic flexibility of linker DNA ends means that that region tends to exhibit the greatest differences under different physical influences, hence the focus on characterizing that area; flexibility of a thread on a spool is most pronounced at the ends. However, we also found that the DNA backbone of H2A.Z on methylated DNA had a lower local resolution compared to its unmethylated counterpart, despite that structure having a higher global resolution, which suggested to us that DNA positioning along the nucleosome is overall weaker under the presence of DNA methylation. This is corroborated by the increased population of open/shifted structures in our classification analysis. The reviewer raises a fair point about the use of a specific restriction enzyme versus MNase. We agree that our accessibility assay is highly influenced by the position of the restriction site and have previously seen that moving the cut site too close to the linker DNA end will abolish any DNA methylation-dependent differences. We did initially attempt an MNase digestion-based assay, but the data were not as reproducible as with the use of a specific restriction enzyme. We do not know the reason behind this irreproducibility though we believe that the processivity of MNase could make it difficult to capture subtle effects like those induced by DNA methylation on already highly accessible H2A.Z nucleosomes. Overall, while we believe that DNA methylation does exert a physical effect, its subtlety may explain the many contradictory studies present within the DNA methylation and nucleosome stability field.

References

Berta, D.G., H. Kuisma, N. Valimaki, M. Raisanen, M. Jantti, A. Pasanen, A. Karhu, J. Kaukomaa, A. Taira, T. Cajuso, S. Nieminen, R.M. Penttinen, S. Ahonen, R. Lehtonen, M. Mehine, P. Vahteristo, J. Jalkanen, B. Sahu, J. Ravantti, N. Makinen, K. Rajamaki, K. Palin, J. Taipale, O. Heikinheimo, R. Butzow, E. Kaasinen, and L.A. Aaltonen. 2021. Deficient H2A.Z deposition is associated with genesis of uterine leiomyoma. Nature. 596:398–403.

Capurso, D., H. Xiong, and M.R. Segal. 2012. A histone arginine methylation localizes to nucleosomes in satellite II and III DNA sequences in the human genome. BMC Genomics. 13:630.

Chodavarapu, R.K., S. Feng, Y.V. Bernatavichute, P.Y. Chen, H. Stroud, Y. Yu, J.A. Hetzel, F. Kuo, J. Kim, S.J. Cokus, D. Casero, M. Bernal, P. Huijser, A.T. Clark, U.

Kramer, S.S. Merchant, X. Zhang, S.E. Jacobsen, and M. Pellegrini. 2010. Relationship between nucleosome positioning and DNA methylation. Nature. 466:388–392.

Choy, J.S., S. Wei, J.Y. Lee, S. Tan, S. Chu, and T.H. Lee. 2010. DNA methylation increases nucleosome compaction and rigidity. J Am Chem Soc. 132:1782–1783.

Chua, E.Y., D. Vasudevan, G.E. Davey, B. Wu, and C.A. Davey. 2012. The mechanics behind DNA sequence-dependent properties of the nucleosome. Nucleic Acids Res. 40:6338–6352.

Collings, C.K., P.J. Waddell, and J.N. Anderson. 2013. Effects of DNA methylation on nucleosome stability. Nucleic Acids Res. 41:2918–2931.

Davey, C., S. Pennings, and J. Allan. 1997. CpG methylation remodels chromatin structure in vitro. J Mol Biol. 267:276–288.

Davey, C.S., S. Pennings, C. Reilly, R.R. Meehan, and J. Allan. 2004. A determining influence for CpG dinucleotides on nucleosome positioning in vitro. Nucleic Acids Res. 32:4322–4331.

Funabiki, H., I.E. Wassing, Q. Jia, J.D. Luo, and T. Carroll. 2023. Coevolution of the CDCA7-HELLS ICF-related nucleosome remodeling complex and DNA methyltransferases. Elife. 12.

Ghenoiu, C., M.S. Wheelock, and H. Funabiki. 2013. Autoinhibition and polo-dependent multisite phosphorylation restrict activity of the histone h3 kinase haspin to mitosis. Mol Cell. 52:734–745.

Jenness, C., S. Giunta, M.M. Muller, H. Kimura, T.W. Muir, and H. Funabiki. 2018. HELLS and CDCA7 comprise a bipartite nucleosome remodeling complex defective in ICF syndrome. Proc Natl Acad Sci U S A. 115:E876–E885.

Jimenez-Useche, I., J. Ke, Y. Tian, D. Shim, S.C. Howell, X. Qiu, and C. Yuan. 2013. DNA methylation regulated nucleosome dynamics. Sci Rep. 3:2121.

Jimenez-Useche, I., D. Shim, J. Yu, and C. Yuan. 2014. Unmethylated and methylated CpG dinucleotides distinctively regulate the physical properties of DNA. Biopolymers. 101:517–524.

Kelly, A.E., C. Ghenoiu, J.Z. Xue, C. Zierhut, H. Kimura, and H. Funabiki. 2010. Survivin reads phosphorylated histone H3 threonine 3 to activate the mitotic kinase Aurora B. Science. 330:235– 239.

Li, S., Y. Peng, D. Landsman, and A.R. Panchenko. 2022. DNA methylation cues in nucleosome geometry, stability and unwrapping. Nucleic Acids Res. 50:1864–1874.

Minary, P., and M. Levitt. 2014. Training-free atomistic prediction of nucleosome occupancy. Proc Natl Acad Sci U S A. 111:6293–6298.

Ngo, T.T., J. Yoo, Q. Dai, Q. Zhang, C. He, A. Aksimentiev, and T. Ha. 2016. Effects of cytosine modifications on DNA flexibility and nucleosome mechanical stability. Nat Commun. 7:10813.

Nishiyama, A., L. Yamaguchi, J. Sharif, Y. Johmura, T. Kawamura, K. Nakanishi, S. Shimamura, K. Arita, T. Kodama, F. Ishikawa, H. Koseki, and M. Nakanishi. 2013. Uhrf1-dependent H3K23 ubiquitylation couples maintenance DNA methylation and replication. Nature. 502:249–253.

Osakabe, A., F. Adachi, Y. Arimura, K. Maehara, Y. Ohkawa, and H. Kurumizaka. 2015. Influence of DNA methylation on positioning and DNA flexibility of nucleosomes with pericentric satellite DNA. Open Biol. 5.

Perez, A., C.L. Castellazzi, F. Battistini, K. Collinet, O. Flores, O. Deniz, M.L. Ruiz, D. Torrents, R. Eritja, M. Soler-Lopez, and M. Orozco. 2012. Impact of methylation on the physical properties of DNA. Biophys J. 102:2140–2148.

Segal, E., Y. Fondufe-Mittendorf, L. Chen, A. Thastrom, Y. Field, I.K. Moore, J.P. Wang, and J. Widom. 2006. A genomic code for nucleosome positioning. Nature. 442:772–778.

Wassing, I.E., A. Nishiyama, R. Shikimachi, Q. Jia, A. Kikuchi, M. Hiruta, K. Sugimura, X. Hong, Y. Chiba, J. Peng, C. Jenness, M. Nakanishi, L. Zhao, K. Arita, and H. Funabiki. 2024. CDCA7 is an evolutionarily conserved hemimethylated DNA sensor in eukaryotes. Sci Adv. 10:eadp5753.

Zilberman, D., D. Coleman-Derr, T. Ballinger, and S. Henikoff. 2008. Histone H2A.Z and DNA methylation are mutually antagonistic chromatin marks. Nature. 456:125–129.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors designed two sets of experiments to explore the molecular mechanisms underlying the mutually exclusive distribution of H2A.Z and DNA methylation previously reported by several groups.

First, they examined how DNA methylation affects the physical stability of H2A.Z-containing nucleosomes. Although their results point to subtle differences between nucleosomes assembled on methylated versus unmethylated DNA, the authors did not extend their analyses to directly test the stability of these H2A.Z-containing nucleosomes under more challenging conditions. Prior studies have demonstrated that certain nucleosomes, such as those containing H3.3-H2A.Z or H2A.Z-H3K56Q, exhibit specific instability, but such instability is only revealed under challenging conditions, for example, altered salt concentrations or the presence of additional factors like FACT (PMID: 17575053; PMID: 19633671; PMID: 19639024; PMID: 41303375). In light of this literature, the observable structural features noted here for nucleosomes containing H2A.Z and methylated DNA are suggestive of increased instability, yet the authors did not employ comparable approaches to rigorously test whether such instability might explain the absence of H2A.Z from methylated genomic regions.

As a result, at this stage of analysis, the idea that nucleosomes containing both H2A.Z and methylated DNA are intrinsically unstable, and that this instability accounts for the depletion of H2A.Z from methylated regions, remains unsubstantiated.

We thank the reviewer's constructive criticisms. Through our response to these points, we were able to significantly improve our manuscript, including major rewriting of the Abstract and Discussion as well as incorporation of new data.

We agree that combinations with other histone variants, modifications, and mutations could further affect our observed impact of DNA methylation on H2A.Z-nucleosome stability. What we observed based on satellite II-derived DNA was that DNA methylation made H2A.Znucleosomes (with H3.2) more open, although the effect of DNA methylation is relatively small (as compared to the general impact of H2A.Z incorporation). We readily admit that such a subtle physical effect is unlikely to be the main driver of the antagonistic distribution of H2A.Z and DNA methylation, though small physical changes have been known to influence larger biological functions, and sought to describe additional regulatory factors that could play major roles.

We also agree that H3.3 is of major interest when discussing H2A.Z. In our Xenopus egg extract experiments using DNA beads, the primary H3 variant deposited is H3.3 as no DNA replication occurs on the beads to allow for H3.1/.2 replication-coupled deposition. From those experiments, we demonstrated that preferential loading of H2A.Z can be primarily explained by SRCAP. In other words, in the absence of SRCAP, loading/retention of H2A.Z on H3.3nucleosomes was not noticeably affected by DNA methylation, indicating that DNA methylation’s physical effects on H2A.Z nucleosomes plays little, if any, role in the preferential accumulation of H2A.Z on unmethylated DNA at least in the context of synthetic DNA beads incubated in

Xenopus egg extract lacking active transcription. Our sequencing data hints at the interesting possibility that transcription, along with other factors missing in egg extract, may be involved in further pruning H2A.Z from methylated DNA which conceivably could take advantage of subtle physical alterations. However, we agree we lack firm supporting evidence for such a mechanism which led us to forgo including that in our final model figure and we instead only report on our observations with discussions on potential biological implications and limitations. Of note, it has been reported that the H2A.Z nucleosome is more accessible than the H2A nucleosome, while inclusion of H3.3 does not further enhance accessibility of the H2A.Z nucleosome (PMID 38920622). We have now noted these points in the Discussion of our revised manuscript.

We appreciate and agree with this reviewer’s point that nucleosome instability sometimes requires challenging conditions to be fully revealed. However, in our system, use of H2A.Z was the challenge provided as we find in our hands that H2A.Z by itself substantially destabilizes histone-DNA contacts compared to canonical H2A. And it is only with this already destabilized nucleosome that we see further enhancement of accessibility/openness in the presence of DNA methylation. This is similar to findings by [PMID: 23260052] that reported that only an intrinsically destabilized sub-population of canonical H2A nucleosomes on 601 DNA experienced detectable physical changes in the presence of DNA methylation.

In response to this reviewer's comment, we edited the Abstract and Discussion to clearly note the subtly of the impact of DNA methylation on H2A.Z nucleosome structure, and that the potential functional significance remains an open question.

Second, the authors investigated whether SRCAP-C contributes to preferential H2A.Z incorporation into unmethylated DNA. The absence of H2A.Z from methylated regions does not necessarily imply that it cannot be incorporated there; it may instead reflect the chromatin environment associated with DNA methylation, which could disfavor SRCAP-C activity, whereas open chromatin environments strongly promote SRCAP-dependent H2A.Z deposition.

This reviewer suggested an alternative model where SRCAP prefers to act on open chromatin and that the apparent preferential H2A.Z deposition to unmethylated DNA is due solely to the increased accessibility associated with unmethylated DNA. Following such a model, one would predict that SRCAP-C's preference to unmethylated DNA would be eliminated on nucleosome-free DNA in Xenopus egg extracts. To test this alternative model, we repeated the SRCAP-C binding experiment in egg extracts depleted of the HIRA complex, the H3.3-H4 chaperone responsible for de novo nucleosome assembly on exogenously added DNA in egg extracts. Contrary to this prediction, both SRCAP and ZNHIT1 still display preferential binding to unmethylated DNA substrates in HIRA-depleted extracts in which nucleosome assembly is suppressed (newly added Suppl Fig 16). The results argue that discrimination of SRCAP-C from methylated DNA is not due to a potential effect of chromatin compaction by DNA methylation. Furthermore, our new result is in line with an idea that SRCAP employs 1D diffusion on the linker DNA before engaging the H2A nucleosome (PMID 39131301), implying that discrimination of SRCAP-C from methylated linker DNA contributes to this process. This is now illustrated in the new model Figure 6.

Please note we also indicate in both our model and in text that there exists an additional methylation-insensitive mechanism that drives H2A.Z deposition on methylated DNA, leading to a substantial amount of colocalized H2A.Z and DNA methylation. Why two different deposition pathways for H2A.Z differing in their methylation sensitivities must exist is an interesting topic for future work and has not been described prior to our report.

This interpretation is consistent with the authors' own comparative mapping of H2A.Z and DNA methylation in sperm pronuclei incubated in egg extract versus a transcriptionally active Xenopus fibroblast line. They observed that about 40% of H2A.Z-associated genomic DNA is methylated in sperm pronuclei, but only 3% in fibroblasts. As they note, the major difference between these systems is the presence of transcription in fibroblasts, a process known to drive H2A.Z eviction/recycling, and which is absent in the egg-extract system. Thus, no specific inhibition of SRCAP-C by methylated DNA needs to be invoked: H2A.Z deposition on both methylated and unmethylated accessible regions, followed by preferential eviction from methylated sites in active nuclei, could fully account for the observed patterns.

As the reviewer correctly notes here, we proposed that transcription is likely to play an important role in pruning H2A.Z from methylated DNA. Our observations and proposed mechanism do not argue against the possible existence of a DNA methylation-insensitive, transcription-dependent mechanism that promotes dissociation of H2A.Z from methylated DNA, which we believe likely would be correlated to gene body methylation. In fact, we did propose in our Discussion that such a transcription-mediated mechanism may conceivably take advantage of the subtly destabilized DNA wrapping of H2A.Z nucleosomes on methylated DNA to further selectively prune H2A.Z at colocalized regions. However, such a mechanism would be an additional component to what we have already described and does not explain the observed preferential recruitment of SRCAP-C to unmethylated DNA in Xenopus egg extracts in the absence of active transcription.

In this respect, studies from the Felsenfeld laboratory showing that double-variant nucleosomes are highly unstable under physiological ionic conditions are particularly relevant (PMID: 19633671; PMID: 19639024). They demonstrated that such unstable nucleosomes are only evident under low ionic strength extraction conditions, emphasizing that the apparent absence of H2A.Z may reflect facilitated removal rather than failure of assembly.

The authors may also have been influenced by the study of Berta et al. (cited in the manuscript), which examined uterine leiomyomas harboring somatic or germline mutations in SRCAP-C subunits. In those tumors, the normal association of H2A.Z with accessible, active chromatin, and its exclusion from methylated regions, was lost. However, this observation does not demonstrate that SRCAP-C actively prevents H2A.Z incorporation into methylated DNA. Instead, it may simply reflect that in the absence of SRCAP-C, a default, less efficient deposition pathway operates regardless of whether the chromatin environment is normally permissive or restrictive for SRCAP-dependent activity.

Even if one accepts the more straightforward interpretation proposed by the present authors, that SRCAP-C is actively inhibited by methylated DNA, as suggested by their pull-down experiments from Xenopus egg extracts using unmethylated and methylated DNA, the hypothesis lacks mechanistic support.

Considering this reviewers' criticism, we have expanded our discussion to indicate a possibility that SRCAP-C may have an alternative mechanism to find open chromatin independent of DNA methylation status. However, our data show that SRCAP-C preferentially binds to unmethylated DNA in a manner independent of transcription or other epigenetic status in Xenopus egg extracts, and that SRCAP-C carries the major mechanism that explains preferential deposition of H2A.Z to unmethylated DNA. Therefore, we believe that our study for the first time offers a mechanistic explanation of how H2A.Z discrimination from methylated DNA is accomplished through SRCAP-dependent H2A.Z deposition.

The following points summarize the issues discussed above:

(1) The authors did not sufficiently test the hypothesis that H2A.Z-methylated DNA nucleosomes are inherently unstable and could explain the exclusion of H2A.Z from methylated genomic regions.

We stand by our conclusion that DNA methylation has an intrinsic capacity to make the H2A.Z nucleosome more open and accessible, even though the effect is subtle. We did not argue that this subtle effect can fully explain the exclusion of H2A.Z from methylated genomic regions. Rather, our Xenopus egg extract experiment suggested that in the transcriptionally inactive egg extract setting, such a mechanism plays little or no role and it is SRCAP-C instead that is the major driver. Whether this physical mechanism also contributes to their exclusion in cells with active transcription remains a future subject of study.

(2) The proposed active role of SRCAP-C in preventing H2A.Z assembly on methylated DNA is supported only by limited experimental data and lacks a mechanistic explanation. In particular, this hypothesis does not account for the significant H2A.Z assembly observed on methylated DNA regions in sperm nuclei after incubation in egg extract.

We respectfully disagree with this summary assessment. Our conclusions are well aligned with the substantial H2A.Z association with methylated DNA in sperm pronuclei assembled in Xenopus egg extracts seen. We demonstrated that:

(1) In transcriptionally-silent Xenopus egg extracts using synthetic DNA beads, DNAbinding of SRCAP-C is inhibited by DNA methylation.

(2) In this set up, H2A.Z is preferentially, if not exclusively, loaded to unmethylated DNA over methylated DNA.

(3) Depletion of SRCAP-C almost completely eliminated preferential association of H2A.Z to unmethylated DNA, while leaving some DNA methylation-insensitive H2A.Z loading.

(4) These data indicate the presence of a SRCAP-C-dependent, DNA methylationsensitive mechanism as well as a SRCAP-C-independent, DNA-methylation-insensitive mechanism to load H2A.Z to chromatin. This conclusion matches well with our genomic analysis showing that H2A.Z is preferentially but not exclusively loaded to hypomethylated genomic segments to sperm pronuclei in Xenopus egg extracts.

(5) As we clearly discussed, this SRCAP-C-dependent mechanism by itself is insufficient to explain the much clearer exclusion of H2A.Z in somatic cells. We discussed the possibility that transcription contributes to further pruning of H2A.Z from methylated DNA.

To deliver this overall message with nuances that we noted above, we have heavily revised the Abstract, the model Figure 6, and Discussion. Thanks to the criticisms raised by this reviewer, we believe that our revised manuscript has been significantly improved.

Reviewer #2 (Recommendations for the authors):

(1) A major omission is the absence of a cryo-EM structure of a canonical nucleosome assembled on the same DNA template - this is essential to assess whether the observed effects are H2A.Z-specific.

We had considered solving the H2A structures, however, ultimately decided against it for a few reasons. First, there already exists crystal structures of canonical H2A nucleosomes using a DNA sequence highly similar to our Sat2R-P with and without the presence of DNA methylation (PDB: 5CPI and 5CPJ). The authors of this study did not see any physical differences present in their structures (Osakabe et al., 2015). Additionally, we had included canonical H2A conditions within our restriction enzyme accessibility assay and did not see a significant impact of DNA methylation on those samples (Fig 3). Because of the previous report and our own negative data, we expected that only limited additional insights would be obtained from the canonical H2A structures and decided not to pursue that analysis, considering the cost and effort for this additional cryo-EM analysis.

(2) The reported increase in accessibility of the methylated H2A.Z nucleosome is negligible compared with the much larger intrinsic DNA accessibility of the unmethylated H2A.Z nucleosome. Claims that methylated H2A.Z nucleosomes are "more open and accessible" must therefore be removed, and the title is misleading, given that no meaningful impact of DNA methylation on H2A.Z nucleosome stability is demonstrated.

We respectfully disagree with this reviewer's criticism. We investigated the potential impact of DNA methylation on nucleosome stability to the best of our abilities through complementary assays and reported our observations. The effect of DNA methylation is smaller than the difference between H2A.Z and H2A, but we were able to see an effect. It is also not uncommon for small differences to have functional impacts in biological systems. We agree that further testing is required to determine whether this subtle effect is functionally important, and it remains the subject of future research due to the many technical challenges associated with addressing said question. We would like to note that 18 years have passed since Daniel Zilberman first reported the antagonistic relationship between H2AZ and DNA methylation (Zilberman et al., 2008) but very few studies have since directly tested specific mechanistic hypotheses. We believe that our study lays the groundwork for exciting future investigation that better elucidates the pathways that contribute to this antagonism and will have meaningful impacts on the field in general. However, thanks to the reviewer's criticism, we realized that we did not clearly state in the Abstract that the effect of DNA methylation on intrinsic H2A.Z nucleosome stability is relatively subtle. We will accordingly revise the Abstract, the model Figure 6, and Discussion to make this point clearer.

(3) The cryo-EM structures of methylated and unmethylated 601L H2A.Z nucleosomes show no detectable differences. As presented, this negative result adds little value and should be removed.

We believe the inclusion and factual reporting of negative data is important for the scientific community as one of the major issues currently in biology research is biased omission of negative data. We considered eLife as a venue to publish this work for this reason. We understand that the reviewer believes our 601L structures may detract from the overall message of our manuscript, however, we believe that this data rather emphasizes the importance of DNA sequence context, something that the reviewer also rightfully notes. It is standard practice in the nucleosome field to use the Widom 601 sequence, along with its variants. Our experience has shown that use of an artificially strong positioning sequence may mask weaker physical effects that could play a physiological role. Thus, we were careful to validate all further assays with multiple DNA sequences and believed it important to report these sequence-dependent effects on nucleosome structure.

(4) Very little H3 signal coincides with H2A.Z at TSSs in sperm pronuclei, yet this is neither explained nor discussed (Supplementary Figure 10D). The authors need to clarify this.

Our H3 signal, which represents the global nucleosome population, is more broadly distributed across the genome than H2A.Z, which is known to localize at specific genomic sites. Since both histone types were sequenced to similar read depths, H3 peaks are generally shallower than H2A.Z and peak heights cannot be directly compared (i.e. they should be represented in separate appropriate data ranges).

(5) In my view, the most conceptually important finding is that H2A.Z-associated reads in sperm pronuclei show ~43% CpG methylation. This directly contradicts the model of strict mutual exclusivity and suggests that the antagonism is context-dependent. Similarly, the finding that the depletion of SRCAP reduces H2A.Z deposition only on unmethylated templates is also very intriguing. Collectively, these result warrants further investigation (see below).

(6) Given that H2A.Z is located at diverse genomic elements (e.g., enhancers, repressed gene bodies, promoters), the manuscript requires a more rigorous genomic annotation comparing H2A.Z occupancy in sperm pronuclei versus XTC-2 cells. The authors should stratify H2A.ZDNA methylation relationships across promoters, 5′UTRs, exons, gene bodies, enhancers, etc., as described in Supplementary Figure 10A.

We appreciate recognition of the importance of our finding by this reviewer. We agree that the substantial presence of co-localized H2A.Z and DNA methylation specifically in the sperm pronuclei samples and the changes in pattern between nuclear types are highly interesting and require further investigation. However, we faced technical challenges in our sequencing experiments that made us refrain from conducting a more detailed analysis for fear of over-interpreting potential artifacts. These challenges mainly stemmed from the difficulties in collecting enough material from Xenopus egg extracts and Tn5’s innate bias towards accessible regions of the genome. Because of this, open regions of the genome tend to be overrepresented in our data (as noted in our Discussion), making it challenging to rigorously compare methylation profiles and H2A.Z/H3 associated genomic elements.

While the degree of separation seems to be dependent on nuclei type, we still believe the antagonism exists in both the sperm pronuclei and XTC-2 samples when comparing H2A.Z methylation profiles to the corresponding H3 condition. Our study also demonstrates that H2A.Z is preferentially deposited to hypomethylated DNA in a manner dependent of SRCAP-C (the loss of SRCAP only reduces H2A.Z on unmethylated substrates) but an additional methylationinsensitive H2A.Z deposition mechanism also exists. We realized that this interesting point was not clearly highlighted in Abstract, so we will revise it accordingly.

(7) Although H2A.Z accumulates less efficiently on exogenous methylated substrates in egg extract, substantial deposition still occurs (~50%). This observation directly challenges the strong antagonistic model described in the manuscript. The authors need to discuss this in more detail.

As depicted in Figure 6 and described in the Discussion, we indicated that both methylation-sensitive and methylation-insensitive pathways exist to deposit H2A.Z within the genome. We also directly stated in our Discussion that a substantial proportion of H2A.Z colocalizes with DNA methylation both in our study as well as in previous reports, which is of major interest for future study. Additionally, we further discussed how the absence of transcription in Xenopus eggs is a likely reason for the more limited effect of DNA methylation restricting H2A.Z deposition in our egg extract system. In the revised manuscript, we heavily edited the Discussion to better clarify these points.

(8) The SRCAP depletion is insufficiently validated, i.e., the antibody-mediated depletion of SRCAP lacks quantitative verification. A minimum of three biological replicates with quantification is required to substantiate the claims.

In response to this, quantification of the SRCAP depletion is now included as Supplementary Figure 13A and B. Since our anti-ZNHIT1 antibodies reproducibly detected ZNHIT1 on DNA beads isolated from egg extracts, we have conducted additional verification of the SRCAP depletion by probing for SRCAP and ZNHIT1 on DNA beads, confirming that these proteins were depleted on DNA beads upon immunodepletion with anti-SRCAP antibodies (Author response image 1). To further validate this conclusion, we added data showing that the effect of SRCAP depletion on methylation-sensitive H2A.Z deposition was reproduced through use of a different commercially available antibody raised against human SRCAP (newly added Suppl Fig 14).

Author response image 1.

Verification of SRCAP depletion using DNA beads. DNA beads were incubated in interphase-cycled Xenopus egg extract that had been depleted with either our custom SRCAP antibody or an IgG negative control. SRCAP and ZNHIT1 association was then assessed via Western Blot.

(9) It appears that the role of p400-Tip60 has been completely overlooked. This complex is the second major H2A.Z deposition complex. Because p400 exhibits DNA methylation-insensitive binding (Supplementary Figure 14), it may account for the deposition of H2A.Z onto methylated DNA. This possibility is highly significant and must be addressed by repeating the key experiments in Figure 5 following p400-Tip60 depletion.

Thank you very much for raising this interesting point. We were aware that the TIP60 complex is a very likely candidate for mediating DNA methylation-insensitive H2A.Z deposition, which is why we tested whether DNA binding of p400 is methylation sensitive (shown in the revised Supplementary Figure 15). We wished to test the potential contribution of TIP60-C, but, unfortunately, the antibodies we currently have available to us were not successful in depleting the complex from egg extract. Since we had no direct experimental evidence indicating the role TIP60-C plays, we decided to take a conservative approach to our model and leave the methylation-insensitive pathway as mediated by something still unidentified. While further investigating TIP60-C’s contribution to this pathway is of definite value, we do not believe that it impacts our major conclusion that SRCAP-C is the main mediator responsible for H2A.Z deposition on unmethylated DNA and thus remains a subject for future study. However, we have now added descriptions to note that TIP60-C is a likely candidate to execute the SRCAPindependent and methylation-insensitive mechanism of H2A.Z loading in Xenopus egg extracts. In the model figure, we initially did not include Tip60-C, but we now infer TIP60-C is a likely candidate in the revised model (Figure 6) to facilitate the future research in the field.

(10) The manuscript repeatedly states that H2A.Z nucleosomes are intrinsically unstable; however, this is an oversimplification. Although some DNA unwrapping is observed, multiple studies show that H3/H4 tetramer-H2A.Z/H2B interactions are more stable (important recent studies include the following: DOI: 10.1038/s41594-021-00589-3; 10.1038/s41467-021-22688-x; and reviewed in 10.1038/s41576-024-00759-1). These references should be considered.

We appreciate that the reviewer points out this important issue. Although we had described that controversy exists regarding how H2A.Z and DNA methylation contributes to nucleosome stability, it was not clearly explained. We understand that this confusion was in part due to the term “nucleosome stability”, which is broad and encompasses many physical aspects. As noted in a prior response, we now better specify our use of the term within the manuscript, emphasizing the nucleosome openness and accessibility, particularly at the nucleosome core particle entry/exit sites. As noted by published studies (PMID 38920622), the impact on nucleosome stability may differ between the internal and external segments of nucleosomal DNA. In our assays, we are most focused on the DNA wrapping stability of the nucleosome and have consistently seen in our hands that H2A.Z nucleosomes are much more open and accessible at DNA ends compared to canonical H2A on satellite II-derived sequences, regardless of methylation status. However, we do understand that many groups have observed the opposite findings while others have obtained results similar to us. This may be caused by usage of different assays (for example, nucleosome assembly during salt dialysis or salt sensitivity vs openness/accessibility of preassembled nucleosome). In the Discussion of the revised manuscript, we now explain these factors, with the hope that our study will help clarify some of the field’s controversies.

Reviewer #3 (Recommendations for the authors):

(1) Since the cryo-EM structure determined by single-particle analysis represents only one major population, it would be important to determine the dyad axis position by complementary biochemical assays, such as MNase-seq or chemical digestion by the Fenton reaction (PMID: 22929776).

We would like to thank the reviewer for bringing up this important issue. We agree that the high-resolution structure represents only a subpopulation in which we specifically selected for the most stably wrapped nucleosomes in each sample. This issue is why we then supplemented our high-resolution structure with our in-silico classification analysis to survey the overall structure distribution of the full nucleosome particle population. The classification input contains all nucleosome-like particles picked from both unmethylated and methylated sample micrographs mixed together, ensuring that all particles are taken into consideration and that both samples have been analyzed in an identical manner. From our sorting analysis, we find an increased population of open and shifted nucleosome structures present in our methylated DNA sample, indicating destabilization of DNA-histone wrapping with DNA methylation. This is corroborated by the lower local resolution seen on the DNA backbone of our high-resolution H2A.Z on methylated DNA structure, despite it having a higher global resolution compared to its unmethylated counterpart. This suggested to us that DNA positioning along the nucleosome is overall weaker under the presence of DNA methylation.

The reviewer raises a fair point about the use of a specific restriction enzyme versus MNase. We agree that our accessibility assay is highly influenced by the position of the restriction site and have previously seen that moving the cut site too close to the linker DNA end will abolish any DNA methylation-dependent differences. We realized that we did not explain how we decided to place the HinfI site in the context of our solved cryo-EM structure. In the revised Figure 3B, we now illustrate that the HinfI site is located at a segment where H2A/H2A.Z directly contacts the DNA and explained that this segment belongs to the region that exhibited clear methylation-induced flexibility in our cryo-EM structures. Thus, our structure helped us design this experiment.

We did initially attempt an MNase digestion-based assay, but the data were not as reproducible as with the use of a specific restriction enzyme. We do not know the reason behind this irreproducibility though we believe that the processivity of MNase could make it difficult to capture subtle effects like those induced by DNA methylation on already highly accessible H2A.Z nucleosomes, as subtle technical errors in the MNase concentration can have significant effects. Overall, while we believe that DNA methylation does exert a physical effect, its subtlety may explain the many contradictory studies present within the DNA methylation and nucleosome stability field.

(2) I assume that the authors confirmed complete DNA methylation by restricted enzyme digestion. It would be helpful to include this validation in supplementary figures.

We would like to thank the reviewer for pointing out that this critical verification was missing from our initial manuscript. DNA methylation of Sat2R-P and Sat2R was verified via BstBI digestion (Suppl Fig 1B and 7D, respectively); 601L verified with HpaII digestion (Suppl Fig 6B); and 19x601 DNA verified via BstUI digestion (Suppl Fig 11A). All data has been added to the specified figures. Unfortunately, the 16xHSat2 DNA substrate we used in our assays does not contain appropriate cut-sites for methylation-sensitive restriction enzymes. Due to that, we always prepared the 16xHSat2 DNA in parallel with the 19x601 substrate under identical conditions then use digestion of the 19x601 substrate to verify quality of methylation for each batch. To more directly verify methylation of 16xHSat2 DNA, we used Xenopus laevis ZHX2 and ZHX3, which we recently identified as proteins that selectively associate with methylated DNA in Xenopus egg extracts. Although identification and characterization of Xenopus ZHX2/3 will be described elsewhere, previous published proteomic studies have also identified mammalian ZHXs as proteins that enrich on methylated DNA (PMID 21029866, 23434322). By incubating DNA beads in Xenopus egg extract and probing for endogenous ZHX2/3 (our antibody recognizes both ZHX2 and ZHX3), we verified that ZHXs selectively binds to methylated 16xHSat2 but not unmethylated DNA (Author response image 2). Although this does not necessarily verify that all CpGs in 16xHSat2 were methylated, we observed comparable methylation-induced inhibition of SRCAP binding between 16x601 and 16HSat2, supporting our conclusion.

Author response image 2.

Verification of 16xHSat2 methylation status via ZHX2/3 protein binding. 16xHSat2 DNA beads were incubated in Xenopus egg extract and endogenous ZHX2/3 protein binding assessed via Western Blot with a custom generated antibody that recognizes both ZHX2 and ZHX3.

(3) Figure 1A: The dyad position is difficult to identify. Please indicate it clearly using a distinct color (not green).

We now directly indicate each sequence midpoint with a black triangle and also changed the font of DNA sequences to further clarify that the dyad resides at the palindromic center.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript presents an extensive body of work and an outstanding contribution to our understanding of the IFN type I and III system in chickens. The research started with the innovative approach of generating KO chickens that lack the receptor for IFNα/β (IFNAR1) or IFN-λ (IFNLR1). The successful deletion and functional loss of these receptors was clearly and comprehensively demonstrated in comparison to the WT. Moreover, the homozygous KO lines (IFNAR1-/- or IFNLR1-/-) were found to have similar body weights, and normal egg production and fertility compared to their WT counterparts. These lines are a major contribution to the toolbox for the study of avian/chicken immunology.

The significance of this contribution is further demonstrated by the use of these lines by the authors to gain insight into the roles of IFN type I and IFN-type III in chickens, by conducting in ovo and in vivo studies examining basic aspects of immune system development and function, as well as the responses to viral challenges conducted in ovo and in vivo.

Based on solid, state-of the-art methods and convincing evidence from studies comparing various immune system related functions in the IFNAR1-/- or IFNLR1-/- lines to the WT, revealed that the deletion of IFNAR1 and/or IFNLR1 resulted in:

(1) impaired IFN signaling and induction of anti-viral state;

(2) modulation of immune cell profiles in the peripheral blood circulation and spleen;

(3) modulation of the cecum microbiome;

(4) reduced concentrations of IgM and IgY in the blood plasma before and following immunization with model antigen KLH, whereby also line differences in the time-course of the antibody production were observed;

(5) decrease in MHCII+ macrophages and B cells in the spleen of IFNAR1 KO chickens, although the MHCII-expression per cell was not affected in this line; and

(6) reduction in the response of αβ1 TCR+ T cells of IFNAR1 KO chickens as suggested by clonal repertoire analyses.

These studies were then followed by examination of the role of type I and type III IFN in virus infection, using different avian influenza A virus strains as well as an avian gamma corona virus (IBV) in in ovo challenge experiments. These studies revealed: viral titers that reflect virus-species and strain-specific IFN responses; no differences in the secretion of IFN-α/β in both KO compared to the WT lines; a predominant role of type I IFN in inducing the interferon-stimulated gene (ISG) Mx; and that an excessive and unbalanced type I IFN response can harm host fitness (survival rate, length of survival) and contribute to immunopathology.

Based on guidance from the in ovo studies, comprehensive in vivo studies were conducted on host-pathogen interactions in hens from the three lines (WT, IFNAR1 KO, or IFNLR1 KO). These studies revealed the early appearance of symptoms and poor survival of hens from the IFNR1 KO line challenged with H3N1 avian influenza A virus; efficient H#N1 virus replication in IFNAR1 KO hens, increased plasma concentrations of IFNα/β and mRNA expression of IFN-λ in spleens of the IFNAR1 KO hens; a pro-inflammatory role of IFN-λ in the oviduct of hens infected with H3N1 virus; increased proinflammatory cytokine expression in spleens of IFNAR1 KO hens, and Impairment of negative feedback mechanisms regulating IFN-α/β secretion in IFNAR1-KO hens and a significant decrease in this group's antiviral state; additionally it was demonstrated that IFN-α/β can compensate IFN-λ to induce an adequate antiviral state in the spleen during H3N1 infection, but IFN-λ cannot compensate for IFN-α/β signaling in the spleen.

Strengths:

(1) Both the methods and results from the comprehensive, well-designed, and well-executed experiments are considered excellent. The results are well and correctly described in the result narrative and well presented in both the manuscript and supplement Tables and Figures. Excellent discussion/interpretation of results.

(2) The successful generation of the type I and type III IFN KO lines offers unprecedented insight and opens multiple new venues for exploring the IFN system in chickens. The new knowledge reported here is direct evidence of the high impact of this model system on effectively addressing a critical knowledge gap in avian immunology.

(3) The thoughtful selection of highly relevant viruses to poultry and human health for the in ovo and in vivo challenge studies to examine and assess host-pathogen interactions in the IFNR KO and WT lines.

(4) Making use of the unique opportunities in the chicken model to examine and evaluate the host's IFN system responses to various viral challenges in ovo, before conducting challenge studies in hens.

(5) The new knowledge gained from the IFNAR1 and IFNLR1 KO lines will find much-needed application in developing more effective strategies to prevent health challenges like avian influenza and its devastating effects on poultry, humans, and other mammals.

(6) The excellent cooperation and contributions of the co-authors and institutions.

Weaknesses:

No weaknesses were identified by this reviewer.

We thank Reviewer #1 for the very positive and thoughtful evaluation of our manuscript. We appreciate the recognition of the effort involved in generating and characterizing the IFNAR1^-/- and IFNLR1^-/- chicken lines and for highlighting their significance as valuable tools for advancing avian immunology.

We are grateful for the reviewer’s clear summary of our findings and for acknowledging the quality of the experimental design, data presentation, and interpretation. The encouraging feedback affirms the broader impact of our study and its contribution to understanding type I and type III interferon biology and antiviral defense mechanisms in chickens.

We have carefully considered all reviewer comments and revised the manuscript accordingly to further clarify methodological details and improve the presentation of our results.

Reviewer #1 (Recommendations for the authors):

Minor suggestions/corrections:

(1) Line 192, 193, 196 - the superscript "+" sign appears to be underlined.

We corrected the formatting of all superscript "+" symbols (L 192-196).

(2) L195: ...in the spleen "of both IIFNR KO lines" (or some clarification of what you are comparing).

The sentence was revised to read “in the spleen of both IFNR knockout lines” for clarity (L 195).

(3) L198: replace "highlighting" with "and".

“Highlighting” was replaced with “and” as suggested (L 198).

(4) L231 and 235: change "monocytes" to "macrophages" as this description appears to refer to spleen cells. Also, make this change in Figure 3b and in the Figure 3 caption (e.g. monocytes/macrophages).

“Monocytes” was replaced with “macrophages” to accurately describe spleen cells. The same correction was made in Figure 3b and the Figure 3 caption as well as in the supplementary Figure 4 (L 229-234).

(5) L257: indicate this significant difference in Figure 5b.

The significant difference has now been clearly indicated in Figure 5b.

(6) L420, 421: change "monocytes" to "macrophages" as this discussion appears to refer to the spleen.

“Monocytes” was replaced with “macrophages” to reflect the correct cell type discussed in the spleen context (L 226-227).

(7) L564-565: has the anti-human MX antibody been shown to cross-react with chicken Mx?

We thank the reviewer for this valuable comment. Yes, the cross-reactivity of the anti-human MxA monoclonal antibody (clone M143, mouse IgGκ; Merck, Germany) with chicken Mx protein has been previously demonstrated. This antibody has been used successfully to detect chicken Mx in several published studies, including Schusser et al., Journal of Virology (2011). Accordingly, supporting references have been added to the revised manuscript (L584-586).

(8) L608: how were PBMC and splenocytes (mononuclear spleen cells?) isolated -Line 647 on page 14 mentions their isolation using Histopaque-1077 density gradient centrifugation

We thank the reviewer for this helpful comment. A detailed description of the isolation procedure for PBMCs and mononuclear spleen cells has now been added to the Materials and Methods section under the new subsection titled “Isolation of peripheral blood and splenic mononuclear cells” In this section, we specify that both PBMCs and splenic mononuclear cells were isolated using Histopaque®-1077 density gradient centrifugation as described on page (14), lines (668-676)

Reviewer #2 (Public review):

Summary:

This study attempts to dissect the contributions of type I and type III IFNs to the antiviral response in chickens. The first part of the study characterises the generation of IFNAR and IFNLR KO chicken strains and describes basic differences. Four different viruses are then tested in chicken embryos, while the subsequent analysis of the antiviral response in vivo is performed with one influenza H3N1 strain.

Strengths:

Having these two KO chicken strains as a tool is a great achievement. The initial analysis is solid. Clear effect of IFNAR deficiency in in vivo infection, less so for IFNLR deficiency.

Weaknesses:

(1) The antibody induction by KLH immunisation: No data indicated whether or not this vaccination induces IFN responses in wt mice, so the effects observed may be due to steady-state differences or to differential effects of IFN induced during the vaccination phase. No pre-immune results are shown. The differences are relatively small and often found at only one plasma dilution - the whole of Figure 4 could be condensed into one or two panels by proper calculation of Ab titers - would these titres be significantly different? This, as all of the other in vivo experiments, has not been repeated, if I understand the methods section correctly.

We thank the reviewer for the valuable comments and helpful suggestions.

Regarding interferon induction by KLH immunisation, we agree that KLH is not known to strongly induce type I or type III interferon responses. Importantly, the goal of this experiment was not to quantify IFN induction per se, but to assess how the absence of IFN receptors affects adaptive antibody responses under standard immunisation conditions. KLH is a highly immunogenic, copper‑containing extracellular oxygen‑carrier protein derived from the marine gastropod Megathura crenulata and is widely used as a T cell–dependent model antigen to study B‑cell activation, antibody production, and class switching in vivo (Harris & Markl, Micron 1999, doi: 10.1016/s0968-4328(99)00036-0; Schusser et al., 2016, doi: 10.1002/eji.201546171). Because chickens are extremely unlikely to encounter KLH under natural conditions, KLH behaves as a neo‑antigen, and anti‑KLH antibodies can be considered to arise from de novo adaptive responses rather than pre‑existing antigen experience. Owing to its structural complexity and unusual glycosylation, KLH provides broad antigenic stimulation and engages adaptive immune mechanisms largely independently of pathogen‑specific innate pattern recognition, while still supporting robust T helper cell responses (Swaminathan et al., 2014, doi: 10.1111/bcp.12422; Geyer et al., 2004, doi: 10.1016/j.micron.2003.10.033). This makes KLH particularly suitable for dissecting intrinsic differences in adaptive immune responses between genotypes.

We have now included pre-immune plasma controls (Figure 4 c, d), demonstrating that baseline antibody levels did not differ statistically between groups and were negligible prior to immunisation.

As for the use of different plasma dilutions, this was necessary to ensure that all samples were measured within the linear detection range of our in-house ELISA. For example, after the primary immunisation, IgY concentrations were relatively low (e.g., day 5 post-immunisation), and plasma samples had to be diluted only 1:100 to detect measurable differences between groups. In contrast, after the booster immunisation, IgY concentrations increased substantially, and lower dilutions such as 1:100 led to signal saturation. Therefore, higher dilutions (up to 1:1600) were required to keep the values within the measurable range.

Following the reviewer’s recommendation, we have now unified the presentation of results by showing data at a single representative dilution for each isotype: 1:100 for IgM (Figure 4C) and 1:1600 for IgY (Figure 4D). These dilutions fall within the linear part of the standard curve to distinguish between groups. We also calculated endpoint antibody titers, which confirmed that the observed differences remain statistically significant (p < 0.05).

Regarding experimental replication, the study design already incorporated sufficient biological replication and longitudinal sampling to ensure robustness of the findings. Each experimental group consisted of ten animals, including three animals that served as negative controls. In addition, animals were sampled at multiple time points following immunisation, allowing the dynamics of the antibody response to be monitored over time. This longitudinal design provides repeated biological measurements within the same experimental cohort and allows confirmation of consistent response patterns across time points. All ELISA measurements were performed in technical triplicates. Together, the combination of adequate group size, appropriate controls, repeated sampling over time, and technical replication provides sufficient statistical power and internal validation of the observed effects. Furthermore, all animal experiments were conducted under strict approval of the Government of Upper Bavaria and in accordance with German animal welfare regulations, which limit unnecessary repetition of in vivo experiments beyond the approved experimental design.

(2) The basic conundrum here and in later figures is never addressed by the authors: Situations where IFN type 1 and 3 signalling deficiency each have an independent effect (i.e., Figure 4d) suggest that they act by separate, unrelated mechanisms. However, all the literature about these IFN families suggests that they show almost identical signalling and gene induction downstream of their respective receptors. How can the same signalling, clearly active here downstream of the receptors for IFN type 1 or type 3, be non-redundant, i.e., why does the unaffected IFN family not stand in? This is a major difference from the mouse studies, which showed a rather subtle phenotype when only one of the two IFN systems was missing, but a massive reduction in virus control in double KO mice (the correct primary paper should be quoted here, not only the review by McNab). Reasons could be a direct effect of IFNab on B cells and an indirect effect of IFNL through non-B cells, timing issues, and many other scenarios can be envisaged. The authors do not address this question, which limits the depth of analysis.<br />

We thank the reviewer for this insightful comment. Indeed, this represents one of the most interesting and novel findings of our study. Unlike in mice, where both type I and type III interferon systems need to be disrupted to observe clear susceptibility to influenza infection, in our chicken model the loss of IFNAR1 alone was sufficient to render the animals highly susceptible. This highlights a key difference between mammalian and avian interferon biology and supports the main goal of our work, to investigate the specific biological activities of avian interferons rather than directly transferring conclusions from mammalian systems.

In relation to Figure 4d (anti-KLH IgY), we observed that both IFNAR1^-/- and IFNLR1^-/- animals reduced IgY levels compared to wild type at day 3 after the booster immunisation. However, by day 5 post-booster, IgY levels in IFNLR1^-/- animals had returned to wild-type levels, while IFNAR1-/- animals still showed significantly lower IgY. This indicates that type III IFN contributes to the early phase of the IgY response but that its absence can later be compensated by type I IFN signalling. In contrast, loss of type I IFN cannot be compensated by type III IFN, suggesting that type I IFN plays a more dominant or sustained role in antibody induction.

Although type I and type III IFNs share overlapping signaling pathways and induce similar sets of ISGs, their effects are not entirely redundant in chickens. A likely explanation is the difference in receptor distribution: IFNAR1 is broadly expressed across most cell types, while IFNLR1 expression is mainly confined to epithelial cells (Reuter et al. 2014, doi: 10.1128/jvi.02764-13; Santhakumar et al., 2017, doi: 10.3389/fimmu.2017.00049). This systemic versus localized receptor pattern likely determines the range of responsive cells and may account for the differential outcomes observed when either receptor is absent.

Taken together, our findings indicate that while type I and type III IFNs share overlapping signaling mechanisms, they maintain distinct biological functions in chickens, consistent with their differing receptor expression and cellular responsiveness. This contrasts with mammalian models, where redundancy between these systems is more apparent and only double knockouts show strong phenotypes especially during influenza infection (Mordstein et al., 2008, doi: 10.1371/journal.ppat.1000151; Mordstein et al., 2010, doi: 10.1128/jvi.00272-10). We have now cited this primary study instead of the McNab review and expanded the Discussion to reflect this interpretation (Page 10, Line 463-467).

(3) In the one in vivo experiment performed with chickens, only one virus was tested; more influenza strains should be included, as well as non-influenza viruses.

We thank the reviewer for this valuable suggestion. The main objective of the present study was to generate and characterize novel chicken models lacking type I and type III interferon receptors in order to investigate their physiological relevance and to obtain the first insights into their roles during viral infection with more emphasis on avian influenza. As part of this manuscript, we performed detailed in ovo experiments using both influenza and non-influenza viruses (Figure 6). These included three influenza strains: H1N1, a mammalian-adapted strain; H3N1, a low pathogenic avian strain showing features of high pathogenicity; and H9N2, a low pathogenic avian strain, as well as a non-influenza virus, the infectious bronchitis virus (IBV). The in ovo analyses revealed clear strain-dependent modulation of interferon responses, and have provided a comprehensive overview of virus-specific interferon activity in chickens. The subsequent in vivo experiment was therefore designed as a proof of concept using the most suitable viral strain to robustly challenge the immune system and to identify the distinct functions of chicken interferons.

(4) The basic conundrum of point 2 applies equally to Figure 6a; both KOs have a phenotype. Again in 6d, both IFNs appear to be separately required for Mx induction. An explanation is needed.

We thank the reviewer for raising this important point. We have revised the Discussion (page 10, lines 442-454) and provided supporting references to clarify how the composition of the chorioallantoic membrane (CAM) and virus tropism together determine the apparent requirement for type I and type III interferons. The CAM contains both epithelial and mesodermal–vascular layers, which support complementary interferon functions: type I IFN acts mainly in systemic and vascular compartments, while type III IFN provides localized protection at the epithelial surface. Consequently, viruses that replicate in both compartments (e.g., WSN33, H3N1) require both IFN pathways for maximal Mx induction (Figures 6a, 6d), whereas viruses with a predominant or prolonged epithelial phase (e.g., H9N2, IBV) at the time point analyzed are effectively controlled by type I IFN signaling alone.

These differences likely reflect virus-specific factors, including cell tropism, replication kinetics, and the spatial–temporal dynamics of receptor expression and signaling. Notably, our measurement of Mx expression at 24 hours post infection (hpi) may represent a phase when type I IFN signaling is dominant and can compensate for the absence of type III IFN. It remains possible that IFN-λ plays a more critical, non-redundant role at earlier stages post infection, when rapid antiviral protection is first required at the epithelial surface. Thus, the apparent redundancy observed at 24 hpi likely reflects temporal compensation and crosstalk between the IFN pathways rather than a lack of biological relevance for type III IFN.

(5) Line 308, where are the viral titers you refer to in the text? The statement that the results demonstrate that excessive IFNab has a negative impact is overstretched, as no IFN measurements of the infected embryos are shown here.

We thank the reviewer for this comment and would like to clarify that measurements of type I IFN (IFN-α/β) concentrations were indeed performed. The data are presented in Figure 6b and cited in the Results section (“Knockout of IFNAR1 and IFNLR1 did not affect IFN-α/β secretion in ovo”). To avoid misunderstanding, the Results section has been revised to explicitly reference the IFN-α/β measurements supporting this conclusion (line 302-309).

These data indicate that all genotypes produced comparable IFN-α/β levels upon viral infection, with the IBV infection inducing approximately tenfold higher IFN-α/β secretion than the influenza strains tested (Figure 6b). The interpretation that an excessive type I IFN response can negatively affect host fitness is based on the combination of quantified IFN-α/β data (Figure 6b) and survival probability results (Supplementary Figure 10), where embryos exhibiting the highest IFN-α/β levels (embryos of all genotypes infected with IBV and embryos infected with IFNLR1^-/- H9N2) showed the poorest survival despite moderate or low viral titers.

(6) The in vivo infection is the most interesting experiment, and the key outcome here is that IFN type 1 is crucial for anti-H3N1 protection in chickens, while type 3 is less impactful. However, this experiment suffers from the different time points when chickens were culled, so many parameters are impossible to compare (e.g., weight loss, histopathology, IFN measurements, and more). Many of these phenomena are highly dynamic in acute virus infections, so disparate time points do not allow a meaningful comparison between different genotypes. What are the stats in 7b? Is the median rather than the mean indicated by the line? Otherwise, the lines appear in surprising places. SD must be shown, and I find it difficult to believe that there is a significant difference in weight, for e.g., IFNAR KO, unless maybe with a paired t test. What is the statistical test?

We thank the reviewer for these thoughtful comments and agree that disease progression and sampling time can influence comparisons in acute infection studies. Hens were euthanized upon reaching predefined humane endpoint scores in full compliance with the Bavarian animal welfare regulations. Because the infection produced markedly different clinical kinetics among genotypes, all data were interpreted with reference to matched disease stages rather than absolute days post-infection.

For matched comparisons: Viral titers in the trachea and cloaca, as well as plasma IFN-α/β concentrations, were compared between day 2 in IFNAR1^-/- hens and day 3 in WT and IFNLR1^-/- hens, which represent equivalent clinical stages before the sharp viral rise seen later in WT and IFNLR1^-/- birds. At these comparable stages, viral titers were still low and IFN-α/β concentrations remained significantly lower in WT and IFNLR1^-/- than in IFNAR1^-/- hens (Figure 7c, d, f), indicating that uncontrolled viral replication and IFN-α/β secretion in the absence of type I signaling occur earlier and more intensely.

For Figure 7b: Because chickens reached humane endpoints at different days post infection (2 dpi for IFNAR1^-/- and 5–7 dpi for WT and IFNLR1^-/-), statistical comparisons were performed within each genotype using paired t-tests and all data were shown together as mean ± SD.

We acknowledge that unequal survival times limit direct temporal comparison. However, the consistent pattern across all parameters including early severe disease, high viral load, and excessive IFN-α/β secretion in IFNAR1^-/- hens versus delayed onset in WT and IFNLR1^-/-, supports the conclusion that type I IFN signaling is essential for early viral restriction and host survival, while type III IFN contributes mainly to localized inflammatory responses. The experiment cannot be repeated under the current animal welfare authorization.

(7) Figures 7e,f: these comparisons are very difficult to interpret as the virus loads at these time points already differ significantly, so any difference could be secondary to virus load differences.

We thank the reviewer for this valuable comment. We agree that viral load can influence interferon induction; however, our comparisons in Figures 7e and 7f were designed to reflect equivalent stages of disease progression rather than identical time points post-infection. For IFN-λ mRNA expression (Fig. 7e), spleens from IFNAR1^-/- hens were sampled on day 2 post-infection, when viral titers were maximal, and compared to WT and IFNLR1^-/- hens sampled on day 5 post-infection, at which point viral titers reached comparable levels. Thus, this comparison represents the phase of peak infection and systemic immune activation across all genotypes rather than an absolute temporal comparison.

Similarly, for IFN-α/β concentrations (Fig. 7f), two levels of comparison were made: between IFNAR1^-/- hens at day 2 post-infection (high viral titer) and WT and IFNLR1^-/- hens at day 3 (low viral titer), and between WT and IFNLR1^-/- hens at day 5 post-infection (high viral titer). In both cases, IFN-α/β levels remained disproportionately elevated in IFNAR1^-/- hens, indicating that the excessive type I IFN response is primarily due to the loss of receptor-mediated feedback regulation rather than viral load alone.

We have clarified this rationale in the legend of figure 7 and in the results (Line 338-345). We believe these results are valuable as they provide important insight into the temporal dynamics and regulatory interplay between type I and type III interferons during avian influenza infection.

Reviewer #2 (Recommendations for the authors):

Experiments need to be repeated. Comparisons in infection experiments must be done on the same day. More viruses need to be tested.

We thank the reviewer for these constructive recommendations. All infection experiments were conducted under approved animal welfare regulations, which limited the number of replicates and prevented repeating in vivo challenges beyond the authorized design, in line with the 3R principles, particularly Reduction, to avoid unnecessary animal use. To ensure comparability, samples were analyzed at matched disease stages rather than identical time points, as clarified in the revised figure legends (figure 7) and Results (Line 338-345). The study already includes multiple influenza and non-influenza viruses (H1N1, H3N1, H9N2, and IBV) tested in ovo to capture virus-specific interferon responses, while the in vivo H3N1 infection served as a proof-of-concept to dissect genotype-specific immune dynamics.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Ducrocq et al. present research exploring the genetic link between simple multicellular group formation (ace2Δ/ace2Δ) and its interaction with cell-cycle progression mutants (e.g., cln3Δ/cln3Δ), demonstrating that this combination can provide fitness benefits during fluctuating resource conditions, resulting in a rapid increase in the fraction of multicellular cell-cycle mutants over unicellular yeast without selection for multicellular size. Because both the multicellular phenotype and the regulatory link enabling faster escape from the stationary phase are controlled by the Ace2 transcription factor, this work demonstrates that multicellularity can arise as a side-effect of a completely independent fitness advantage unrelated to the benefits of group formation itself. As a "passenger phenotype," multicellularity could thus emerge for other selective reasons, potentially facilitating a later transition to more entrenched multicellularity if novel conditions arise where group formation becomes directly beneficial.

Strengths:

This work is novel and exciting for research exploring the very first steps of the transition from unicellularity to simple multicellularity. This is particularly significant because the formation of multicellular groups is almost always assumed to come at a cell-level fitness cost due to reduced reproductive fitness compared to remaining unicellular. This cell-level fitness cost generally needs to be outweighed by the benefits of multicellular group formation (e.g., large size escaping predation) for the multicellular phenotype to be stable, which is true for a large number of cases studied in the literature, where the multicellular phenotype can only evolve over unicellular competitors under strong selection for multicellular groups. However, this study presents an interesting case of a genetic and environmental condition under which individual cells (forming simple multicellular clusters) can actually have higher reproductive fitness than unicellular yeast. This demonstrates that the assumed cost at the single-cell level does not always apply. In summary, this work represents a unique example contrary to common assumptions regarding the costs of multicellular phenotypes, showing that simple multicellular phenotypes can evolve and remain stable without requiring strong selection for multicellular size or other benefits of group formation.

The claims and interpretation of the results align well with the data presented. This is due to the careful and straightforward experimental design testing predictions with a clear, stepwise methodology, ruling out alternative explanations and providing support for the proposed link between the mutations (ace2, cln3, and others), their impact on faster exit from quiescence, and thus earlier entry into reproduction in fresh media, resulting in higher fitness in the snowflake yeast phenotype compared to unicellular yeast.

Weaknesses:

The authors show that the same multicellular phenotype with higher cell-level fitness due to faster exit from the stationary phase can also be observed with alleles found at other loci in non-laboratory yeast strains, implying that the results are likely not specific to a peculiar case genetically engineered in laboratory strains, but that similar phenotypes may be present in nature. However, this remains to be explored further by examining the natural ecology of commercially available or wild yeast isolates and their genomes. This is by no means a weakness of this study and, therefore, not necessarily something the current work can improve. It does mean, however, that the relevance of these findings for early multicellularity in yeast, and even more so for nascent multicellularity in distinct taxa, remains to be explored in the future. Until then, it is difficult to make strong claims about how applicable these results would be for non-laboratory yeast and other taxa. Regardless, this work does its part by representing a very exciting finding.

Reviewer #2 (Public review):

Summary:

Here, the authors attempt to demonstrate that a simple model of multicellularity - snowflake yeast - exhibits key ecologically relevant changes in the regulation of the cell cycle. By examining the effects of the ace2 mutation in environments where multicellularity is not directly selected for or against, and combining it with mutations in key cell cycle regulators, they hope to show that mutations driving simple multicellularity can be selectively favored due to their effects on the release from quiescence rather than their effects on multicellularity itself.

Strengths:

The experiments performed are extensive and thorough. The yeast genotypes examined are judiciously chosen, so as to map out a functional model of the relationship between alterations to cell cycle control and changes to multicellularity phenotypes. Multiple possible interactions are examined, with the causal link and model of the relationship between the multicellular passenger phenotype and the selectable quiescence-release phenotype being well-supported. There are extensive controls demonstrating the separation between the 'passenger' multicellular phenotype and the cell cycle regulation phenotypes examined, including haploid/diploid strains with different multicellular phenotypes but similar cell cycle regulation phenotypes, and phenocopy strains in which downstream enzymes are deleted rather than key central regulators.

Weaknesses:

My only concerns about these results relate to the focus on selection on cell cycle control being examined in a model of multicellularity with key core cell cycle mutations rather than in a wild-type background, as this is a somewhat artificial system.

I believe, however, that the authors convincingly make their case that this work on the multicellular phenotypes of yeast represents a potent proof-of-concept that simple multicellularity can be driven into existence or selected for as a passenger phenotype due to pleiotropic effects of mutations under selection from real-world ecological pressures. They are able to connect this phenotype back to known mutations of particular cell cycle regulators (RB) in other multicellular lineages and demonstrate that ecologically relevant changes to the cell cycle are connected to multicellular phenotypes. As a proof of concept of the connection between these phenotypes, rather than a study of a particular event in the past of a living lineage, it makes a strong case.

A longstanding question in the field of multicellularity is the selective pressures that can drive simple multicellularity into existence and then act on simple multicells to drive their increased size and complexity. This work brings to the table tangible evidence of the possibility that, instead of being selected for on its own, simple multicellularity can be a side-effect of selection on other key phenotypes.

This separates the question of the origins of multicellularity and the forces that drive its further evolution. This separation can reframe how the field is studied, especially in the context of the apparent dichotomy between dozens of origins of 'simple' multicellularity across the tree of life and a few origins of 'complex' multicellularity in the history of Earth. Especially in light of other evidence that multicellularity is connected to changes in cell cycle regulation, I believe that this is an important insight that will alter the way we think about the origins of this key evolutionary transition.

We thank the reviewers for their insightful comments on our work.

We agree with reviewer #1 that further experiments would be needed to figure out how the observations done on lab strains can apply to yeast in various ecological conditions and particularly in the wild. We here provide a proof of principle that multicellularity selection can arise as a side-effect. It obviously does not prove that it took place during yeast evolution, but we would like to emphasize that resource fluctuations are very common in ecological conditions, making it highly likely that the environmental conditions necessary for the selection of the side effects described have arisen.

We agree with reviewer #2 that our work on yeast strains is “somewhat artificial” as often the case with model organisms under laboratory conditions. Importantly though, we showed that the effect found with the cln3 knock-out mutation can be phenocopied by overexpression of WHI5 (encoding the yeast equivalent of Rb). We propose that variations in the levels of cell cycle regulators during evolution may have played a role in multicellularity selection as a side effect. We agree that this is merely a hypothesis to explain the selection of multicellularity (just like predator escape) and that there is no direct evidence that this occurred in the history of the lineage. Nevertheless, our work provides a first evidence that such a selection of multicellularity as a side effect could be possible, and gives a framework to understand how multicellularity can persist in the wild, even when it is not the primary target of selection.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

As mentioned in my public review, I very much appreciate this work, its interpretation for early multicellularity as an example opposite to the assumed cost of multicellular phenotypes, and the robust design behind the premise and claims. Therefore, my suggestions below are mostly aimed at improving the readability and data presentation.

(1) In the abstract, Lines 24-27 (the last sentence): This statement is worded too generally and therefore reads as too strong. I think the authors' work provides an example that multicellularity itself does not need to be beneficial all the time - this is really exciting and makes sense! However, there is a substantial body of work showing the origin and maintenance of multicellularity for its direct benefits. Relative to that body of work, this represents a special case, and therefore, while we should definitely reconsider the view that "multicellularity always comes at a cell-level fitness cost," we cannot overgeneralize these findings. Please consider reframing this statement.

Done, now line 25 (addition of “in some cases”)

(2) Line 48 (Introduction): "This mostly concerns two major regulators, RB and Cyclin D." Which organisms are you referring to? Please specify.

Done.

(3) In the Introduction, there are at least three sentences that need citations: L57-58, L59-60, and L65. For instance, I do not know what makes CLN3 the yeast functional equivalent of RB, and I wanted to verify this claim, but no references are cited. Please ensure citations are provided throughout the manuscript.

Done: ref 11,12 and 13 were added

(4) This is my main request regarding data collection and presentation. The authors share some microscopy images of mutant strains in Figure 2 for different purposes (e.g., Figure 2B compares the fraction of budded cells between two genotypes). However, I would appreciate seeing a collected microscopy figure showcasing the phenotypes of all genotypes that went into competition experiments, including the planktonic (WT lab strain) yeast, either where they appear or in a supplementary figure, all presented with the same magnification and scale to make them comparable. Because cell size, shape, and multicellular phenotype are all key aspects of the competition experiments, being able to see all those genotypes/phenotypes would prepare the reader to make predictions about the fitness assays and other experiments.

Done Supplementary Figure 1 B-E were added

(5) Related to my previous point, I would appreciate seeing cell size measurements for the different genotypes (both single cells of planktonic genotypes and single cells forming multicellular clusters). Cell size is a key trait that directly impacts the results shown in the paper, and summary statistics comparing them would be helpful for interpreting the results.

Done Supplementary Figure 1 F was added

(6) In competition experiments, the authors mix unicellular and multicellular yeast clusters at 50/50 and measure the fraction of a phenotype of interest (usually the % of snowflake). It took me a while to understand what is being counted under the "% snowflake yeast" category. This is because, while each cell in unicellular yeast should be counted as one unit, one can count a snowflake yeast composed of 50 cells as 50 units or as 1 unit. Please clearly state what is being counted for the Y-axis labeled "% of snowflake yeast" (or relabel those Y-axes in plots to make this clear).

Done: Added in figure legend 1A and Y-axes of competition figures

(7) I recommend editing the genotype labels in figures (see, for instance, Figure 1B, C, D). In Figure 1B, the bars are labeled as "CLN3/CLN3 co-culture" or "cln3Δ/cln3Δ co-culture," etc. These are actually co-cultures of SF vs. PK (with or without a CLN3 copy). Please consider using more representative labels that will be easier for readers to understand.

Done: this has been changed in all concerned figures

(8) In the Results, L225, you begin referring to AMN1368D as AMN1. I suggest using the full allelic form throughout the text so it will be clear each time that you are referring to that specific allele, as I was confused about whether you were discussing the allele or the gene AMN1 itself.

This has been changed throughout the text.

(9) Discussion, Lines 250-252, states that this is a "situation that is likely to happen very often under ecological conditions." Are there any examples you can cite?

Done, as also requested by reviewer #2 (now line 256-7)

(10) Lines 272-275 contain a strong, general statement suggesting that co-evolution of cell cycle regulation and multicellularity could be more general (which is acceptable as speculation). However, the suggestion that this co-evolution could have "started very early in the evolution of eukaryotic cells" is too speculative. I would recommend sticking with the alternative, suggesting that the link between the two phenotypes may be a case of convergent evolution.

Done

(11) Lines 278-279 are both vague and too bold. The text mentions a link between cancer and multicellularity and then extends this link through cell cycle regulators. Without explaining the connection between cancer and multicellularity and then trying to link it to cell cycle regulators, all in a few words without background, this sentence is too vague. Please consider deleting this or spending more time clearly explaining the link, which would at best still be speculative.

These speculative sentences were removed.

(12) First, I wanted to note that I highlighted Lines 284-287, as this passage is clearly written and provides a nice argument. I also wonder if you could mention that your work shows simple multicellular cluster formation should not always come at a cost, contrary to the general assumption in the literature, and add a few citations to support that claim. This would highlight how significant this work is within the broader multicellularity literature.

Changed in discussion (now line 242-4 with additional references 30 and 31)

(13) I recommend labeling the genotype of your "quintuple mutant" in Figure 3. You can refer to it as the quintuple mutant in the text, but I had to go back and forth to see what those mutations were when trying to think about potential genetic interactions. Even the legend of Figure 3 does not specify the genotype and refers to it only as the "quintuple mutant."

Now explicitly stated in the title of the figure

Reviewer #2 (Recommendations for the authors):

I find the presented research to be of high quality, with very important implications. I have suggestions for improvement of the manuscript, but they are largely stylistic, with one paper that I believe deserves citation regarding the proteins involved. I see little need for additional experiments or analysis, just a clearer description of the results and their significance.

(1) Line 62: Yeast CLN3 definitely performs the same role as cyclin D in the cell cycle, but has an unclear phylogenetic relationship with the rest of the cyclins. See Cross, Buchler, & Skotheim 2011 ("Evolution of networks and sequences in eukaryotic cell cycle control"). This reference also covers the functional relationship between RB and Whi5, referred to in nearby sentences, as does Medina, Walsh, and Buchler 2019 ("Evolutionary innovation, fungal cell biology, and the lateral gene transfer of a viral KilA-N domain").

The reference has been added

(2) Line 69: Is the question whether the evolution of G1/S regulation favoring multicellularity the question, or the two of them being connected such that the evolution of one can affect the other?

It is clearly the first of the two questions.

(3) Line 73: Comma after Ace2.

Done

(4) Line 76: It would be clearer to specify that snowflake and ACE2 yeast were co-cultured without settling selection or other selection that explicitly favors multicellularity, unlike in experiments where multicellular evolution is observed, as in Ratcliff publications.

This is now specified.

(5) Line 80: Specify which phenotypes observed for ace2 mutants are observed, specifically, both the multicellularity and the release from quiescence.

Done

(6) Line 146: This observation should be noted as another indication that the multicellular phenotype is not behind the selective pressure, because it is so different between unicells and multicells.

Overall, you have very strong evidence that this is the case, and emphasizing this would benefit the paper!

Done.

(7) Line 151: specify that you are maintaining yeast in proliferation in coculture.

Done.

(8) Line 181: This is another key experiment showing that the multicellular phenotype is not the causal reason for the change in quiescence. It might make things clearer to bring all these confirmatory experiments together, particularly the haploids and the sonicated single cells.

This is now clearly stated line 195.

(9) Line 225: The choice of referring to the non-laboratory strain as the 'AMN1' wild type default may be confusing to readers, who may treat the genetic background you are using as the ground truth wild type. I recommend throughout the paper always specifying the allele's amino acid to avoid any confusion.

The genotype is now clearly presented throughout the text.

(10) Line 238: I would continue to specify that the multicellular phenotype has no selective advantage, specifically when no selection for size is applied.

See added sentence Line 242-4 (revised version)

(11) Line 243: I would say that the evolution of cell cycle regulation may interact with the multicellular phenotype.

This was changed (now line 248)

(12) Line 244: Strike 'indeed' and the 'the' before AMN1 and ACE2.

Done

(13) Line 252: Suggest some ecological conditions under which quiescence exit is likely, such as boom and bust or moving from rotting fruit to rotting fruit.

Done

(14) Line 267: Are you suggesting that the specific genes AMN1 and ACE2 had particular effects on actual organisms in the past, or that it represents a broad pattern of evolution in which multicellularity could be more broadly related to exit from quiescence? I believe it is the latter, and I think that should be clearer.

Modified as suggested

(15) Line 280: In this paragraph, I think that the point being made could be slightly clearer - if I am not mistaken, you are making the distinction between the appearance of multicellularity and its refinement under selection, and that the former may be more common than previously believed, given this proof of concept. I think this can be made clearer. Furthermore, it is worth noting that all experiments that show effects of the multicellular phenotype are in mutant backgrounds, and explaining why this is still relevant to wild organisms. It might be taken by some as indicating that the multicellular phenotypes are not relevant to a wild population, but the connection to known RB mutations in known multicellular lineages and the fact that it is connected to a very key aspect of cell cycle regulation, I think, overcomes this issue, and this should be made clear.

Our study reveals a genetic link between multicellularity and Whi5 and Cln3, two important G1/S cell cycle regulators. Similar genetic interactions have been observed in phylogenetically distant species, reinforcing the idea that the interplay between cell cycle regulation and multicellularity is a general feature and not a mere artifact of mutant background.

The neutral fitness effect of multicellularity in wild-type backgrounds is particularly of interest. By being maintained as a side effect of selection on fundamental cellular processes, the neutral effect of multicellularity may have provided “an evolutionary scheme” for its repeated emergence throughout the tree of life. As such, the "passenger selection" hypothesis fits well with the observations of phenotypic reversibility and facultative multicellularity, despite varying and specific selective pressures. Our work thus gives a framework to understand how multicellularity can persist in the wild, even when it is not the primary target of selection.

(16) Line 314: What promoters are they driven by?

Specified

(17) Line 336: What was the culture volume, and the volume transferred?

Specified

(18) Line 362: How was the proportion of blue-stained cells scored? Manually, or with an imaging software cutoff?

Specified

(19) Figure 1: I think that the full genotypes of each strain should be specified, either in the legend or the key of the figure, rather than always specifying the ACE2 genotype and other mutations separately.

Done as requested by reviewer #1

(20) Figure 2E, 2F: Same as Figure 1, regarding genotypes.

Done

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Morgan et al. studied how paternal dietary alteration influenced testicular phenotype, placental and fetal growth using a mouse model of paternal low protein diet (LPD) or Western Diet (WD) feeding, with or without supplementation of methyl-donors and carriers (MD). They found diet- and sex-specific effects of paternal diet alteration. All experimental diets decreased paternal body weight and the number of spermatogonial stem cells, while fertility was unaffected. WD males (irrespective of MD) showed signs of adiposity and metabolic dysfunction, abnormal seminiferous tubules, and dysregulation of testicular genes related to chromatin homeostasis. Conversely, LPD induced abnormalities in the early placental cone, fetal growth restriction, and placental insufficiency, which were partly ameliorated by MD. The paternal diets changed the placental transcriptome in a sex-specific manner and led to a loss of sexual dimorphism in the placental transcriptome. These data provide a novel insight into how paternal health can affect the outcome of pregnancies, which is often overlooked in prenatal care.

Strengths:

The authors have performed a well-designed study using commonly used mouse models of paternal underfeeding (low protein) and overfeeding (Western diet). They performed comprehensive phenotyping at multiple timepoints, including the fathers, the early placenta, and the late gestation feto-placental unit. The inclusion of both testicular and placental morphological and transcriptomic analysis is a powerful, non-biased tool for such exploratory observational studies. The authors describe changes in testicular gene expression revolving around histone (methylation) pathways that are linked to altered offspring development (H3.3 and H3K4), which is in line with hypothesised paternal contributions to offspring health. The authors report sex differences in control placentas that mimic those in humans, providing potential for translatability of the findings. The exploration of sexual dimorphism (often overlooked) and its absence in response to dietary modification is novel and contributes to the evidence-base for the inclusion of both sexes in developmental studies.

Weaknesses:

The data are overall consistent with the conclusions of the authors. The paternal and pregnancy data are discussed separately, instead of linking the paternal phenotype to offspring outcomes. Some clarifications regarding the methods and the model would improve the interpretation of the findings.

(1) The authors insufficiently discuss their rationale for studying methyl-donors and carriers as micronutrient supplementation in their mouse model. The impact of the findings would be better disseminated if their role were explained in more detail.

We acknowledge the Reviewer’s comments regarding the amount of detail in support of the inclusion of methyl carriers and donors within our diet. Therefore, we will revise the manuscript to include more justification, especially within the Introduction section, for their inclusion. Please see lines 111-120.

(2) It is unclear from the methods exactly how long the male mice were kept on their respective diets at the time of mating and culling. Male mice were kept on the diet between 8 and 24 weeks before mating, which is a large window in which the males undergo a considerable change in body weight (Figure 1A). If males were mated at 8 weeks but phenotyped at 24 weeks, or if there were differences between groups, this complicates the interpretation of the findings and the extrapolation of the paternal phenotype to changes seen in the fetoplacental unit. The same applies to paternal age, which is an important known factor affecting male fertility and offspring outcomes.

We thank the Reviewer for their comments regarding the ages of the males analysed. As we had 5 treatment groups, and intended to generate a minimum of 8 litters of offspring per treatment group, this resulted in over 40 litters in total. In order to dissect these litters appropriately, and in a timely fashion, we had to stagger their generation over time. As such, this resulted in utilising our males at different ages/durations on the diet. However, in all our statistical analysis, we factored in the duration of time on the diet, which also acted as a proxy measure of paternal age. We also ensured that we staggered the generation of litters in each diet group so that any age effects were experienced across all paternal regimens.

We have revised the manuscript to acknowledge this fact and to highlight that the duration of time on any diet was factored into the statistical analysis.

(3) The male mice exhibited lower body weights when fed experimental diets compared to the control diet, even when placed on the hypercaloric Western Diet. As paternal body weight is an important contributor to offspring health, this is an important confounder that needs to be addressed. This may also have translational implications; in humans, consumption of a Western-style diet is often associated with weight gain. The cause of the weight discrepancy is also unaddressed. It is mentioned that the isocaloric LPD was fed ad libitum, while it is unclear whether the WD was also fed ad libitum, or whether males under- or over-ate on each experimental diet.

We agree with the Reviewer that the general trend towards a lighter body weight for our experimental animals is unexpected. We can confirm that all diets were fed ad libitum. However, as males were group housed, we were unable to measure food consumption for individual males. We also observed that for males fed the high fat diets, they often shredded significant quantities of their diet, rather than eating it, so preventing accurate measurement of food intake.

We also agree with the Reviewer that body weight can be a significant confounder for many paternal and offspring parameters. However, while the experimental males did become lighter, there were no statistical differences between groups in mean body weight. As such, body weight was not included as a variable within our statistical analysis.

(4) The description and presentation of certain statistical analyses could be improved.

(i) It is unclear what statistical analysis has been performed on the time-course data in Figure 1A (if any). If one-way ANOVA was performed at each timepoint (as the methods and legend suggest), this is an inaccurate method to analyse time-course data.

(ii) It is unclear what methods were used to test the relative abundance of microbiome species at the family level (Figure 2L), whether correction was applied for multiple testing, and what the stars represent in the figure. 3) Mentioning whether siblings were used in any analyses would improve transparency, and if so, whether statistical correction needed to be applied to control for confounding by the father.

We apologies for the lack of clarity regarding the statistical analyses. Going forward, we will revise the manuscript and include a more detailed description of the different analyses, inclusion of siblings and correction for multiple testing.

Reviewer #1 (Public review):

Summary:

The authors investigated the effects of a low-protein diet (LPD) and a high sugar- and fat-rich diet (Western diet, WD) on paternal metabolic and reproductive parameters and fetoplacental development and gene expression. They did not observe significant effects on fertility; however, they reported gut microbiota dysbiosis, alterations in testicular morphology, and severe detrimental effects on spermatogenesis. In addition, they examined whether the adverse effects of these diets could be prevented by supplementation with methyl donors. Although LPD and WD showed limited negative effects on paternal reproductive health (with no impairment of reproductive success), the consequences on fetal and placental development were evident and, as reported in many previous studies, were sex-dependent.

Strengths:

This study is of high quality and addresses a research question of great global relevance, particularly in light of the growing concern regarding the exponential increase in metabolic disorders, such as obesity and diabetes, worldwide. The work highlights the importance of a balanced paternal diet in regulating the expression of metabolic genes in the offspring at both fetal and placental levels. The identification of genes involved in metabolic pathways that may influence offspring health after birth is highly valuable, strengthening the manuscript and emphasizing the need to further investigate long-term outcomes in adult offspring.

The histological analyses performed on paternal testes clearly demonstrate diet-induced damage. Moreover, although placental morphometric analyses and detailed histological assessments of the different placental zones did not reveal significant differences between groups, their inclusion is important. These results indicate that even in the absence of overt placental phenotypic changes, placental function may still be altered, with potential consequences for fetal programming.

Weaknesses:

Overall, this manuscript presents a rich and comprehensive dataset; however, this has resulted in the analysis of paternal gut dysbiosis remaining largely descriptive. While still valuable, this raises questions regarding why supplementation with methyl donors was unable to restore gut microbial balance in animals receiving the modified diets.

We thank the Reviewer for their considered thoughts on the gut dysbiosis induced in our models the minimal impact of the methyl donors and carriers. We will include additional text within the Discussion to acknowledge this. However, at this point in time, we are unsure as to why the methyl donors had minimal impact. It could be that the macronutrients (i.e. protein, fat, carbohydrates) have more of an influence on gut bacterial profiles than micronutrients. Alternatively, due to the prolonged nature of our feeding regimens, any initial influences of the methyl donors may become diluted out over time. We will amend the text to reflect these potential factors.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have done an immense amount of work, which should be commended. In addition to the public review, I have a few suggestions for improvement.

(1) To further explore the weight discrepancy between the males subjected to diet alteration and those on the control diet, further details about the intake and provision of the diets would be beneficial. Seeing as the fat mass was increased in males fed a WD, do you have information on where the weight 'loss' originated from?

We thank the Reviewer for their insight into the changes in male body weight. We agree that the differences in total body weight verses the amount of adipose tissue, is intriguing. Unfortunately, we were unable to monitor the food intake of our animals for two main reasons. The first was that for animal welfare considerations, all our males were initially group housed prior to mating. This meant that typically, males were housed in groups of 4 during the initial feeding (pre-mating) period. Males were only housed singly upon them being used for mating. As such, it was not possible to obtain food consumption data for individual males.

A second limitation arose due to the high extend of males who were fed the Western Diet effectively shredding the diet. This meant that it was not possible to weight the food to obtain a crude idea of how much they were consuming. The reason for this shredding is not clear to us. All mice received environmental enrichment, as we did not observed this behaviour for our control or low protein diet fed males.

With regards to the weight of the other organs, we did not observe and significant overall changes in organ weight, or weight relative to body weight. Unfortunately, we did not have access to, or conduct any whole body scanning, such as DEXA, which would have given more insight into the body composition of our mice.

(2) The testicular abnormalities and gene expression findings are linked nicely to the offspring's story. This is not as compelling for other findings, including the gut microbiome changes, which are not discussed in the context of the fetoplacental outcomes. More discussion of the potential impact of paternal changes on fetal outcomes would strengthen claims that these findings are impactful.

We thank the Reviewer for their comments and suggestion. Our caution with connecting the gut microbiota to offspring development is that, to the best of our understanding, there is little data with regards to its effect on post-fertilisation development. While there is data showing that the microbiome can produce compounds and metabolites that can affect sperm quality and metabolism, lipid composition and testicular morphology, the connection with post-fertilisation development is limited. Additionally, as we saw no difference in fundamental fertility, as measured by changes in litter size, we propose that there no overall changes in the ability of the sperm from our experimental males to reach, fertilise and support development.

However, we acknowledge the Reviewers comments on strengthening the manuscript and so have included some additional text within the Discussion to highlight the links between the microbiome and male reproductive fitness. Please see lines 337-348.

(3) It is clarified in the methods that n=8 males were used in the study, but different nnumbers are shown for some parameters. It would improve transparency for the reader if it were clarified whether these differences result from missing data or from the removal of statistical outliers.

The Reviewer is correct that while 8 males were initially placed on their respective diets, for some of the analyses, the n-number is less than 8. In some instances, for example the analysis of total body fat (Fig. 1D), data was unfortunately not collected during an initial round of dissections. As such, the n number here is only 6 in each group. Additionally, due to the high cost associated with sequencing the microbiome for 5 groups, we decided to only sequence 6 samples per group. However, we do not feel that this impacts significantly on the overall focus of the data presented.

(4) Despite this, you may have been underpowered to detect differences in some parameters, for example, the placental stereology. Alternative approaches, such as immunostaining with whole-section quantification, may be more sensitive to detect subtle changes. Alternatively, have you considered using smaller grids for improved sensitivity of the stereological analysis?

We thank the Reviewer for their insight into the data and their suggestion for immunostaining. We agree with the Reviewers that a greater number of samples would have strengthened our analyses. However, we are not in the possession of further samples which have been processed in the correct manner for additional stereological analysis. We are hoping to conduct further placental analyses based on our RNA-Seq data, but this will require the generation of new samples.

(5) It would be easier to interpret the figures if it were clear which datasets were analysed using non-parametric tests. Were Figure 2F, 2G, 6A, 6E, and 6I are shown differently for that reason, perhaps? It would improve transparency if non-normally distributed data are shown as medians, as that's what's being compared in a non-parametric test.

We apologies for any confusion regarding the analysis of our data. The Reviewer is correct that the data in 2F and 2G were analysed using a non-parametric test. We have now made this clearer in the legend to the figure highlighting which data sets were analysed by ANOVA or Kruskal–Wallis test. We have also done this for the other figure legends where appropriate. With regard to Figure 6, the data presented in Panels A, E and I were intended to show the range of data extending above and below the 90th and 10th centiles of the CD fetuses. As such, we felt that violin plots were the most appropriate way to display these data.

(6) Supplemental Figure 1 seems to be missing.

We apologise sincerely for the lack of inclusion of Supplemental Figure 1. We will ensure that it is included in our resubmission

(7) Line 523 states that samples with RIN < 7 were used for microarray analysis. Do the authors mean RIN > 7?

We thank the Reviewer for identifying our mistake. The Reviewer is correct that this should have been a RIN >7. We have now corrected this.

(8) It is mentioned in lines 603-604 that paraffin shrinkage was accounted for. It could be useful to describe how this was done.

We have revised the text within the Materials and Methods to provide additional clarity on how we compensated for the shrinkage due to the paraffin processing.

In the revised Methods we have added a brief “Shrinkage correction” subsection describing how paraffin-embedding shrinkage was quantified for each placenta individually. Specifically, we now state that post-embedding placental volume was estimated using the Cavalieri Principle on systematic and uniformly-random sampled H&E sections, and a per-placenta volume shrinkage coefficient (k_V = V_post/V_pre) was calculated.

We have also added the equations showing how this coefficient was used to correct compartment volumes and the derived surface area estimates (surface area calculated from S_v and the corresponding shrinkage-corrected placenta volume). Please see lines 618-644.

(9) This may be due to the generation of the reviewer PDF, but Figure 4E and 4H are illegible in our version of the manuscript.

We apologies for the lower resolution with these figures and the difficulty in seeing the information presented. We have created revised versions of these figures which we hope are of higher quality and clarity.

(10) What do the stars represent in Figure 6A, E, I - compared to what, controls?

The Reviewer is correct that the asterisks in Figures 6A, E and I represent differences in the proportion of fetuses either above or below the 90th and 10th centile of the CD fetuses respectively. As such, in panel A, for both the LPD and MD-LPD groups, there are significantly more fetuses who are below the 10th centile of the CD group. Similarly, in panel E, there are significantly more placentas in the LPD group that have a weight above the 90th centile of the CD group. We have revised the graphs to make these differences, and their comparisons clearer.

Reviewer #2 (Recommendations for the authors):

Some Recommendations for improving the writing and presentation, and minor corrections to the text and figures:

(1) Please describe Wnt signaling in the Abstract.

The Abstract has been amended to provide some additional text regarding Wnt signalling. Please see lines 60-63.

(2) Page 6, line 134: A brief explanation of why measuring the inhibin beta-A chain should be included.

The text within this section has been amended to include a brief description of the role of Inhibin β-A chain on testicular function. Please see lines 135-139.

(3) The methodology used for Tnf determination is missing and should be described.

We apologies for the lack of detail regarding our analysis of serum Tnf in our males. This has now been included. Please see lines 479-480.

(4) It is important to mention that free fatty acid levels in the MD-WD group were similar to those in the CD group, although they remained comparable to the WD group.

We agree with the Reviewer and have amended the text to indicate that there was no difference in the FFA profile of the MD-WD males to either the CD or WD males. Please see lines 147-148.

(5) Figure 2 presents both metabolic parameters and bacterial profile analyses. Although the authors appear to relate these outcomes, clarity would be improved by presenting them in separate figures.

As requested, we have now presented these data as two separate Figures

(6) Figure 3H: The data suggest that the decrease in the number of spermatogonia (PLZF⁺) observed in the LPD and WD groups was prevented when the diets were supplemented with methyl donors.

(7) However, the description and interpretation of this result (or of a neutral effect) are missing.

We agree with the Reviewer in their interpretation of the PLZF+ data. We have indicated this in the text within the Results and Discussion sections. Please see lines 177-178 and lines.

(8) Line 284: Please check the abbreviation for MD-LPD.

We thank the Reviewer for identifying this typographical mistake. This has now been corrected to state MD-LPD and not MDL.

(9) Line 285: Please check the lettering in the text and in Figure 6H-K.

We thank the Reviewer for identifying this typographical mistake. This has now been corrected to state the panels are Figure 9H-K, as we have split the original Figure 2 into two figures.

Author response:

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

eLife Assessment

The study presents important insights into the regulation of muscle hypertrophy, regulated by Muscle Ankyrin Repeat Proteins (MARPs) and mTOR. The methods are overall solid and complementary, with only minor limitations. Overall, the findings will be of interest for both muscle-biology specialists and the broader mechanobiology community.

We thank the editors for their interest in our manuscript. Below we respond to the reviewer’s comments. Based on these comments we made extensive textual revisions throughout the manuscript, and we added additional analyses to the revised results.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors employ diaphragm denervation in rats and mice to study titin‑based mechanosensing and longitudinal muscle hypertrophy. By integrating bulk RNA‑seq, proteomics, and phosphoproteomics, they map the stretch‑responsive signalling landscape, uncovering robust induction of the muscle‑ankyrin‑repeat proteins (MARP1‑3) together with enhanced phosphorylation of titin's N2A element. Genetic ablation of MARPs in mice amplifies longitudinal fibre growth and is accompanied by activation of the mTOR pathway, whereas systemic rapamycin treatment suppresses the hypertrophic response, highlighting mTORC1 as a key downstream effector of titin/MARP signalling.

Strengths:

The authors address a clear biological question: "how titin‑associated factors translate mechanical stretch into longitudinal fibre growth" using a unique and clinically relevant animal model of diaphragm denervation. Using a comprehensive multiomics approach, the authors identify MARPs as potential mediators of these effects and use a genetic mouse model to provide compelling evidence supporting causality. Additionally, connecting these findings to rapamycin, a drug widely used clinically, further increases the relevance and potential impact of the study.

We thank the reviewer for their kind words and critical review of our manuscript. The roles of the MARP proteins are diverse and form an intriguing target for further study.

Weaknesses:

There are several areas where the manuscript could be substantially improved.

(1) The statistical analysis of multi-omics data needs clarification. Typically, analyses across multiple experimental groups require controlling the false discovery rate (FDR) simultaneously to avoid reporting false-positive findings. It would be very helpful if the authors could specify whether adjusted p-values were calculated using a multi-factorial statistical model (e.g., ~group) or through separate pairwise contrasts.

We agree with the reviewer that the description of the statistical analysis could be improved. We report the q-values in the supplemental data tables to correct for false positive data, the p-values reflect pairwise comparisons. Statistical testing was performed on whole proteomes or phospho-proteomes, making for very stringent testing (please also see reply to reviewer 2, response 5). Unbiased quantitative proteomics functions primarily as a screen, in-solution digestion of muscle proteins yields comparatively few peptides making population adjusted p-value calculation very stringent, suggesting no/few differences in expression. Hence, we compared RNAseq to proteome data to isolate consistently differential proteins. We have revised the method section (lines 745-746) to include clarifications of the FDR analysis.

(2) (A)There are three separate points regarding MARP3 that could be improved. First, the authors report that MARP3-KO mice exhibit smaller increases in muscle mass after diaphragm denervation compared to wild-type mice (a -13% difference), indicating MARP3 likely promotes rather than attenuates hypertrophy. However, the manuscript currently states the opposite (lines 215-216); this interpretation should be revisited. (B) Second, it would be valuable if the authors could provide data showing whether MARP3 transcript or protein levels change response to denervation - if they do not, discussing mechanisms behind the observed phenotype would help clarify the findings. (C) Finally, given that some MARP-KO mice already exhibit baseline differences, employing and reporting the full two-way ANOVA (including genotype × treatment interaction) would allow a direct statistical assessment of whether MARP deficiency modifies the muscle's response to stretch. This analysis would help clearly resolve any existing ambiguity.

(A) Compared to wildtype mice, MARP3 KO mice exhibit baseline diaphragm hypertrophy. This suggests that MARP3 may normally restrain hypertrophy under basal conditions. However, in response to UDD, MARP3 KO mice display an attenuated hypertrophic response, which could be interpreted as MARP3 promoting hypertrophy under stress conditions, as noted by the reviewer. The relationship between MARP3 and metabolism remains incompletely understood, but prior studies indicate that loss of MARP3 enhances glucose tolerance and insulin sensitivity (PMID: 12456686), suggesting that MARP3 may act as a negative regulator of metabolic signaling. Both glucose and insulin can activate the PI3K pathway to promote hypertrophy (PMID: 16679293), which may contribute to the baseline hypertrophy observed in MARP3 KO diaphragms. In addition, MARP3 deficiency has been associated with activation of AMPK signaling (PMID: 26398569). AMPK is a key regulator of metabolic pathways and a well-established inhibitor of hypertrophic signaling, in part through suppression of mTOR activity, and is also responsive to mechanical stimuli (PMID: 18556591). Thus, increased AMPK activity in MARP3 KO mice may limit hypertrophy in response to UDD. Supporting this, our phospho-proteomics data indicate increased activation of the AMPK β-subunit following UDD, suggesting a potential role for AMPK signaling in stretch-induced hypertrophy. Based on these considerations, we have removed the statement that MARP3 attenuates hypertrophy and instead incorporated the potential role of AMPK signaling into the Discussion (lines 354–355). While the present study focuses on the triple MARP KO model, future work will examine the specific contributions of individual MARP proteins to muscle hypertrophy.

(B) MARP3 (Ankrd23) upregulation at the RNA level was detected by RNA-seq in rat diaphragm following both UDD and BDD (Supplemental Tables 1 and 2). This is consistent with our prior findings in mice, where western blot analysis showed increased MARP3 protein expression following UDD (PMID: 29978560). We note that reliable detection of MARP3 protein remains technically challenging due to limited availability of specific antibodies.

(C) We agree with the reviewer and have added the results of the two-way ANOVA to the figures (see updated Figure 4). The three MARP proteins exhibit differential effects on diaphragm hypertrophy, supporting their role as modulators of stretch-induced hypertrophy.

(3) The current presentation of multi-omics data is somewhat difficult to follow, making it challenging to determine whether observed changes occur at the transcript or protein level due to inconsistent gene/protein naming and capitalization (e.g., proper forms are mTOR, p70 S6K, 4E-BP1). Clearly organizing and presenting transcript and protein-level changes side-by-side, especially for key molecules discussed in later experiments, would make the data more accessible and provide clearer insights into the biology of titin-mediated mechanosensing.

We agree with the reviewer that naming conventions between gene and protein can be hard to follow. We kept the names for titin-associated proteins as some have multiple protein names and the most common names is shown here. However, we made the suggested changes for the mTOR related proteins (for example, see figure 5).

(4) The current analysis relies on total protein measurements downstream of mTOR, yet mTOR's primary mode of action is to change phosphorylation status. Because the authors have already generated a phosphoproteomic dataset, it would be very helpful to report - or at least comment on - whether known mTOR target phosphosites were detected and how they respond to denervation and rapamycin. Including even a brief summary of canonical sites such as S6K1 Thr389 or 4E - BP1 Thr37/46 would make the link between mTOR activity and hypertrophy much clearer.

We agree with the reviewer that the mTOR data requires more work to ascertain its function in regulating hypertrophy following UDD. We investigated S6K1 Thr389 or 4E BP1 Thr37/46 in both the phosphoproteomic dataset and by western blot. These sites do not appear in phosphoproteome mass spectrometry (supplemental data table 13) and 4E BP1 Thr37/46 was unchanged by western blot (not shown). The S6K1 Thr389 antibody was aspecific in our hands, but Norrby et al (PMID: 22657251) saw increased levels by 6-days UDD. Hence the mTOR aspect of this study is quite complex, suggesting mTOR plays a major role in UDD hypertrophy, but potentially through an alternative activation pathway from what is classically described for muscle hypertrophy. We are investigating the mTOR mechanism further focusing on mTOR’s role in regulating longitudinal hypertrophy with potential connection to titin signaling and hope to publish this in the next few years. We revised the discussion to include canonical mTOR activation in hypertrophy, please see lines 388-392.

(5) Finally, since rapamycin blocks only a subset of mTOR signalling, a brief discussion that distinguishes rapamycin‑sensitive from rapamycin‑insensitive pathways would be valuable. Clarifying whether diaphragm stretch relies exclusively on the sensitive branch or also engages the resistant branch would place the results in a broader mTOR context and deepen the mechanistic narrative.

We agree with the reviewer that distinguishing between rapamycin-sensitive and -insensitive mTOR signaling adds useful context to the interpretation of stretch-induced hypertrophy. Rapamycin primarily inhibits mTORC1, whereas mTORC2 is generally considered rapamycin-insensitive, although prolonged or high-dose exposure can also affect mTORC2 activity. Our data indicate that UDD induces a form of hypertrophy that is sensitive to rapamycin, supporting a prominent role for mTORC1 in this process. However, we cannot exclude the possibility that rapamycin-insensitive pathways, including mTORC2 signaling, also contribute. Notably, denervation itself may influence mTORC2 activity, which could complicate the distinction between stretch- and denervation-mediated signaling. Given these considerations, we have added a brief discussion to acknowledge potential contributions of rapamycin-insensitive mTOR signaling (lines 379-384). A more comprehensive dissection of mTORC1 versus mTORC2 signaling in this context will require targeted approaches and falls beyond the scope of the present study.

Reviewer #1 (Recommendations for the authors):

Minor comments:

(6) The manuscript notes that KEGG analysis "confirmed" the GO‑term findings. Because KEGG pathways and GO terms describe different types of biological information, it might be clearer simply to present them as complementary lines of evidence rather than one validating the other.

We agree and modified the text accordingly. “Concurrently, KEGG PATHWAY database searches (Supplemental data Table 6) indicated that the DEG’s are involved in muscle remodeling.” See lines 166-169.

(7) Figure 2's legend mentions a two‑way ANOVA, but the specific factors tested are not specified. Listing those two factors would help readers interpret the statistics more easily.

The two-way ANOVA refers to the violin plot in figure 2E and tests the difference of the 2 surgical modalities sham vs UDD and sham vs BDD. Sham groups were combined in the graphs for easy comparison. We clarified the text of figure legend 2.

(8) The Methods briefly describe phosphopeptide enrichment, but additional details on the criteria for site identification - such as the localisation algorithm, probability cut‑off, and FDR thresholds - would make the phosphoproteomics section more transparent and reproducible.

Please see the updated method section, lines 756-765

Reviewer #2 (Public review):

Summary:

Muscle hypertrophy is a major regulator of human health and performance. Here, van der Pilj and colleagues assess the role of the giant elastic protein, titin, in regulating the longitudinal hypertrophy of diaphragm muscles following denervation. Interestingly, the authors find an early hypertrophic response, with 30% new serial sarcomeres added within 6 days, followed by subsequent muscle atrophy. Using RBM20 mutant mice, which express a more compliant titin, the authors discovered that this longitudinal hypertrophy is mediated via titin mechanosensing. Through an omics approach, it is suggested that the Muscle ankyrin proteins may regulate this approach. Genetic ablation of MARPs 1-3 blocks the hypertrophic response, although single knockouts are more variable, suggesting extensive complementation between these titin binding proteins. Finally, it is found through the administration of rapamycin that the mTOR signalling pathway plays a role in longitudinal hypertrophic growth.

Strengths:

This paper is well written and uses an impressive suite of genetic mouse models to address this interesting question of what drives longitudinal muscle growth.

We appreciate the reviewer’s kind words on our manuscript and their critical review of our work. A potential separate mechanism governing cross-sectional versus longitudinal hypertrophy is of great interest and something we aim to address in future manuscripts.

Weaknesses:

While the findings are of interest, they lack sufficient mechanistic detail in the current state to separate cross-sectional versus longitudinal hypertrophy. The authors have excellent tools such as the RBM20 model to functionally dissect mTOR signalling to these processes. It is also unclear if this process is unique to the diaphragm or is conserved across other muscle groups during eccentric contractions.

Reviewer #2 (Recommendations for the authors):

(1) Cross-sectional hypertrophy characterization: The paper emphasizes longitudinal hypertrophy but does not quantify the contribution of radial (cross-sectional) hypertrophy to the total mass increase. Given that the denervated costal diaphragm shows ~50% increase in mass (Figure 1B) but there is only ~30% fiber lengthening, it is important to determine the proportion attributable to fiber diameter changes. Histological analysis of muscle fiber cross-sectional area would clarify the relative contributions of longitudinal versus radial hypertrophy to the overall mass phenotype.

We agree with the reviewer that radial hypertrophy is an important mechanism for muscle weight gain in UDD. In previous work we characterized both the radial and longitudinal hypertrophy response in 6-day UDD and found that ~20% of the mass gain seen in UDD is radial hypertrophy (PMID: 29978560). We reference this paper in the discussion section, line 277-278. Doing a full histological work-up of UDD diaphragm would be interesting but falls outside the scope of this manuscript. Our focus was to characterize longitudinal hypertrophy by addition of sarcomeres in series and provide insight into titin’s role in regulating longitudinal hypertrophy. We hope that the reviewer agrees with this approach.

(2) Titin isoform expression analysis: At line 103, the authors propose that longitudinal hypertrophy reduces strain on titin by decreasing fractional sarcomere extension. However, this hypothesis does not exclude the possibility of isoform switching to a less elastic titin variant, which may compensate for changes in mechanical stress. The RNA-sequencing data should be analyzed for titin exon usage patterns between sham and UDD to determine whether changes in isoform composition (e.g., PEVK region splicing) accompany longitudinal hypertrophy. If isoform switching occurs, this represents an alternative or complementary mechanism to sarcomere addition.

We analyzed titin exon usage in rat following both UDD and BDD. Increases in sarcomeres in series associated with UDD show modest changes in titin exon usage, though not significant by population adjusted p-values. The denervation effect of BDD did show changes in splicing, indicating lower inclusion of PEVK encoding exons, suggesting a stiffening of the titin molecules. Stiffening of titin molecules might be protective for the fully paralyzed diaphragm and preserve muscle mass. This would align with our prior publication (PMID: 29978560) which showed that stiffer titin generated more radial hypertrophy in response to UDD. In response to the reviewer’s comment, we added the splicing data to the supplemental data as new figure 2 and briefly address titin splicing in the results section, see lines 121-125.

(3) The comparison of 3-day unilateral diaphragm denervation (UDD) and bilateral diaphragm denervation (BDD) in rats (Figure 1D-E) is used to argue that hypertrophic signaling is stretch-dependent rather than denervation-dependent. However, this interpretation requires clarification. In mice, hypertrophy is detectable as early as 1 day post-UDD, whereas the 3-day BDD protocol may drive an accelerated hypertrophic-to-atrophic remodelling process given the severity of the model. Moreover, longitudinal and global muscle hypertrophy may operate through distinct mechanisms: denervation could suppress longitudinal hypertrophy through a separate pathway while promoting or delaying cross-sectional hypertrophy. The authors should acknowledge that the current evidence does not fully exclude denervation-dependent mechanisms and should consider extended BDD time points or additional mechanistic studies to clarify this distinction.

UDD and BDD are both denervation models and hypertrophy occurs in the denervated costal of UDD operated animals. Stretch is thus the mechanical difference between UDD and BDD and thus the trigger for hypertrophy signaling. At the denervation signaling level both models should in principle be comparable and are unlikely to play different roles between UDD and BDD, except that UDD also induces a more potent hypertrophy signaling profile on top of the atrophy program. That said, BDD is a more severe model and respiration rate is depressed compared to UDD where respiration rate is elevated. BDD rats also engage in abdominal breathing, which mildly stretches the diaphragm. Hypoxia is likely to play a stronger role in BDD than UDD and could thus further enhance the atrophy profile of BDD. We agree with the reviewer that more work is needed to elucidate the BDD remodeling response, however UDD induced stretch is the main driver of longitudinal hypertrophy. In response to the reviewer’s comment, we have added clarifying text to the discussion, lines 286-292.

The potential for there being two independent mechanisms for both radial and longitudinal hypertrophy is of great interest to us. We foresee that dissecting out these differences will require a cell culture-based approach and will aid in avoiding the complexity of overlapping denervation and hypertrophy signals as seen in this manuscript.

(4) Characterization of RBM20 models: The RBM20 experiments rely on the assumption that increased titin compliance reduces stretch sensitivity. However, the paper provides minimal baseline characterization of the diaphragms. Specifically: (a) What are the sarcomere lengths in RBM20-deficient diaphragms at rest and under stretch? (b) How does the passive force-length relationship differ between wildtype and RBM20-deficient diaphragm muscles? and (c) Would RBM20-deficient muscles, despite having longer sarcomeres at baseline, actually experience sufficient strain to activate mechanosensing? These data are necessary to interpret why RBM20-deficient mice show attenuated mass gain rather than none (as in BDD) during UDD (Supplemental Figure 2A-C). Additionally, what would the authors hypothesize would happen if rapamycin were used in RMB20 UDD models? It appears to be an attractive experimental approach to separate potential mTOR contributions to longitudinal versus cross-sectional hypertrophy.

We agree with the reviewer that more work is needed on Rbm20 deficient mice and rats to elucidate their response to stretch. Part of this characterization has previously been published (PMID: 29978560) and Rbm20 splice-deficient mice have reduced passive stiffness in the diaphragm and show a robust mechanosensing response to UDD. Rbm20 splice-deficient mice also show a similar increase in longitudinal hypertrophy, but a blunted radial hypertrophy in response to 6-days UDD. The main reason for not expanding on these mice/rats further was the added complexity of Rbm20 splicing multiple targets that could affect hypertrophy signaling, for example LDB3 (ZASP) and FLNC (Filamin C) are both associated with hypertrophic cardiomyopathy. Hence for the purpose of this manuscript we showed mice and rats having a similar response to UDD, hypertrophy wise, and that titin stiffness (reduced in Rbm20-deficient animals) affects hypertrophy at the diaphragm mass level.

Testing rapamycin on Rbm20-deficient animals could be interesting, however the complexities of also changing splicing of non-titin targets will make interpretation of mTOR signaling difficult. Perhaps an alternative approach would be to generate a titin mouse model with more compliant titin (e.g. increase the size of the PEVK segment), a model we are considering for future studies. TtnΔ112-158 mice, deleting a large portion of the PEVK region (PMID: 30565562) show increases in sarcomere number. We would expect a model with more PEVK to thus show a reduction in the number of sarcomeres in series. We discuss the role of titin stiffness in the discussion and how titin stiffness ties to longitudinal hypertrophy, please see lines 302-314.

(5) Statistical analysis and multiple hypothesis correction: The proteomic analyses appear to employ a nominal p-value threshold (p < 0.05) without correction for multiple comparisons or false discovery rate (FDR) control. This is particularly concerning given the large number of comparisons. For example, the authors report 142 titin phosphorylation sites significantly different between sham and UDD at p < 0.05 (approximately 20% of ~700 identified sites). However, with proper FDR correction (adjusted p < 0.05), only 14 sites remain significant - a 90% reduction. This discrepancy is critical for the discussion on titin N2A phosphorylation sites pS9459 and pS9520, where only pS9520 achieves statistical significance after FDR adjustment. The authors should justify their choice of statistical thresholds and reanalyze key findings using FDR-corrected p-values. Additionally, the phosphoproteomics dataset should be screened for duplicate phosphosite identifications to ensure each site is counted only once.

Reviewer 1 has voiced similar concerns, and we have thus expanded the methodology to explain the statistical tests used to analyze the data and the process of establishing Z-scores of isobaric peptides for the same phospho-sites (see lines 756-765). Our statistical analysis covers all detected peptides, when we only analyze the titin peptides: pS9459 is only significant in t-test, likely due to large variation in isobaric peptides. pS9520 is significant in both independent t-test and FDR. We changed figure 3D to show the fold change instead of the previous Z-score for more intuitive interpretation.

Minor comments:

(6) Line 52: "thesarcomeres" should read "the sarcomeres".

A space has been added, please see line 52.

(7) Line 52: "half-sarcomer" should read "half-sarcomere"

Spelling has been corrected, please see line 52.

(8) Figure clarity: Figure 1 (B-C) presents mouse data, while Figure 1 (D-E) presents rat data. This distinction should be clearly labeled in the figure legend or on the axes to prevent misinterpretation, particularly for readers unfamiliar with the experimental design.

We added the species to the y-axis of revised figure 1B-E and added additional clarification in the figure legend.

(9) Supplementary tables: When reporting statistical comparisons in the supplementary tables, please consider including the directionality of the statistical tests (e.g., which group was higher or lower) alongside p-values. This will facilitate interpretation without requiring reference to the main text figures.

We agree with the reviewer and added statistical direction as a new column next to the p-values, please see the revised supplemental tables.

(10) Given the interesting divergent findings in MARPtKO versus single knockouts, it would be interesting to assess by immunofluorescence the association of each MARP with the N2A region of titin following UDD.

We agree with the reviewer that localization is important. Miller et al (PMID: 14583192) previously localized MARP1-3 to the N2A segment by immuno-EM and our work previously localized MARP1 to N2A using SR-SIM (PMID: 29978560). We will further investigate MARPs binding to the N2A region in an upcoming study that we intend to publish soon.

Author response:

Reviewer #1 (Public review):

Weaknesses:

This is a challenging hypothesis that would require some additional experimental controls. The pathway dissection, while extensive, is sometimes approached in unconvincing ways, and the results are not always evident to judge or interpret. Technically, the western blots and transcriptomic analyses require notable improvements.

We would like to thank the reviewer for the careful and patient examination of the issues identified in our manuscript. The poor quality of some of the Western blot bands in Figure 4 may have been caused by inappropriate electrophoresis conditions during the Western blot experiments. In the revised manuscript, we will optimize the electrophoresis conditions to obtain higher-quality protein bands and update the quantitative data. Regarding the quantification format, we believe that heatmaps provide a more intuitive representation of trends in protein expression across different treatment groups. This approach more accurately reflects the results of our biological replicates than simply analyzing the significance of differences in the grayscale values of protein bands. For the analysis of transcriptomic data, we will conduct a more detailed analysis of signal pathway enrichment and the identified differentially expressed genes to ensure that predicted genes are excluded from our current results and redundant data presentation is removed.

Regarding additional experimental controls, such as incorporating experimental data under blue light treatment conditions as a control for red light. While exploring the optimal red light irradiation dose at the cellular level, we simultaneously conducted experiments on the effects of blue light irradiation at the same dose on keratinocyte activity. The results indicated that as the blue light irradiation dose increased (0–160 J/cm²), the keratinocyte activity exhibited a dose-dependent decline. This indicates that blue light is phototoxic to keratinocytes. The relevant experimental results have already been published in our previous study (Communications Biology 2024, doi: 10.1038/s42003-024-06973-1). Taken together with the data from our study, this demonstrates that the anti-aging effects of red light reported in the current manuscript are indeed driven by red light.

Reviewer #2 (Public review):

Weaknesses:

The paper does not evolve to use the mechanistic discoveries of the manuscript to help our community to identify the mechanism of photobiomodulation, which is not known so far.

I would like to draw attention to a recently published paper by Herrera et al. (FEBS Letters 2025, doi:10.1002/1873-3468.70195), which shows that red light (660 nm) stimulates mitochondrial fatty acid oxidation in keratinocytes via AMPK‑dependent phosphorylation of ACC, without altering expression of electron transport chain complexes. I believe this paper is highly complementary to the current study.

Herrera et al. demonstrate that red light increases basal, ATP-linked, and maximal oxygen consumption rates in keratinocytes specifically through enhanced fatty acid oxidation (inhibited by etomoxir). This independently validates the central finding of the current manuscript, i.e., red light boosts lipid metabolism, strengthening the robustness of this concept.

While the current manuscript focuses on the SIRT4-MCD axis, Herrera et al. identify AMPK phosphorylation and ACC inhibition as key effectors. The authors can integrate and expand their discussion, since SIRT4 downregulation may converge on AMPK activation, or they may represent parallel, reinforcing mechanisms. This would enrich the mechanistic model and open new hypotheses.

The mechanism of photobiomodulation: Herrera et al. explicitly challenge the prevailing paradigm that red light acts solely via cytochrome c oxidase (by showing long-lasting effects, unchanged OXPHOS protein levels, and no difference in permeabilised cells). The current finding (red light acts through SIRT4 downregulation, i.e., not direct enzymatic activation) aligns perfectly with Herrera´s critique.

Long-term metabolic effects-Herrera et al. show that a single red light exposure elevates oxygen consumption for up to 2 days. The current study focuses on changes at 12-24 h. Their data extend the time window and suggest that the metabolic reprogramming you describe may persist longer than currently discussed, which is clinically relevant.

Discussing Herrera et al.'s results would not only acknowledge independent, corroborating evidence but would also allow the authors to position their SIRT4-centric mechanism within a broader, emerging understanding of red-light photobiomodulation.

We would like to thank the reviewer for providing us with constructive suggestions for discussion. Our results showed that under red light conditions, both glycolipid and lipid metabolism were activated in keratinocytes, and cellular metabolic flux increased. The activation of lipid metabolism directly led to an increase in metabolism-associated H3K9ac and drove the upregulation of anti-aging-related genes; we believe this is key to the anti-aging effects of red light. Mechanistic analysis combining proteomics and acetylation proteomics revealed that red light significantly downregulated SIRT4 expression and increased the acetylation of MCD, a protein regulated by SIRT4 that governs cellular fatty acid oxidation rates. Through validation using cell-level knockdown and inhibitors, we confirmed that SIRT4 inhibition exerts anti-aging effects in vitro and that inhibiting MCD function under red light conditions suppresses H3K9ac. These results establish the role of the SIRT4-MCD signalling axis in mediating the anti-aging effects of red light.

The study by Herrera et al. included a substantial body of validation data confirming the role of red light in promoting fatty acid oxidation, providing robust empirical support for our research. Furthermore, Herrera et al. revealed that red light-induced fatty acid oxidation depends on AMPK and ACC phosphorylation. This mechanism of red-light photobiomodulation may refute the notion that its bio-regulatory effects rely solely on the action of mitochondrial cytochrome c oxidase. Furthermore, together with our study revealing that red light exerts anti-aging photobiomodulatory effects via the SIRT4-MCD signalling axis, these findings independently confirm that red light regulates cellular fatty acid oxidation, thereby demonstrating the pivotal role of activated fatty acid oxidation in the bio-regulatory effects of red light. In the revised manuscript, we will include a discussion on the potential link between the red light-driven downregulation of SIRT4 and the phosphorylation of AMPK/ACC. This will be of positive value in elucidating how SIRT4 exerts its anti-aging effects by regulating lipid metabolism, as well as in explaining the possible mechanisms by which red light downregulates SIRT4.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript has several strengths, including a technically comprehensive approach that combines mouse genetics, electrophysiology, live imaging in assembloids, and human organoid models, providing a rich and multifaceted dataset. Cross-species validation through the parallel use of mouse and human systems strengthens the generality of the observed phenotypes and increases relevance to human neurodevelopment.

Consistent phenotypic observations across systems show that ARHGEF6 loss affects migration, neurite morphology, growth cone structure, and neuronal survival, supporting a coherent role in cytoskeletal regulation.

There is clear evidence for developmental defects, including reduced interneuron numbers, increased apoptosis in the ganglionic eminences, and migration deficits, all well supported by quantitative analyses. Also, there is a high-quality electrophysiological characterization that demonstrates reduced firing in interneurons, providing a well-controlled functional phenotype.

Strengths:

The manuscript has several strengths, including a technically comprehensive approach that combines mouse genetics, electrophysiology, live imaging in assembloids, and human organoid models, providing a rich and multifaceted dataset. Cross-species validation through the parallel use of mouse and human systems strengthens the generality of the observed phenotypes and increases relevance to human neurodevelopment.

Consistent phenotypic observations across systems show that ARHGEF6 loss affects migration, neurite morphology, growth cone structure, and neuronal survival, supporting a coherent role in cytoskeletal regulation.

There is clear evidence for developmental defects, including reduced interneuron numbers, increased apoptosis in the ganglionic eminences, and migration deficits, all well supported by quantitative analyses. Also, there is a high-quality electrophysiological characterization that demonstrates reduced firing in interneurons, providing a well-controlled functional phenotype.

We thank the reviewer for their positive and thoughtful assessment of our manuscript. We appreciate their recognition of the technical breadth of the study, including the integration of mouse genetics, electrophysiology, live imaging in assembloids, and human organoid models. We are also grateful that the reviewer highlights the value of our cross-species approach, as a major goal of the study was to determine whether ARHGEF6 loss produces convergent developmental and cellular phenotypes in both mouse and human systems.

Weaknesses:

Despite the strengths mentioned above, the study has some conceptual and experimental weaknesses that reduce its impact. The mechanistic insight is limited, as the research does not directly establish how ARHGEF6 regulates downstream signaling pathways.

We appreciate the reviewer’s constructive comment. We agree that, although our data establish a phenotypic link between ARHGEF6 loss and interneuron development, they do not directly dissect the molecular mechanisms underlying the observed defects. Our interpretation that the mutant phenotype involves dysregulation of cytoskeletal dynamics is based on the directly observed defects in actin polymerization and organization in neural progenitor cells and neuronal growth cones respectively, and is consistent with the abnormalities observed in neurite morphology and neuronal migration. This interpretation is further supported by the established role of Arhgef6 as a regulator of the small Rho GTPases Rac1 and Cdc42. Previous evidence shows that Arhgef6 loss reduces the activity of both GTPases and deregulates the expression of the cytoskeletal regulators Pak1–3, Limk1, and Cofilin in the mouse brain (Ramakers et al., 2012). Moreover, spine abnormalities in Arhgef6-knockdown ex vivo slice cultures can be rescued by expressing the active form of Pak3, a downstream effector of Rac1 and Cdc42 (Node-Langlois et al., 2006). Together, these findings support a model in which the loss of the protein affects development through cytoskeletal dysregulation, likely involving altered Rho GTPase signalling. We nevertheless agree that further experiments would be required to establish a direct causal relationship between ARHGEF6 loss, Rho GTPase activity, cytoskeletal dysregulation, and the interneuron phenotypes described here. We will therefore revise the manuscript to clarify that this mechanistic link remains an interpretation supported by our data and the literature, rather than a direct demonstration within the present study.

Also, there is insufficient evidence for interneuron specificity; although the central claim is that ARHGEF6 plays a selective role in interneurons, the data do not adequately exclude the possibility that the observed effects reflect broader neuronal defects. The study lacks critical controls across cell types, as several phenotypes observed in organoids and progenitors, including apoptosis, reduced neuronal output, and altered morphology, could also affect multiple neuronal populations without being directly tested.

We agree that the current data do not exclude the possibility of alterations in other neuronal lineages, specifically the excitatory lineage. With regard to this, we would like to emphasize that the investigation of excitatory cell phenotypes was beyond the scope of the present study, as this aspect has previously been examined by Ramakers et al., 2012 and Node-Langlois et al., 2006, particularly in the context of hippocampal pyramidal cells, which are among the few cell types showing consistent expression of the gene in the adult mouse brain (Allen Brain Atlas; Yao et al., 2021). In this context, it is interesting to note that, in Ramakers et al., 2012 (Figure S1), MAP2 immunostaining of hippocampal formations revealed comparable distribution and intensity of neuronal cell bodies and dendrites throughout the hippocampus of both wild-type and Arhgef6-KO animals. With regard to morphological maturation of excitatory cells, whereas we observe a simplification of interneuron morphology in both mouse and human models, Ramakers et al., 2012 reported increased dendritic arborization complexity in hippocampal pyramidal cells. With regard to migration, a direct comparison with excitatory neurons would be intrinsically difficult, as excitatory and inhibitory neurons undergo highly distinct migratory processes and are therefore not directly comparable. We greatly appreciate the reviewer’s comment, as it gives us the opportunity to better discuss the relationship between our findings and previous studies in the Discussion. We will revise the manuscript and avoid implying that the phenotype observed is exclusive to interneurons.

Furthermore, the data are predominantly descriptive, with many results remaining correlative and failing to establish causal relationships.

We agree that our study primarily establishes a phenotypic framework and does not fully resolve the causal hierarchy among altered survival, migration, cytoskeletal morphology, and intrinsic excitability. We will revise the manuscript to make this limitation explicit, avoiding statements that imply direct causality beyond the data presented.

Some more comments:

(1) Given that ARHGEF6 is a guanine nucleotide exchange factor for Rac1 and Cdc42, the absence of direct measurements of GTPase activity or downstream signaling represents a significant gap. The interpretation that the observed phenotypes are mediated through specific cytoskeletal pathways, therefore, remains inferential.

We appreciate the comment. The interpretation that our phenotype involves dysregulated cytoskeletal dynamics is based on the observed defects in actin polymerization and F-actin organization in neuronal growth cones and is consistent with the abnormalities in neurite morphology and neuronal migration. We will explicitly state in the Discussion that, since we did not directly measure Rac1 and Cdc42 activity levels in our models, our hypothesis regarding the involvement of this molecular pathway in the establishment of the observed phenotype therefore remains inferential, despite being supported by the current literature.

(2) The manuscript repeatedly interprets the findings as interneuron-specific. However, several key observations are not demonstrated to be restricted to IN. Without direct comparison to excitatory neurons or other cell types, it is difficult to conclude that ARHGEF6 plays a selective role in interneurons rather than a more general role in neuronal development. The well-done analysis of the transcriptomic dataset is not sufficient to claim IN specificity. This issue is particularly important for the interpretation of the human organoid experiments, where reductions in SOX2⁺ progenitors and NEUN⁺ neurons, as well as increased apoptosis, could reflect global developmental defects. Similarly, in the mouse experiments, the reduction in GAD67⁺ cells is compelling, but it is not shown whether other neuronal populations are also affected.

As previously mentioned, we understand the reviewer’s concern regarding the specificity of the observed phenotypes in interneurons and agree that the claims should be tempered. However, it is important to note that the interpretation of the human organoid experiments should be reconsidered. The use of specifically ventralized MGE-like organoids allowed us to assess the cell-autonomous nature of defects such as the reduction in inhibitory progenitors’ neuronal output, the increased apoptosis, and the morphological abnormalities of inhibitory neurons. We will acknowledge in the Discussion the limitations of the study with regard to assessing the cell-autonomous nature of the observed migration defects.

(3) The study provides a strong phenotypic description but limited causal resolution. For example, migration defects, altered growth cone morphology, and reduced branching are all consistent with impaired cytoskeletal regulation, but the links between these phenotypes are not directly established. Likewise, while the electrophysiological data convincingly show reduced firing in interneurons, the connection between altered cytoskeletal dynamics and intrinsic excitability is not explored.

The observed migration defects, altered growth-cone morphology, and reduced branching are consistent with impaired cytoskeletal regulation. However, we acknowledge that the mechanistic links among these phenotypes remain to be directly demonstrated. Similarly, although our electrophysiological data show reduced firing in ARHGEF6-KO interneurons, the present study does not provide direct evidence linking impaired excitability to altered cytoskeletal dynamics. In the latter case, we think that the underlying mechanisms should be further investigated at the subcellular level, particularly with respect to cytoskeleton-mediated intracellular trafficking and localization and distribution of ion channels. One limitation of the present study, which may have masked electrophysiological alterations associated with differences in membrane composition (current Figure S1D–H), is that different interneuron subtypes with distinct intrinsic properties were pooled together in the analysis. We will expand the Discussion to address these limitations.

(4) Several aspects of data presentation could be improved. In multiple figures (e.g., Figure 1A, D; Figure 4 and Video S1, 2), the images are difficult to interpret due to high cellular density, limited magnification, or lack of clear annotation. In some cases, it is not fully clear how quantifications were performed or which regions were analyzed. Improving the visual clarity with arrows, boxes, and high-magnification inserts of the data would strengthen confidence in the conclusions.

We would like to thank the reviewer for pointing this out. We agree that some images and videos would benefit from clearer annotation. In the revised manuscript, we will add high-magnification insets, arrows or boxes highlighting the relevant regions/cells, and clearer descriptions of the quantified regions. We will also improve legends and video labels to indicate genotype, region, and tracked cells.

Reviewer #2 (Public review):

The authors investigate the impact of the deletion of the small GTPase regulator ARHGEF6 on the development and physiology of interneurons. Using public databases, they first show that ARHGEF6 is enriched in interneurons or in areas that give rise to them, both in development and adulthood, in humans and mice. Using a complete KO mouse previously reported, and using a GAD67-GFP reporter mice line, they show that in the adult mouse cortex and hippocampus, there is a notorious reduction GFP+ cells. These mice show increased apoptotic cells at different timepoints and areas of the brain during development. In the developing cortex of ARHGEF6-KO mice, there are fewer IN in all layers of the developing cortex, and cells present processes not correctly oriented. IN from the hippocampus in culture show reduced excitability and impaired neurite branching. The authors then established isogenic hiPSCs lines to study ARHGEF6 deletion in human cells and differentiated ventral forebrain neurons, to find interneuron-related and non-related phenotypes. Most importantly, human interneurons grown in organoids show reduced branching and altered growth cone morphology. The authors claim that the novel interneuron phenotypes found in these models can explain, in part, the human intellectual disabilities associated with mutations in this protein. The study is well conducted and opens new avenues of research not only for the role of small GTPases regulation in early nervous system development, but also for how interneuron deficiencies impact a wider range of intellectual disability syndromes found in humans.

We appreciate the reviewer’s positive evaluation of our manuscript and their recognition of this work’s potential to expand the focus of intellectual disability research on the development and function of the inhibitory system. We are particularly encouraged that the reviewer highlights the strength of our combined mouse and human cellular models, as well as the relevance of the interneuron-related phenotypes we identify across systems.

However, most conclusions of the present version would be strengthened after considering the following comments:

Major comments:

(1) The reported biological processes evaluated at different developmental stages may be directly or indirectly related to ARHGEF6 function itself. As a model of a hereditary disease, full organism gene deletion is valid, since the human patients suffer from that condition as well. However, to investigate the roles of a protein, complete deletions may not be very accurate since they can give rise to phenotypes that are only indirectly related to the protein function itself. Most conclusions of the present manuscript should either be discussed in this regard or add evidence for a direct role of the protein. One such evidence is typically performed with acute knockdowns in culture, or in developing brains by in utero electroporation. For example, Figure 1C shows that the principal excitatory neurons in the hippocampus do not express ARHGEF6. However, most electrophysiological and behavioral evidence of defects in ARHGEF6-KO mice arises from evaluating these cells (Ramakers et al., 2012). I am not suggesting that either previous or actual evidence is wrong. But I believe readers would benefit from a clear distinction (or add caution notes) between a functional consequence of the deletion (that can be months away and in other cells than the actual molecular defect) and a true cell biological function of the protein under study. In favor of the authors, this is a concern with most conclusions derived from KO organisms.

We agree with the reviewer that phenotypes observed in constitutive knockout models may, in some contexts, reflect indirect or compensatory consequences of long-term gene loss. Conditional and/or inducible knockout or knockdown approaches can certainly help dissect the nature of the observed defects and better define the effects of gene ablation at different developmental stages or in specific cell types. However, in the context of our study, it is important to note that the experiments performed in ventralized MGE-like organoids allowed us to assess the cell-autonomous nature of very early developmental defects in the inhibitory lineage, in isolation from other cell types. These defects include reduced neuronal output from inhibitory progenitors, increased apoptosis, and morphological abnormalities in inhibitory neurons. Therefore, the phenotypes reported here are less likely to reflect effects originating in, or indirectly caused by, cell types that do not express Arhgef6.

With regard to Figure 1C, we state in the Results that “among excitatory populations, only CA3 pyramidal neurons and mossy cells exhibited expression levels comparable to those observed in inhibitory clusters (Figure 1D, Table S2),” thereby not neglecting the potential effect of the lack of a functional protein in these populations.

(2) Figure 1E-G H I. All conclusions are made with a GAD67-GFP reporter, which is a very powerful and reliable tool for large-scale screening. All the conclusions of the paper would be strengthened if some immunohistochemical staining in the same areas of specific markers for interneurons would be added as supporting complementary evidence.

We appreciate the insightful comment of the reviewer. Additional validation using established interneuronal markers will further strengthen the GAD67-eGFP analysis. We will perform complementary stainings (e.g., PVALB and CCK) and quantifications and include these data as a Supplementary Figure.

(3) Cell death in development: It is surprising that the high amount of TUNEL staining during development does not translate into gross histological changes in the adult brain (studied elsewhere). Can authors discuss possible explanations?

We appreciate the thoughtful consideration of our findings. We think that possible explanations include partial compensatory mechanisms during development, which may mitigate the long-term anatomical consequences of increased cell death. In addition, the phenotype may be restricted to specific neuronal populations or developmental windows, thereby producing functional alterations without necessarily resulting in overt macroanatomical defects. Thus, although increased developmental cell death may contribute to altered circuit assembly and neuronal output, it may not be sufficient to produce gross histological changes detectable at the adult brain level.

(4) Section 4 (Figures 2F-J) - The authors present this staining as an analysis of migration. Normally, migration studies are performed with a "pulse-chase" paradigm, where a single cohort is labeled and then followed over time (normally by in utero electroporation of a fluorescent protein). Tissue is then fixed at different time points, and migration can be followed. On the contrary, the evidence is from a single point, in an experimental setting in which all Gad67 IN are stained, and hence, one cannot imply a defect in migration. The differences between WT and ARHGEF6-KO are obvious and interesting; it is just that they cannot be solely attributed to a problem in migration.

Also, a true phenotype of migration in the current setting should have found that the cells that failed to migrate are accumulated in deeper layers. My impression is that the changes in IN per layer are easier explained by total cell number, rather than migration. Perhaps evaluating earlier timepoints could clarify this.

We appreciate the reviewer’s suggestion to implement an additional time point in the in vivo migration analysis. Since an earlier in vivo time point would most likely not reveal migration-related defects, as most cells would still be confined to the ganglionic eminence (Liaci et al., 2022), we will include analyses performed at a later developmental time point as supplementary evidence. We will also revise the wording to clarify that the fixed-tissue data show altered distribution and orientation of GAD67-eGFP-positive interneurons, which are consistent with impaired migratory behavior when considered together with the in vitro live-imaging data. At the same time, we will acknowledge that reduced interneuron survival and/or neuronal output may also contribute to the observed phenotype.

(5) It is known that ARHGEF6 deletion produces severe F-actin phenotypes in neurons. Have the authors confirmed in their hippocampal cultures GAD67 cells ALSO have these phenotypes? Stress fibers in somas, growth cones, and actin patches along neurites.

We did not directly assess F-actin organization in GAD67-eGFP murine primary cultures. Direct analyses of F-actin organization, growth-cone morphology, and cytoskeletal organization were performed only in the human system. To further assess this phenotype, we will perform phalloidin staining on GAD67-eGFP brain sections to evaluate F-actin organization in interneurons in vivo.

(6) Section 4. The authors present data for deficient migration of the GFP-labeled interneurons. Is it possible to assess, in the same sections, whether other cell types are also affected? Although the hypothesis that ARHGEF6 deletion will have an impact in IN is well rooted in expression data, by assessing other cell types, one can even include a positive control or evidence for a cell-autonomous phenotype.

We thank the reviewer for their thoughtful suggestions. We agree that extending the analysis to additional cell types would provide further insight into the specificity of the phenotype; however, a comprehensive evaluation of all neuronal populations falls beyond the scope of this research. The use of ventralized MGE-like organoids enabled us to examine whether key defects were cell-autonomous, including the reduced neuronal output of inhibitory progenitors, increased apoptosis, and abnormal inhibitory-neuron morphology.

(7) ARHGEDF6 deletion has an important impact on organoid development (size, shape, etc). Have the authors analysed whether these organoids produced fewer interneurons?

We would like to clarify that the organoids analyzed in the study are ventral MGE-like organoids and therefore the reduction in neuronal output (current Figure 4K) primarily reflects the ventral/interneuron lineage in this model.

(8) In assembloids, the differences in migration parameters are very small between WT and ARHGEF6-KO, which reinforces that perhaps what is observed in the different layers of cortex during mouse development is likely not entirely due to migration, as concluded.

We agree that the migration parameters in assembloids should not be interpreted in isolation. We will revise the text to emphasize that the reduction in the number of interneurons observed in the adult brains is part of a broader pattern that also includes altered neuronal output and reduced viability.

(9) To properly weigh the present evidence -interneuron deficits- using the ARHGEF6-KO model, authors should include a deeper discussion in light of much work that has been done using these mice. How does the finding of a diminished IN population in the brain of these mice explain the large amount of electrophysiological and behavioral evidence produced before with these animals? Perhaps the most important work to discuss these aspects is the initial ARHGEF6-KO report by Ramakers and colleagues (2012), but there are others.

We appreciate the reviewer’s emphasis on the importance of framing our findings within the broader context of the existing literature. We will expand the Discussion to better integrate previous work on ARHGEF6-KO mice. Specifically, we will discuss how reduced interneuron number and altered interneuronal function may contribute to previously reported electrophysiological and behavioral phenotypes, acting in concert with previously described alterations in excitatory neurons and synaptic plasticity (Ramakers et al., 2012).

Minor comments:

(1) Figure 1A. It looks clear that the GE shows the highest expression of ARHGEF6; however, the reader needs the reference levels where the log2 expression is calculated. What are the reference levels?

We would like to thank the reviewer for pointing this out. We will clarify in the caption that the log2(RPKM+1) expression values are shown as absolute values and are not relative to a reference condition.

(2) Have the authors compared the number of GAD67-eGFP cells in the hippocampal cultures between WT and ARHGEF6-KO mice?

We did not rely on total GAD67-eGFP counts in dissociated hippocampal cultures because differences could reflect initial plating composition, survival, and maturation. In our experience, the MGE-like organoid system provides a more controlled in vitro context to assess neuronal output in the ventral lineage.

(3) Section 3, as a caution note, authors should mention that it is not possible to know from the evidence provided which cells are dying.

We agree with the reviewer and will add a cautionary statement noting that TUNEL staining alone does not identify the precise dying cell type. We will clarify that increased cell death in the ganglionic eminence and MGE-like organoids is consistent with a prominent involvement of the ventral/inhibitory lineage, while acknowledging the limits of the assay.

(4) In the dorsal-ventral assembloids, it is expected that the ventral organoid would contain lots of GFP expression compared to the dorsal, but in the image shown (Figure 5A) both parts of the assembloid seem to have the same amount and distribution of GFP. How is that possible?

We appreciate the thoughtful comment of the reviewer. After two weeks of fusion, a considerable number of interneurons are expected to have migrated from the ventral to the dorsal compartment of the assembloid (Birey et al., 2017; Sloan et al., 2018). In terms of distribution, we think that current Figure 5A shows a gradient of eGFP-positive cells within the dorsal compartment, with the number of labeled cells decreasing as the distance from the fusion interface between the two organoids increases. By contrast, a comparable gradient is not evident in the ventral compartment, where several labeled neurons remain present even in regions distal to the fusion site.

Reviewer #3 (Public review):

Summary:

ARHGEF6 is a RAC1/CDC42 guanine nucleotide exchange factor that has been proposed to be associated with X-linked intellectual disability, but its relevance to the pathology is not well established. ARHGEF6 has been assigned a role in spine density and plasticity of hippocampal pyramidal neurons, but nothing is known about its role in interneuron development. Here, the authors show that ARHGEF6 is expressed early in development in the inhibitory lineage during the peak of interneuron generation and migration. The aim of the study is therefore to investigate whether, in addition to its role in pyramidal neurons, ARHGEF6 could play a role in inhibitory neuron development. Using both ARHGEF6-KO mice and organoids from ARHGEF6-KO hiPSCs, the authors show that ARHGEF6 plays a critical role in interneuron development and function

Strengths:

The major strength of the paper is the very detailed analysis of the role of ARHGEF6 using two different systems: ARHGEF6-KO mice and deletion of ARHGEF6 in human iPSC-derived organoids. Strikingly, deletion of ARHGEF6 in both systems induces similar defects such as an increase in apoptosis, reduced neuronal output, impaired neuronal morphology, and disrupted migratory dynamics. This compelling evidence demonstrates that ARHGEF6, in addition to its already well-described role in spine formation and plasticity, is playing a crucial role during embryonic development through its function in interneurons.

We thank the reviewer for this positive assessment of our work and for highlighting the strength of our combined in vivo and human iPSC-derived organoid approaches. We are pleased that the reviewer recognizes the consistency of the phenotypes observed across both systems and acknowledges that our findings support a crucial role, during early stages of embryonic development, for a protein previously thought to be relevant primarily in the synaptic context.

Weaknesses:

(1) In Figure 1, the authors show that ARHGEF6 is expressed in different regions of the brain, including the interneuron lineage, and that depletion of ARHGEF6 reduces the number of GABAergic neurons in the adult cortex and hippocampus. To try to better characterize this defect, the authors in Figure 2 investigate whether deletion of ARHGEF6 affects interneuron migration and survival during embryonic development. To do so, ARHGEF6 ko mice were crossed with the GAD67-eGFP reporter line to follow the inhibitory lineage. The authors analyse apoptosis using TUNEL staining, and show that it is significantly increased in the ganglion eminence of ARHGEF6-KO E14.5 embryos. The authors claim that this is not the case in the cortex. However, the image shown in Figure 2A really suggests that staining is increased. Which part of the neocortex is analysed for quantification? This should be clarified.

We would like to thank the reviewer for pointing this out. The region analyzed was the same as that used to assess GAD67-eGFP-positive cells in Figure 2F. We will clarify the exact neocortical region used for TUNEL quantification and revise the figure and legend to make the analyzed area explicit. We will also analyze additional animals to improve the accuracy of the analysis.

(2) In Figure 2F-J, the authors investigate the migration of interneurons by analysing the GAD67-eGFP staining, and clearly show that the migratory abilities of the depleted neurons are reduced. However, the authors do not discuss the fact that, because depletion of ARHGEF6 increases apoptosis, there are fewer neurons available for migration. This is important for the interpretation of the data. This point should be clarified.

We appreciate this comment and believe that it is particularly relevant to the interpretation of the data shown in Figure 2F–G. We will clarify the limited interpretation of this specific analysis in the Results section. The altered directionality observed in vivo, together with evidence of impaired migratory behavior obtained through in vitro live imaging, supports the possibility that altered migratory dynamics contribute to the phenotype, although increased apoptosis and reduced neuronal output may also contribute.

(3) In Supplementary Figure S2, the authors describe the establishment of the ARHGEF6-KO human iPSC line and test the ability of these cells to undergo correct development, especially for the generation of neural progenitor cells. I was wondering why the authors do not present the data of both control and ARHGEF6-KO cells.

We thank the reviewer for pointing this out. All staining reported in the organoids and assembloids in this paper shows that the WT ATCC-DYS0100 cell line, as well as the mutant, efficiently differentiates into neuronal tissue. The Supplementary Figure was intended to validate the impact of the mutation on the ability of the iPSC line to retain its differentiation capacity as a preliminary step before proceeding with organoid differentiation. We will integrate stainings for NPC markers on the WT line in the Supplementary Figure.

(4) At the molecular level, how ARHGEF6 depletion could affect neuronal survival is missing. In addition, as ARHGEF6 is a GEF for RAC1 and Cdc42 amongst other GEFs, I would have expected that the authors test how RAC1 activity (and Cdc42) is affected in ARHGEF6-depleted brains and in ARHGEF6-KO organoids. The measure of phalloidin staining and the anisotropy index are not really meaningful.

We appreciate the thoughtful comment of the reviewer. Previous evidence already shows that Arhgef6 loss reduces the activity of both GTPases and deregulates the expression of the cytoskeletal regulators Pak1–3, Limk1, and Cofilin in the mouse brain (Ramakers et al., 2012). Regarding organoids, we agree that direct RAC1/CDC42 activity measurements would have strengthened the molecular mechanism. We will revise the manuscript to avoid implying that our phalloidin-based measurements alone establish the underlying dysregulated molecular pathway.

(5) The authors show that ARHGEF6-KO forebrain organoids were markedly smaller compared to their isogenic controls, and their study suggests that ARHGEF6 expression impacts progenitor maintenance and neurogenesis. Despite representing only a minority of the total neuronal population, I was wondering whether ARHGEF6-KO mice present brain morphology defects such as microcephaly.

We appreciate the comment. We did not perform a morphometric analysis for microcephaly in the present study. We will add this limitation to the Discussion and note that gross brain morphology changes were not reported in the previously published ARHGEF6-KO mouse characterization (Ramakers et al., 2012). We will also clarify that the smaller organoid phenotype may reflect developmental defects that may reflect developmental defects that are not fully compensated in a reductionist in vitro model and therefore do not necessarily imply overt microcephaly in vivo.

References

Allen Institute for Brain Science. Allen Mouse Brain Atlas: Arhgef6 ISH data. Available from: Allen Brain Map.

Birey, F., Andersen, J., Makinson, C. D., Islam, S., Wei, W., Huber, N., Fan, H. C., Metzler, K. R. C., Panagiotakos, G., Thom, N., O’Rourke, N. A., Steinmetz, L. M., Bernstein, J. A., Hallmayer, J., Huguenard, J. R., & Pașca, S. P. (2017). Assembly of functionally integrated human forebrain spheroids. Nature, 545(7652), 54–59. https://doi.org/10.1038/nature22330

Liaci, C., Camera, M., Zamboni, V., Sarò, G., Ammoni, A., Parmigiani, E., Ponzoni, L., Hidisoglu, E., Chiantia, G., Marcantoni, A., Giustetto, M., Tomagra, G., Carabelli, V., Torelli, F., Sala, M., Yanagawa, Y., Obata, K., Hirsch, E., & Merlo, G. R. (2022). Loss of ARHGAP15 affects the directional control of migrating interneurons in the embryonic cortex and increases susceptibility to epilepsy. Frontiers in Cell and Developmental Biology, 10, 875468. https://doi.org/10.3389/fcell.2022.875468

Nodé-Langlois, R., Muller, D., & Boda, B. (2006). Sequential implication of the mental retardation proteins ARHGEF6 and PAK3 in spine morphogenesis. Journal of Cell Science, 119(23), 4986–4993. https://doi.org/10.1242/jcs.03273

Pelkey, K. A., Chittajallu, R., Craig, M. T., Tricoire, L., Wester, J. C., & McBain, C. J. (2017). Hippocampal GABAergic inhibitory interneurons. Physiological Reviews, 97(4), 1619–1747. https://doi.org/10.1152/physrev.00007.2017

Ramakers, G. J. A., Wolfer, D., Rosenberger, G., Kuchenbecker, K., Kreienkamp, H.-J., Prange-Kiel, J., Rune, G., Richter, K., Langnaese, K., Masneuf, S., Bösl, M. R., Fischer, K.-D., Krugers, H. J., Lipp, H.-P., van Galen, E., & Kutsche, K. (2012). Dysregulation of Rho GTPases in the αPix/Arhgef6 mouse model of X-linked intellectual disability is paralleled by impaired structural and synaptic plasticity and cognitive deficits. Human Molecular Genetics, 21(2), 268–286. https://doi.org/10.1093/hmg/ddr457

Sloan, S. A., Andersen, J., Pașca, A. M., Birey, F., & Pașca, S. P. (2018). Generation and assembly of human brain region-specific three-dimensional cultures. Nature Protocols, 13(9), 2062–2085. https://doi.org/10.1038/s41596-018-0032-7

Yao, Z., Nguyen, T. N., van Velthoven, C. T. J., Goldy, J., Sedeno-Cortes, A. E., Baftizadeh, F., Bertagnolli, D., Casper, T., Chiang, M., Crichton, K., Ding, S.-L., Fong, O., Garren, E., Glandon, A., Gouwens, N. W., Gray, J., Graybuck, L. T., Hawrylycz, M. J., Hirschstein, D., … Zeng, H. (2021). A taxonomy of transcriptomic cell types across the isocortex and hippocampal formation. Cell, 184(12), 3222–3241.e26. https://doi.org/10.1016/j.cell.2021.04.021

Author response:

We sincerely thank the reviewers and editors for the thorough, constructive, and insightful comments, which have greatly helped us improve the accuracy, clarity, and rigor of the manuscript. We acknowledge that the current version has several limitations, including insufficient contextualization with other model systems and lack of critical synthesis. These important weaknesses will be comprehensively addressed in a future revised version of the review.

For the present revision, we have focused exclusively on correcting objective errors, factual inaccuracies, and citation mistakes as pointed out by the reviewers. All specific factual and reference issues raised by Reviewer 2 and Reviewer 3 have been carefully corrected in the revised manuscript, including inaccurate statements, incorrect citations, missing references, and inconsistent descriptions of zebrafish clock genes, photoreception, and physiological functions.

We appreciate the reviewers’ thoughtful suggestions regarding the conceptual depth, comparative context, critical synthesis, and expanded discussion of sleep and model limitations. While we fully agree that these aspects would significantly strengthen the review, we plan to systematically incorporate these broader conceptual improvements in a future, more substantial revision.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Evidence, reproducibility and clarity):

Summary

Sheidaei and colleagues report a novel and potentially important role for an early mitotic actomyosinbased mechanism, PANEM contraction, in promoting timely congression of chromosomes located at the nuclear periphery, particularly those in polar positions. The manuscript will interest researchers studying cell division, cytoskeletal dynamics, and motor proteins. Although some data overlap with the group's prior work, the authors extend those findings by optimizing key perturbations and performing more detailed analyses of chromosome movements, which together provide a clearer mechanistic explanation. The study also builds naturally on recent ideas from other groups about how chromosome positioning influences both early and later mitotic movements.

In its current form, however, the manuscript is not acceptable for publication. It suffers from major organizational problems, an overcrowded and confusing Results section and figures, and a lack of essential experimental controls and contextual discussion. These deficiencies make it difficult to evaluate the data and the authors' conclusions. A substantial structural revision is required to improve clarity and persuasiveness. In addition, several key control experiments and more conceptual context are needed to establish the specificity and relevance of PANEM relative to other microtubule- and actin-based mitotic mechanisms. Testing PANEM in additional cell lines or contexts would also strengthen the claim. I therefore recommend Major Revision, addressing the structural, conceptual, and experimental issues detailed below.

Major Comments

A. Structural overhaul and figure reorganization

The Results section is overly dense, lacks clear structure, and includes descriptive content that belongs in the Methods. Many figure panels should be moved to Supplementary Materials. A substantial reorganization is required to transform the manuscript into a focused, "Reports"-type article.

Move methodological and descriptive details (e.g., especially from the second Results subheading and Figure 2) to the Methods or Supplementary Materials.

In these parts, we define four phases of kinetochore motion in early mitosis. Without such a description in the main text, readers would be confused about subsequent analyses. Figure 2 is also important to show examples of how the four phases develop. Although we respect this suggestion from the reviewer, we would like to keep these parts in the main text and main figure.

Remove repetitive statements that simply restate that later phenotypes arise as consequences of delayed Phase 1 (applicable to subheadings 3 onward).

As suggested, we have removed the statement for the delayed start of Phase 2 for peripheral kinetochores in azBB-treated cells (Page 9, second paragraph). We have also simplified the statement for the delayed start of Phase 3 and Phase 4 to avoid repetition (Page 9, third paragraph; Page 10, second paragraph).

Figure 4I: This panel is currently unclear and should be drastically simplified.

Following this suggestion, we simplified Figure 4I by removing the column of ‘Start’, which is easily deduced from the ‘Duration’ results and therefore does not provide much new information.

I recommend to reorganize figures as follows:

Figure I: Keep as single figure but simplify. Figure 1D and 1E could be combined, move unnormalized SCV to supplementary materials. Same goes for 1F.

We have reorganized Figure 1, as suggested, and moved unnormalized data to supplemental materials.

New Figure 2: Combine current Figures 2A, 3A, 3C, 3D, 4C, 4F, and 4H to illustrate how PANEM contraction facilitates initial interactions of peripheral chromosomes with spindle microtubules which increases speed of congression initiation.

If we were to follow this suggestion, we would lose Figure 2B, D, Figure 3B and Figure 4A, where examples of kinetochore motions are shown in images and 3D diagrams. The new Figure would mostly consist of only graphs. Without examples of images and 3D diagrams, readers would have difficulty understanding the study. Although we respect this suggestion from the reviewer, we would like to keep Figures 2, 3 and 4, as they are (except for making Figure 4I simpler; see above).

New Figure 3: Combine current Figures 5A, 5C, 5D, 5F, 6B, 6C, and lower panels of 4H to show how

PANEM contraction repositions polar chromosomes and reduces chromosome volume in early mitosis to enable rapid initiation of congression.

If we were to follow this suggestion, we would lose Figure 5B and Figure 6A, where examples of kinetochore/chromosome dynamics are shown in images and 3D diagrams. For the same reason as above, we would like to keep Figure 5 and 6 as they are, although we respect this suggestion from the reviewer.

New Figure 4: Combine Figures 7A, 7B, 7D, 7E, 7F, expanded Supplementary Figure S7, and new data to demonstrate that PANEM actively pushes peripheral chromosomes inward which is important for efficient chromosome congression in diverse cellular contexts.

We have conducted new experiments to demonstrate the role of PANEM in diverse cellular contexts, as detailed below. We have combined the new results with the original Figure S7 to create Figure 8 in line with this suggestion.

On the other hand, in our view, combining Figure 7A-E and the extended Figure S7 would be confusing because the two parts address different topics. Although we respect this suggestion from the reviewer, we would like to keep Figure 7 and the extended Figure S7 (i.e. Figure 8) separate.

B. Specificity and redundancy of actin perturbation

To establish the specificity and relevance of PANEM, the authors should include or discuss appropriate controls:

Apply global actin inhibitors (e.g., cytochalasin D, latrunculin A) to disrupt the entire actin cytoskeleton. These perturbations strongly affect mitotic rounding and cytokinesis but only modestly influence early chromosome movements, as reported previously (Lancaster et al., 2013; Dewey et al., 2017; Koprivec et al., 2025). The minimal effect of global inhibition must be addressed when proposing a localized actomyosin mechanism. Comment if the apparent differences in this approach and one that the authors were using arises due to different cell types.

We did experiments along this line, using a dominant-negative LINC construct, in our previous study (Booth et al eLife 2019). LINC-DN should more specifically remove/reduce PANEM than the global actin inhibitors mentioned above. LINC-DN attenuated the reduction of CSV soon after NEBD and increased the number of polar chromosomes (Booth et al eLife 2019); i.e. in this regard, the outcome was similar to azBB treatment in the current study. One can expect that global actin inhibitors would also inhibit the PANEM formation and show effects similar to LINC-DN. By contrast, the indicated references reported that global actin inhibitors strongly affect mitotic rounding and cytokinesis but only modestly influence early chromosome movements, as the reviewer noted. One possibility is that such differences may have arisen from different cell types – this could be important, especially given that some cells form the PANEM and others do not (Figure 8A). A second possibility is that cytokinesis, mitotic rounding and PANEM formation may rely on actin polymerization to different extents. For example, the same concentration of global actin polymerization inhibitors may affect cytokinesis, but may still allow PANEM formation to proceed without observable effects on early chromosome movements. As suggested, we discussed this topic in the Discussion (page 16, third paragraph).

Clarify why spindle-associated actin, especially near centrosomes, as reported in prior studies using human cultured cells (Kita et al., 2019; Plessner et al., 2019; Aquino-Perez et al., 2024), was not observed in this study. The Myosin-10 and actin were also observed close to centrosomes during mitosis in X.laevis mitotic spindles (Woolner et al., 2008). Possible explanations include differences in fixation, probe selection, imaging methods, or cell type. Note that some actin probes (e.g., phalloidin) poorly penetrate internal actin, and certain antibodies require harsh extraction protocols. Comment on possibility that interference with a pool of Myo10 at the centrosomes is important for effects on congression.

As the reviewer implies, we cannot rule out that we could not detect actin associated with the spindle or centrosomes because of the difference in methods or cell lines between the current study and the literature mentioned by the reviewer. We have therefore moderated our claim in the Discussion that ‘we did not detect any actin network inside the nucleus, on the spindle or between chromosomes’ by adding ‘at least, using the method and the cell line in the current study’ to this statement (Page 14, second paragraph). We have also cited the three references mentioned by the reviewer in the Discussion (Page 14, second paragraph). Regarding Myosin10, azBB (blebbistatin variant) should have negligible effects on class-X myosin, including Myosin-10 (Limouze et al 2004 [PMID 15548862]). It is therefore unlikely that the effects of azBB that we observed in the current study are due to the inhibition of Myosin-10. We have cited Woolner et al 2008 and another paper and discussed this topic in the Discussion (Page 14, second paragraph).

C. Expansion of PANEM functional analysis

To strengthen the conclusions and broaden the study beyond the group's previous work, PANEM function should be tested in additional contexts (some may be considered optional but important for broader impact): [underlined by authors]

Test PANEM function in at least one additional cell line that displays PANEM to rule out cell-line-specific effects.

As suggested, we have studied the effect of PANEM contraction in cell lines other than U2OS. We have found that when PANEM contraction was inhibited, the reduction in chromosome scattering was diminished in RPE1 cells (new Figure 8B, C). Moreover, we have found that inhibition of PANEM contraction increased polar chromosomes during prometaphase/ metaphase in RPE1 and HCT116 cells (which form PANEM), but not in HeLa cells (which do not form PANEM) (new Figure 8D, E). These results suggest that the effects of PANEM contraction, originally observed in U2OS cells, are also present in other cell lines (RPE1 and HCT116) that form PANEM.

Examine higher-ploidy or binucleated cells to determine whether multiple PANEM contractions are coordinated and if PANEM contraction contributes more in cells of higher ploidies or specific nuclear morphologies.

This is an interesting suggestion, but it takes lots of time to conduct such a study, and it goes beyond the scope of this paper.

Investigate dependency on nuclear shape or lamina stiffness; test whether PANEM force transmission requires a rigid nuclear remnant.

This is an interesting suggestion, but it takes lots of time to conduct such a study, and it goes beyond the scope of this paper.

Analyze PANEM's contribution under mild microtubule perturbations that are known to induce congression problems (e.g., low-dose nocodazole).

In the current study, we found that PANEM contraction affects chromosome motions in Phase 1 and Phase 3 but not Phase 2 or Phase 4. Mild microtubule perturbation itself could affect chromosome motions in all four Phases. We do not think it would be so informative to study what additional effects the reduced PANEM contraction shows when combined with mild microtubule perturbation.

Evaluate PANEM contraction role in unsynchronized U2OS cells, where centrosome separation can occur before NEBD in a subset of cells (Koprivec et al., 2025), and in other cell types with variable spindle elongation timing.

Following this suggestion, we first investigated the timing of spindle elongation, relative to NEBD, in asynchronous U2OS cells (Figure 8 – figure supplement 3). We imaged cells every 5 min (it was difficult to reasonably observe enough mitotic cells using a shorter interval). Most of the cells showed no significant change in the spindle length (distance between two spindle poles) after (or around) NEBD [e.g. Cell 1 in A] or a mild reduction in it [e.g. Cell 2 in A]. Only a small number of cells (2-3 out of 26) showed a mild increase in the spindle length after (or around) NEBD [e.g. Cell 3 in A]. Because the spindle elongation after NEBD was rare and mild, it was difficult to address how the timing of spindle elongation affects the effect of PANEM on reducing chromosome scattering and on chromosome relocation from polar regions. We explained this result and discussed this topic in the Discussion section.

Quantify not only the percentage of affected cells after azBB but also the number of chromosomes per cell with congression defects in the current and future experiments.

It is tricky to count the number of chromosomes because they frequently overlap. Counting kinetochores is more feasible, but kinetochore signals show some non-specific background (e.g. those outside of the nucleus in prophase). We therefore quantified the chromosome volume at polar regions in azBB-treated cells (Figure 6C).

D. Conceptual integration in Introduction and Discussion

The manuscript should better situate its findings within the context of early mitotic chromosome movements:

Clearly state in the Introduction and elaborate in the Discussion that initiation of congression is coupled to biorientation (Vukušić & Tolić, 2025). This provides essential context for how PANEM-mediated nuclear volume reduction supports efficient congression of polar chromosomes.

It has been a widely accepted view in the field that chromosome congression precedes biorientation, since the publication in 2006 (Kapoor et al Science 2006). Very recently, this view has been challenged by the new publication (Vukušić & Tolić, Nat comm 2025), as indicated by this reviewer. We have mentioned this new model and discussed the new interpretation of our results based on this new model, in the Discussion (page 15; ‘It has been a widely accepted view…’).

To explain the new interpretation of our results more clearly, we have a new diagram as a supplemental figure (Figure 9 – figure supplement 1) in the revised manuscript.

Explain that PANEM is most critical for polar chromosomes because their peripheral positions are unfavorable for rapid biorientation (Barišić et al., 2014; Vukušić & Tolić, 2025).

We have included such a statement in the Discussion, as a part of the new interpretation of our results based on the new model that chromosome biorientation precedes congression (see above). We have also cited the indicated two papers.

Discuss how cell lines lacking PANEM (e.g., HeLa and others) nonetheless achieve efficient congression, and what alternative mechanisms compensate in the absence of PANEM. For example, it is well established that cells congress chromosomes after monastrol or nocodazole washout, which essentially bypasses the contribution of PANEM contraction.

Following this suggestion, we discussed three possible mechanisms that could compensate for a lack of PANEM and facilitate kinetochore-MT interaction and chromosome congression, based on previous literature (Page 17): 1) the enhanced assembly rate of spindle MTs may facilitate kinetochore-MT interactions in N-CIN+ cancer cells, 2) chromosome biorientation may precede congression more frequently to promote the congression towards the spindle midplane, and 3) the balance between CENP-E, Dynein and chromokinesin’s activities may incline to greater chromosome-arm ejection forces towards the spindle midplane.

Minor Comments

These issues are more easily addressable but will significantly improve clarity and presentation.

Introduction

Remove the reference to Figure 1A in the Introduction. The portion of Figure 1 and related text that recapitulates the authors' previous work should be incorporated into the Introduction, not the Results.

As suggested in the second sentence of this comment, we have moved most of the second paragraph of the first section of Results to Introduction (Page 4) and cited Figure 1A and 1B in Introduction. We would like to keep the reference to Figure 1A in the Introduction, because showing the PANEM images at the beginning of the manuscript would help readers’ understanding of our study. In addition, citing Figure 1A in the Introduction is more consistent with the suggestion in the second sentence of this comment.

Results (by subheading)

First subheading: When introducing the ~8-minute early mitotic interval, cite additional studies that have characterized this period: Magidson et al., 2011 (Cell); Renda et al., 2022 (Cell Reports); Koprivec et al., 2025 (bioRxiv); Vukušić & Tolić, 2025 (Nat Commun); Barišić et al., 2013 (Nat Cell Biol).

As suggested, we cited these references at the indicated part of the first section of the Results (page 5).

Second subheading: Cite key reviews and foundational research on kinetochore architecture and sequential chromosome movement during early mitosis: Mussachio & Desai, 2017 (Biology); Itoh et al., 2018 (Sci Rep); Magidson et al., 2011 (Cell); Vukušić & Tolić, 2025 (Nat Commun); Koprivec et al., 2025 (bioRxiv); Rieder & Alexander, 1990 (J Cell Biol); Skibbens et al., 1993 (J Cell Biol); Kapoor et al., 2006 (Science); Armond et al., 2015 (PLoS Comput Biol); Jaqaman et al., 2010 (J Cell Biol).

Rieder & Alexander, 1990 (J Cell Biol) and Kapoor et al., 2006 (Science) have already been cited in the second section of the Results in the original manuscript. We agree that all other references should be cited in this manuscript, and they are now cited in the Introduction and/or Discussion where they fit best (e.g. Mussachio & Desai 2017 reviews the kinetochore in general and is therefore best cited in the Introduction).

Third subheading: Clarify why some kinetochores on Figure 3A appear outside the white boundaries if these boundaries are intended to represent the nuclear envelope.

We interpret that these are background signals in the cytoplasm, which do not come from kinetochores, because 1) before NEBD, they were outside of the nucleus, and 2) after NEBD, they did not show any characteristic kinetochore motions such as those towards a spindle pole (Phase 2) and the spindle mid-plane (Phase 4). We have commented on these background signals in the legend for Figure 3A.

Fourth subheading: Note that congression speed is lower for centrally located kinetochores because they achieve biorientation more rapidly (Barišić et al., 2013, Nat Cell Biol; Vukušić & Tolić, 2025, Nat Commun).

Relevant to this comment, there was an error regarding the congression speed of central kinetochores (original Figure 4H). The congression speed of peripheral kinetochores was shown correctly, but for central kinetochores it was shown incorrectly with µm per time interval (30s) shown, rather than µm per minute. We amended this error in the revised manuscript (new Figure 4H). Based on the corrected data, the speed of congression is similar between peripheral and central kinetochores. The original Figure 3G (the speed of poleward motion for central kinetochores) had a similar error, which we have also corrected in the revised manuscript. We apologize for these errors and the confusion it may have caused.

Regarding this comment, if biorientation is achieved more rapidly for central kinetochores, Phase 3 (rather than congression speed) would be shorter for central kinetochores. Indeed, Phase 3 is slightly shorter for central kinetochores (control) than for peripheral kinetochores (control) (Figure 4C), but the difference is not statistically significant (t test; p\=0.21).

Fifth subheading: Cite studies on polar chromosome movements: Klaasen et al., 2022 (Nature); Koprivec et al., 2025 (bioRxiv). Clarify that Figure 5F displays only those kinetochores that initiated directed congression movements.

These two references have already been cited and discussed in this Result section of our original manuscript. However, considering this suggestion, we have discussed more about polar chromosome movements reported by Koprivec et al (page 11). Meanwhile, the reviewer is correct about Figure 5F, and we have clarified this point in the Figure 5F legend.

Sixth subheading (currently in Discussion): Move the final paragraph of the Discussion into the Results and expand it with preliminary analyses linking PANEM contraction to congression efficiency across untreated cell types or under mild nocodazole treatment.

As suggested, we have moved the final paragraph of the Discussion in the original manuscript to make a new final section in the Results in the revised manuscript. Moreover, as suggested, we have studied the outcome of inhibiting PANEM contraction in cell lines other than U2OS (Figure 8 B–E), and have described the new results to the new final section in the Results.

Discussion

1. When discussing cortical actin, cite key reviews on its presence and function during mitosis: Kunda & Baum, 2009 (Trends Cell Biol); Pollard & O'Shaughnessy, 2019 (Annu Rev Biochem); Di Pietro et al., 2016 (EMBO Rep).

As suggested, we have cited all these review papers in the Discussion (page 17), and mentioned the role of the cortical actin on the spindle orientation and positioning (Kunda & Baum, 2009; Di Pietro et al., 2016), as well as the function of the actomyosin ring on cytokinesis (Pollard & O'Shaughnessy, 2019).

Significance

Advance

This study's main strength is its novel and potentially important demonstration that contraction of PANEM, a peripheral actomyosin network that operates contracts early mitosis, contributes to the timely initiation of chromosome congression, especially for polar chromosomes. While PANEM itself was previously described by this group, this manuscript provides new mechanistic evidence, improved perturbations, and detailed chromosome tracking. To my knowledge, no prior studies have mechanistically connected this contraction to polar chromosome congression in this level of detail. The work complements dominant microtubule-centric models of chromosome congression and introduces actomyosin-based forces as a cooperating system during very early mitosis. However, the impact of the study is currently limited by major organizational issues, insufficient controls, and incomplete contextualization within existing literature. Addressing these issues will substantially improve clarity and credibility. [underlined by authors]

We have addressed the underlined criticisms as detailed above.

Audience

Primary audience of this study will be researchers working in cell division, mitosis, cytoskeleton dynamics, and motor proteins. The findings may interest also the wider cell biology community, particularly those studying chromosome segregation fidelity, spindle mechanics, and cytoskeletal crosstalk. If validated and clarified, the concept of PANEM could be integrated into textbooks and models of chromosome congression and could inform studies on mitotic errors and cancer cell mechanics.

Expertise

My expertise lies in kinetochore-microtubule interactions, spindle mechanics, chromosome congression, and mitotic signaling pathways.

Reviewer #2 (Evidence, reproducibility and clarity):

In this manuscript, Sheidaei et al. reported on their study of chromosome congression during the early stages of mitotic spindle assembly. Building on their previous study (ref. #15, Booth et al., Elife, 2019), they focused on the exact role of the actin-myosin-based contraction of the nuclear envelope. First, they addressed a technical issue from their previous study, finding a way to specifically impair the actomyosin contraction of the nuclear membrane without affecting the contraction of the plasma membrane. This allowed them to study the former more specifically. They then tracked individual kinetochores to reveal which were affected by nuclear membrane contraction and at what stage of displacement towards the metaphase plate. The investigation is rigorous, with all the necessary controls performed. The images are of high quality. The analyses are accurate and supported by convincing quantifications. In summary, they found that peripheral chromosomes, which are close to the nuclear membrane, are more influenced by nuclear membrane contraction than internal chromosomes. They discovered that nuclear membrane contraction primarily contributes to the initial displacement of peripheral chromosomes by moving them towards the microtubules. The microtubules then become the sole contributors to their motion towards the pole and subsequently the midplane. This step is particularly critical for the outermost chromosomes, which are located behind the spindle pole and are most likely to be missegregated.

Significance

While the conclusions are somewhat intuitive and could be considered incremental with regard to previous works, they are solid and improve our understanding of mitotic fidelity. The authors had already reported the overall role of nuclear membrane contraction in reducing chromosome missegregation in their previous study, as mentioned fairly and transparently in the text. However, the reason for this is now described in more detail with solid quantification. Overall, this is good-quality work which does not drastically change our understanding of chromosome congression, but contributes to improving it. Personally, I am surprised by the impact of such a small contraction (of around one micron) on the proper capture of chromosomes and wonder whether the signalling associated with the contraction has a local impact on microtubule dynamics. However, investigating this point is clearly beyond the scope of this study, which can be published as it is. [underlined by authors]

The suggested topic (underlined) is intriguing. However, we agree with the reviewer that it is beyond the scope of this paper. The reviewer recommends publication of our manuscript as it is.

Reviewer #3:

Sheidaei et al., report how chromosomes are brought to positions that facilitate kinetochore-microtubule interactions during mitosis. The study focusses on an important early step of the highly orchestrated chromosome segregation process. Studying kinetochore capture during early prophase is extremely difficult due to kinetochore crowding but the team has taken up the challenge by classifying the types of kinetochore movements, carefully marking kinetochore positions in early mitosis and linking these to map their fate/next-positions over time. The work is an excellent addition to the field as most of the literature has thus far focussed on tracking kinetochore in slightly later stages of mitosis. The authors show that the PANEM facilitates chromosome positioning towards the interior of the newly forming spindle, which in turn facilitates chromosome congression - in the absence of PANEM chromosomes end up in unfavourable locations, and they fail to form proper kinetochore-microtubule interactions. The work highlights the perinuclear actomyosin network in early mitosis (PANEM) as a key spatial and temporal element of chromosome congression which precedes the segregation process.

Major points

(1) The complexity of tracking has been managed by classifying kinetochore movements into 4 categories, considering motions towards or away from the spindle mid-plane. While this is a very creative solution in most cases, there may be some difficult phases that involve movement in both directions or no dominant direction (eg Phase3-like). It is unclear if all kinetochores go through phase1, 2, 3 and 4 in a sequential or a few deviate from this pattern. A comment on this would be helpful. Also, it may be interesting to compare those that deviate from the sequence, and ask how they recover in the presence and absence of azBB.

To respond to this comment, we would like to first clarify how we selected kinetochores for our analysis. We selected kinetochores that can be individually tracked. If kinetochore tracking was difficult (before the start of Phase 4 in control and azBB-treated cells or before observing the extended Phase 3 in azBB-treated cells) because of kinetochore crowding, we did not choose such kinetochores. For example, related to the next comment of this Reviewer, we did not include kinetochores close to spindle poles (within 4 µm) at NEBD in our analysis for the following two reasons: First, these kinetochores often did not show clear and rapid movements towards a spindle pole, which we used to define Phase 2. Second, although we referred to kinetochore co-localization with a microtubule signal for the start of Phase 2, this was difficult for kinetochores close to spindle poles because of a high density of microtubules. As requested, we have added this comment to the Method section (page 25).

With the above selection, all selected kinetochores without azBB treatment (control) showed the poleward motion (Phase 2) and congression (Phase 4) in this order, though their extents were varied among kinetochores. All selected kinetochores with azBB treatment also showed the poleward motion (Phase 2), and some of them showed congression (Phase 4) after Phase 2. Then, Phase 1 and Phase 3 were defined as intervals between NEBD and Phase 2 and between Phase 2 and Phase 4, respectively. If no Phase 4 was observed with azBB, we judged that Phase 3 continued till the end of tracking. We have added this comment to the Method section (page 25-26).

(2) Would peripheral kinetochore close to poles behave differently compared to peripheral kinetochore close to the midplane (figure S4)? In figure 3D, are they separated? If not, would it look different?

Since we did not include kinetochores close to spindle poles (at NEBD), for which it was difficult to define Phase 2 (see our response to the above major point 1), in our analysis, the suggested comparison is not feasible.

(3) Uncongressed polar chromosomes (eg., CENPE inhibited cells) are known to promote tumbling of the spindle. In figure 5B with polar chromosomes, it will be helpful to indicate how the authors decouple spindle pole movements from individual kinetochore movements.

In contrast to CENPE-inhibited cells, azBB-treated cells did not show much tumbling of the spindle, though both cells showed uncongressed polar chromosomes. The reason for this difference may be fewer uncongressed polar chromosomes in azBB-treated cells. There were still modest spindle motions in azBB-treated cells. However, because kinetochore motions were assessed relative to a spindle pole (and other reference points on the spindle) in our study (Figure 2A, C), the modest spindle motions were offset in our analyses of kinetochore motions. We have clarified the underlined part in the Method section (page 24).

(4) The work has high quality manual tracking of objects in early mitosis- if this would be made available to the field, it can help build AI models for tracking. The authors could consider depositing the tracking data and increasing the impact of their work.

As suggested, we have included kinetochore tracking data as supplemental data in the revised manuscript (Figure 3 – source data 1–4; Figure 5 – source data 1, 2).

Minor points

(1) It will be helpful for readers to see how many kinetochores/cell were considered in the tracking studies. Figure legends show kinetochore numbers but not cell numbers.

As suggested, we have now mentioned the number of cells, where the kinetochore motions were analyzed, in the legends for Figures 3, 4, 5, and supplemental figures.

(2) Discussion point: If cells had not separated their centrosomes before NEBD, would PANEM still be effective? Perhaps the cancer cell lines or examples as shown in Figure 6A have some clues here.

Following this suggestion, we first investigated the timing of spindle elongation, relative to NEBD, in asynchronous U2OS cells (Figure 8 – figure supplement 3). We imaged cells every 5 min (it was difficult to reasonably observe enough mitotic cells using a shorter interval). Most of the cells showed no significant change in the spindle length (distance between two spindle poles) after (or around) NEBD [e.g. Cell 1 in A] or a mild reduction in it [e.g. Cell 2 in A]. Only a small number of cells (2-3 out of 26) showed a mild increase in the spindle length after (or around) NEBD [e.g. Cell 3 in A]. Because the spindle elongation after NEBD was rare and mild, it was difficult to address how the timing of spindle elongation affects the effect of PANEM on reducing chromosome scattering and on chromosome relocation from polar regions. We explained this result and discussed this topic in the Discussion section.

(3) Figure 7 cartoon shows misalignment leading to missegregation. It may be useful to consider this in the context of the centrosome directed kinetochore movements via pivoting microtubules. Is this process blocked in azBB-treated cells?

We understand that the Reviewer refers to the kinetochore pivoting mechanism around a spindle pole, which was recently reported by the Tolic group (Koprivec et al., 2026). Such a pivoting mechanism would work only when the spindle elongates (i.e. the distance between spindle poles is enlarged) after NEBD. Therefore, to address this Reviewer’s question, we tried to assess how PANEM contraction contributes to relocating polar chromosomes when the spindle elongates before or after NEBD in asynchronous U2OS cells (i.e. in the situation where the kinetochore pivoting mechanism is applied or not), as we noted above in response to Point 2. However, spindle elongation after NEBD was rare and mild, and we were unable to address this issue (see our response to Point 2). We discussed this matter in the Discussion section.

(4) Are all the N-CIN- lines with PANEM highly sensitive to azBB? In other words, is PANEM essential for normal congression in some of these lines.

Because blebbistatin could kill cells by inhibiting cytokinesis, the blebbistatin sensitivity of cell growth may not necessarily reflect how essential the PANEM contraction is for chromosome congression.

Instead, we addressed more directly how essential the PANEM contraction is for chromosome congression. We analyzed chromosome congression in RPE1 and HCT116 cells (both are NCIN-) in the presence and absence of pnBB, the inhibitor of PANEM contraction (new Figure 8D, E). With pnBB, these cells showed congression defects, suggesting that the PANEM contraction is essential for chromosome congression in these N-CIN- cells.

(5) Are congression times delayed in lines that naturally lack PANEM?

For example, it takes 10-20 min for HeLa cells (lacking PANEM) to complete chromosome congression after the NEBD (Bancroft et al 2025: https://doi.org/10.1242/jcs.163659). This is not significantly different from the time (8-18 min) for chromosome congression we observed in U2OS cells (which form PANEM). We assume that cells lacking PANEM have developed a compensatory mechanism for efficient chromosome congression – we have discussed possible compensatory mechanisms in the last paragraph of the Discussion (page 17).

(6) Page 23 "we first identified the end of congression" how does this relate to kinetochore oscillations that move kinetochores away from the metaphase plate?

The start of kinetochore oscillation was defined as the end of Phase 4 if we could track the kinetochore until that point. In some cases where the kinetochore became close to the midplane (< 2.5 µm), it was not possible to track it further due to kinetochore crowding around the spindle mid-plane – in such cases, the end of Phase 4 was assigned as the end of tracking. These definitions were not necessarily clear in the original manuscript. Moreover, in the original manuscript, it was not clearly stated that the end of Phase 4 was defined in the same way for both non-polar and polar kinetochores. We have now clarified these points in the Method section (page 25).

(7) Are spindle pole distances (spindle sizes) different in early and late mitotic cells (4min vs 6min after NEBD) in control vs azBB-treated cells? Please comment on Figure S2E (mean distance) in the context of when phase 4 is completed. Does spindle size return to normal after congression?

In Figure S2E (Figure 1 – figure supplement 6 in the revised manuscript), we did not observe a significant difference in the spindle-pole distance (the spindle size) between control and azBBtreated cells at any individual time points. The smallest p-value was 0.094 at 6.0 min. As suggested, we have explained this in the legend for this supplementary figure. Completion of Phase 4 is highly variable across different kinetochores within the same cell; thus, a general comment on its completion timing in cells is not feasible.

Significance:

The current work builds upon their previous work, in which the authors demonstrated that an actomyosin network forms on the cytoplasmic side of the nuclear envelope during prophase. This work explains how the network facilitates chromosome capture and congression by tracking motions of individual kinetochores during early mitosis. The findings can be broadly useful for cell division and the cytoskeletal fields.

Author response:

Thank you for your decision letter with the public review and the recommendations. While we are delighted that the referees feel the work is addressing an outstanding and important issue, they have raised concerns regarding the strength of the support. We will address all the concerns in full in a revised manuscript in the due course. Please find below a couple of general points regarding the referees’ concerns and a proposal as to how we plan to address them.

(1) The idea of the manuscript is to present a plausible solution for a long-standing question in the field of mitochondrial biology and evolution. The fact that the identified solution to the origin of AAC transporters is a remote structural homolog (as you will see in our later detailed response that it is better than any other sequence/structure available till date) is to be expected. If the actual similarities were any better than what we have identified (with a special case of circular permutation), they could have been identified by other simpler structural homology search methodologies.

(2) A recurrent and strong disagreement of the reviewers on the findings presented in this manuscript is rooted on the fact that the structural and sequence relatedness between AAC and CysZ detected in this work are so weak that they can be co-incidental and not an actual evolutionary link. Based on the above, we now searched carefully in all available structural databases such as SCOP, CATH, ECOD etc. whether the above fold link has been noted by others independently. We notice that in the ECOD (Evolutionary Classification of Protein Domains) database only AAC and CysZ are grouped together under a single Possible homology group (X) called ‘Mitochondrial ADP/ATP carrier-like’. The ECOD database contains hierarchical classification of protein domains organized according to their evolutionary relationships and the server is maintained by Prof. Nick Grishin at The University of Texas Southwestern Medical Center.

Link to ECOD database: http://prodata.swmed.edu/ecod/index_af2_pdb.php

Reference: Cheng H, Schaeffer RD, Liao Y, Kinch LN, Pei J, et al. (2014) ECOD: An Evolutionary Classification of Protein Domains. PLOS Computational Biology 10(12): e1003926. https://doi.org/10.1371/journal.pcbi.1003926

Therefore, our study and the independent findings of the ECOD database team together offers greater confidence on the proposed remote evolutionary relationship between AAC and CysZ, and that the structural and sequence similarity we report in the manuscript are not a mere co-incidence. We will also incorporate the details of possible evolutionary relationship between AAC and CysZ identified in the ECOD database in the revised version of manuscript.

(3) One point we would like to stress is that considering all the similarities identified, it very unlikely falls into the class of ‘convergent evolution’. We will make this point explicit in the revised version.

(4) Lastly, while we totally agree that the similarities are in the twilight zone, considering the importance of the problem, we feel that our work would induce researchers from the field of protein design to attempt possible interconversion of the two distantly related transporters thus providing an experimental rationale for the evolution of these transporters.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Renard, Ukrow et al. applied their recently published computational pipeline (CHROMAS) to the skin of Euprymna berryi and Sepia officinalis to track the dynamics of cephalopod chromatophore expansion. By segmenting each chromatophore into radial slices and analyzing the co-expansion of slices across regions of the skin, they inferred the motor control underlying chromatophore groups.

Strengths:

The authors demonstrate that most motor units of cephalopod skin include a subregion of multiple chromatophores, creating "virtual chromatophores" in between the fixed chromatophores. This is an interesting concept that challenges prevailing models of chromatophore organization, and raises interesting possibilities for how chromatophore arrays may be patterned during development.

This study introduces new analyses of cephalopod skin that will be valuable for the quantitative study of cephalopod behavior.

Weaknesses:

The authors chose to image spontaneous skin changes in sedated animals, rather than visually-evoked skin changes in awake, freely-moving animals. Spontaneous chromatophore changes tend to be small shimmers of expansion and contraction, rather than obvious, sizable expansions. This may make it more challenging to distinguish truly co-occurring expansions from background activity. The authors don't provide any raw data (videos) of the skin, so it is difficult to independently assess the robustness of the inferred chromatophore groupings.

The patch-clamp experiments in E. berryi are used to test the validity of their approach for inferring motor units. The stimulations evoke expansions of sub-regions of each chromatophore, creating "virtual chromatophores" as predicted from the behavioral analysis. However, the authors were not able to predict these specific motor units from behavioral analysis before confirming them with patch-clamp, limiting the strength of the validation. It would be informative to quantify the results of the patch-clamp experiments - are the inferred motor units of similar sizes to those predicted from behavior?

The authors report testing multiple experimental conditions (e.g., age, size, behavioral stimuli, sedation, head-fixation, and lighting), but only a small subset of these data are presented. It is difficult to determine which conditions were used for which experiments, and the manuscript would benefit from pooling data from multiple experiments to draw general conclusions about the motor control of cephalopod skin.

The authors use a different clustering algorithm for E. berryi and S. officinalis, but do not discuss why different clustering approaches were required for the two species.

Impact:

The authors use their computational pipeline to generate a number of interesting predictions about chromatophore control, including motor unit size, their spatial distribution within the skin, and the independent control of subregions within individual chromatophores by putatively distinct motor neurons. While these observations are interesting, the current data do not yet fully support them.

The CHROMAS tool is likely to be valuable to the field, given the need for quantitative frameworks in cephalopod biology. The predictions outlined here provide a useful foundation for future experimental investigation.

We thank the reviewer for the thoughtful and detailed evaluation of our work and for recognizing the potential of the CHROMAS pipeline for studying chromatophore control.

We agree that some aspects of the manuscript required clarification and additional explanation, and we have revised the text accordingly. We also now provide access to representative raw video recordings in the Data Availability section. In the E. berryi patch-clamp experiments, single motor neurons evoked expansions of sub-regions of chromatophores, consistent with the “virtual chromatophore” concept. We have now quantified the size of motor units across patch-clamp sessions, and the results show that the inferred motor-unit sizes broadly match those predicted from behavioral recordings, supporting the validity of our approach.

We agree that pooling data across individuals would provide valuable insight into variability across animals. In practice, we recorded chromatophore activity from several animals (14 Euprymna berryi and 12 Sepia officinalis) under different experimental conditions during development of the experimental pipeline. However, acquiring long, stable, artifact-free recordings suitable for motor unit analysis is technically challenging. We now clarify this point in the manuscript. Specifically, we explain that multiple animals were recorded during pipeline development, while the analyses presented focus on recordings with the highest signal quality. We anticipate that the framework introduced here will enable future studies to collect larger datasets and compare motor unit organization across individuals, developmental stages, and species.

HDBSCAN was used for E. berryi during initial exploratory analyses, and Affinity Propagation was adopted for S. officinalis because it better captured the correlation structure of those recordings. We did not re-analyze the E. berryi data with Affinity Propagation, and the implications of algorithm choice are now discussed in the Discussion.

Reviewer #2 (Public review):

Summary:

Overall, this is an excellent paper, making use of a newly developed system for monitoring the behaviour of chromatophores in the skin of (mostly) free-swimming bobtail squid and European cuttlefish. The manuscript is very well-written, clearly presented and very well-structured. The central finding, that individual chromatophores are connected to multiple motor neurones, is not new. Novelty instead comes from the ability to measure the actuation of chromatophore sections across wide areas of skin in free-swimming animals, showing the diversity of local motor units and reinforcing the notion that individual chromatophores are not necessarily the individual units of colour change, but rather local motor units that cover multiple neighbour and near-neighbour chromatophore muscles. This is an excellent finding and one that will shape our understanding of the neural control of cephalopod skin colour.

Strengths:

The methodological approach to collecting large amounts of data about local variations in the expansion of sections of chromatophores is exciting, and the analysis pipeline for clustering sections of chromatophores whose spontaneous activity correlated over time is powerful and exciting.

Weaknesses:

Some minor edits and typographical errors need correcting. I also had some concerns that the preparation for the electrophysiological section of the manuscript complies with the journal's ethical requirements, so I would urge that this be carefully checked.

We thank the reviewer for the positive evaluation of our work and for recognizing the value of the methodological approach and the clarity of the manuscript.

We have carefully reviewed the manuscript and corrected minor typographical errors.

Regarding the ethical considerations raised for the electrophysiological experiments, we have carefully verified that the experimental procedures comply with the journal's ethical requirements and relevant institutional guidelines.

Reviewer #3 (Public review):

Summary:

This study uses high-resolution videography and a custom computer-vision pipeline to dissect the motor control of cephalopod chromatophores in Euprymna berryi and Sepia officinalis. By quantifying anisotropic chromatophore deformations and applying dimensionality reduction methods, the authors infer that individual chromatophores can be a part of multiple motor units. Clustering analyses reveal putative motor units that often span multiple chromatophores, with diverse and overlapping geometries. Chromatophore expansion dynamics are faster and more stereotyped than relaxation, consistent with active neural contraction followed by passive recoil. Together, the results show that chromatophores function not as uniform pixels but as fractionated, coordinately controlled elements that enable flexible pattern generation

Strengths:

The authors present compelling, direct evidence that a). chromatophore deformations are anisotropic, and indirect evidence that b) individual chromatophores can be split across multiple putative motor units. This evidence is provided through data collected over large spatial scales, but also at a sub-chromatophore resolution. This combination of scale and resolution is not possible using traditional neuroanatomical and physiological approaches alone.

The authors also develop a new non-invasive, image analysis approach to extract information about chromatophore deformation across large spatial scales on the organism's body. In principle, this approach is applicable across species and may allow for further comparative characterization of chromatophore motor control. It is therefore a promising new tool and useful resource for the community.

Weaknesses:

An important weakness of the work is that the methods the authors develop can only be applied during resting, spontaneous 'flickering' activity of chromatophores. The inability to reliably apply their technique during any kind of realistic camouflage is a large limitation, as it means this method cannot be used to study the dynamics of motor control during realistic camouflage behaviors.

Another weakness of this paper is the rather limited electrophysiological validation of the computational findings. The authors present only one electrophysiology experiment in E. berryi, the species that they used only for 'methodological development' and not for detailed characterization. A complementary electrophysiological experiment in S. officinalis, or some visualization of neuron morphology confirming that motor neurons do indeed project to multiple chromatophores, would strengthen the generalizability of their computational analysis. This would be particularly pertinent to validate the author's claim that some motor units contain chromatophores that are quite distant from one another on the animal.

Overall, the authors' technical contributions and method development are an important advance. This work serves as an excellent proof of concept that their method can extract useful information about chromatophore motor control. Further validation of their method is needed to fully trust the fine-scale conclusions drawn about the distribution and composition of multi-innervated chromatophores. Furthermore, the authors raise many interesting ideas about developmental constraints on circuit wiring and potential adaptive significance of multi-innervated chromatophores for certain features of camouflage patterning. Their method may be able to help resolve some of these questions in the future if it is refined and applied across developmental stages, regions of the animal, and across species

We thank the reviewer for their thoughtful evaluation and for recognizing the potential of the computational approach introduced in this study.

Regarding the focus on spontaneous chromatophore activity, we have clarified earlier in the Results section why these events are necessary to isolate individual muscle activations. While large camouflage patterns are visually striking, they involve the coordinated activation of many groups of chromatophores by premotor circuits simultaneously, making the identification of individual motor units, our goal here, impossible. Our approach can, however, also be applied during active behavior, including camouflage; the questions addressed there would be different, focusing on how multiple motor units are coordinated to generate the resulting skin patterns, rather than resolving the structure of single motor units. This could be challenging if the patterns of premotor control are highly variable, thus making the detection of meaningful or interpretable motion correlations difficult. This remains to be tested.

We also acknowledge that electrophysiological validation remains limited. Patch-clamp experiments were performed in Euprymna berryi to test predictions generated by the computational analysis, and these experiments confirmed that activation of single motor neurons can produce anisotropic expansion of chromatophore subregions. We now provide the associated datasets in the Data Availability section. We agree that complementary electrophysiological or anatomical experiments in Sepia officinalis would further strengthen the conclusions. Such experiments represent an important direction for future work.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

General points:

(1) Given all the experimental conditions and animals tested, the manuscript would be much stronger if the figures represented pooled data from many animals and experiments (e.g. Figure 1C).

We agree that pooling data from multiple animals would strengthen the manuscript. In practice, we tested these experimental conditions across several animals (14 Euprymna berryi and 12 Sepia officinalis), but we selected the segments shown in the figures for their minimal artifacts and errors. Acquiring high-quality, stable recordings of this type is extremely challenging, and the presented data represents the clearest examples suitable for analysis and visualization. We hope that in the future these methods will enable not only the collection of a larger, high-quality dataset, but also comparisons across individuals, ages, species, and different regions of the mantle.

(2) It's very unclear what animals were used for each experiment:

(a) E. berryi: L677 states that 14 animals were filmed, and L684 implies that non-sedated individuals were used in addition to sedated animals, but it appears all the data is from a single E. berryi with sedation?

The original wording was unclear, so we modified the sentence for clarity. The Methods now specify that 14 animals were filmed to refine the experimental pipeline and explore different conditions, while the data presented in the Results are from a single lightly sedated individual chosen for quality and stability of chromatophore activity.

(b) S. officinalis: L692 onwards states that lots of different conditions and animals were explored, but only minimal data from a couple of animals is described in the figures. L156 states that all (?) the data comes from one head-fixed animal and one sedated and head-fixed animal. L549: The conclusion states that the pipeline was used in freely moving animals, but it appears that all of the S. officinalis were head-fixed? This is very confusing. Rather than describing the conditions of every experiment ever performed, the manuscript would benefit from explicitly stating the experimental conditions used for each figure.

The original text was unclear. We have clarified in the manuscript which animals and experimental conditions were used for the analyses in each figure. To clarify, E. berryi was recorded without head fixation, whereas S. officinalis data were obtained under head-fixed conditions. We did film 11 S. officinalis without head fixation, and data can in principle be extracted from these recordings. Head fixation was used both to minimize visual artifacts and to enable longer, stable recordings, which was important for capturing the highest level of apparent noise in motor unit activation—information that is critical for our analyses of motor-unit organization, though not necessary for studies of broader camouflage patterns. Our computational pipeline enables large-scale analyses that would be very difficult or impossible with traditional electrophysiology, not that all data were acquired from freely behaving animals. While fully unconstrained recordings remain technically challenging due to optical and logistical constraints, we maintain that our approach provides a valid framework for analyzing freely behaving animals.

(c) Additionally, there is a claim that the sedated condition represents the unsedated one (e.g. L151 and L643), but no data is shown to support this. L173 references Figure 6d as evidence, but 6d doesn't exist. Only L210 provides sedation/no sedation statistics for the number of components per motor unit. However, in L643 it says "and motor unit organization remained unchanged". This data needs to be shown to include that statement.

Reference to the inexistant 6d figure was removed. L170 provides statistics for the number of principal components per chromatophore, and L210 provides statistics for the number of components per MU. We do not think a sub-figure is necessary. We, however, agree that L643 “motor unit organisation” is potentially misleading as we only compared the number of chromatophores belonging to a single MU and not the MU shape or distribution. Changed “organization” to “size (in chromatophores)”.

(3) The text needs considerable revision. There are many typos (including multiple instances of "refs" instead of the actual references being inserted). These issues make the manuscript much more difficult to evaluate.

Our apologies. We have now added the missing refs.

(4) It is not clear how convincing the chromatophore groups are. For instance, Figure 4h could alternatively be interpreted as a group of 5 chromatophores in a motor group that happen to co-vary with a sixth one at a great distance. Without seeing some of the raw data (videos), it's difficult to assess how convincing it is that these chromatophores belong to the same group. I recommend analyzing: when multiple chromatophores expand together, what is the likelihood that other chromatophores also happen to expand at the same time (given the frequency that they're all changing shape spontaneously)?

We appreciate the reviewer’s concern. Chromatophores are assigned to the same cluster because their activity, or that of their slices, covaries consistently over time. It is, of course, possible that what appears as a single motor unit may reflect two or more motor neurons acting simultaneously during the recording. Longer video segments increase confidence in the integrity of inferred motor units, but in the absence of a ground truth for motor unit spatial organization in this species at this age, it is difficult to quantify the likelihood that two motor units are being conflated. Raw video data is provided in the Data Availability section. We note, however, that most of the time motor units cannot be readily discerned by eye, because individual chromatophores and their constituent slices fluctuate continuously, and motor-unit correlations are subtle and distributed across multiple chromatophores.

(5) The rationale for focusing on spontaneous activity is introduced relatively late in the manuscript and would benefit from being stated earlier. Examples should be provided of what this looks like (as opposed to regular chromatophore expansion). It would be valuable to see measurements across many experiments of how expanded the chromatophores are - what is the change in surface area? And what is the frequency of expansion for each chromatophore?

Thank you for the remark. This is true. We have added a paragraph at the beginning of the Results section to clarify the rationale for focusing on spontaneous activity.

This section now reads:

“Because our primary aim was to describe the composition and coordination of chromatophore motor units, it was important to examine animals in the absence of the descending commands that occur during active behavior. Spontaneous activity, typically mild and “noisy” was thus ideal to enable measurements of the motion correlations between chromatophores that reflected shared motor neuron drive, rather than shared correlations due to upstream motor neuron groupings by premotor circuits.”

We added an example of video recording of spontaneous activity in our Data Availability section.

While quantifying expansion magnitude and frequency across experiments would indeed be valuable, these questions fall outside the primary focus of the present study, which centers on resolving motor unit organization. In the section “Dynamics of chromatophore expansion and contraction,” we analyze the speed of expansion and contraction to demonstrate that such kinetic features can be reliably detected with the temporal resolution of our video imaging approach. By isolating single muscle activations, we establish a methodological framework that can be used in future work to quantify expansion amplitude, rate of change and frequency across preparations.

(6) Chromatophore expansion was only measured in anesthetized E. berryi, and L679 states that chromatophore expansion was triggered by shining light on the skin. However, light-mediated chromatophore expansion may be mediated by a different mechanism, so chromatophore correlations do not necessarily reflect the underlying motor control.

We agree that there is, in principle, a theoretical risk of direct light-mediated activation of chromatophores. Yet, the kinetics of this light mediated activation are very different, and are the object of a separate, on-going investigation by our groups. In our experiments, the illumination was applied to the whole animal rather than locally to the skin, ensuring that all chromatophores and the eyes were exposed to the same light source. By transitioning from darkness to light, we created a window in which chromatophores were partially expanded—both fully contracted and fully expanded states would show little to no decorrelation. Within this window, we observed spontaneous fluctuations in chromatophore activity, which formed the basis for our correlation analyses. To our knowledge, direct light-mediated expansion of chromatophores has not been reported in E. berryi although it may exist there. Finally, the size, shape, and orientation of the inferred motor units align with electrophysiological evidence, supporting the validity of our motor unit inferences.

(7) Some figures might be better suited for the supplement. For instance, it's not clear what the significance of Figure 5 is (it's not currently sufficiently justified in the text).

We have clarified the purpose of Fig. 5 in both the Results and Discussion sections. In the Results, we now explain that events are separated by amplitude to show that expansion–contraction kinetics can be reliably measured across a full range of chromatophore events, validating the precision of our videographic approach. In the Discussion, we highlight that this precision allows measurement of radial muscle speeds and opens avenues to study chromatophore biomechanics, including the contributions of intertwined forces such as radial muscles, elastic pigment sacs, and intercellular coupling.

(8) Multiple chromatophores can belong to multiple clusters - this study reveals that this is because subsections of a chromatophore are controlled separately. But do the same sections (slices) of chromatophores ever belong to multiple clusters?

Yes, it is possible. Dubas (1985) used videographic recordings to show that the same chromatophore muscle fibers could be activated by stimulation of different nerve bundles, supporting Florey’s (1969) electrophysiological evidence for polyneuronal excitatory innervation. From Dubas: "Usually, different muscle fibres were recruited by each nerve but sometimes a single muscle fibre responded to stimulation of each nerve. Variations of the stimulus voltage also produced gradation of the amplitude of shortening of individual muscle fibres. This supports the evidence above for multiple innervation of single muscle fibres."

The petal-like distribution of motor-neuron influence shows overlapping territories, suggesting that some chromatophore sections may be influenced by multiple neurons. However, this overlap could arise from polyinnervation of individual muscles, the presence of gap junctions between muscles, or passive mechanical coupling due to the elastic properties of the pigment sac.

The petal-like distribution of motor-neuron influence shows overlapping territories, suggesting that some chromatophore sections may be influenced by multiple neurons. However, this overlap could arise from polyinnervation of individual muscles, the presence of gap junctions between muscles, or passive mechanical coupling due to the elastic properties of the pigment sac.

With the present approach, it is not possible to disentangle the relative contributions of these mechanisms, which will require targeted physiological or anatomical experiments. For this reason, we adopted a hard clustering approach for individual chromatophore slices.

(9) All time should be labeled in seconds, not in frames, and all distances should be measured in um or mm, not in pixels.

We chose to present figures in pixels and frames to reflect the native units of our recordings and analyses, which preserves fidelity and reproducibility of the computational pipeline. For biological interpretation, corresponding values are converted to µm in the main text, providing the relevant real-world scale. A scale for conversion is provided in the figure legend.

Specific comments:

(1) L36: I'm not sure the description of virtual chromatophores here is clear enough to make sense to a more general audience.

Addressed. We retained the concept of ‘virtual chromatophores’ in the abstract and added a brief clarifying phrase to indicate that these are functional groupings of adjacent chromatophore territories that act as single units.

(2) L50: "Rimmed by" - consider rephrasing.

Addressed. Replaced with “surrounded”.

(3) L64: "refs" - actual references aren't inserted. There are multiple other examples of this.

Addressed. Added missing references.

(4) L100: This section could use rewriting. Some of the text reads more like a figure legend.

Addressed. We have streamlined the main text to reduce redundancy with the figure legend.

(5) L101: Consider the opening sentence/s providing a more general introduction to the question and approach.

Addressed.

(6) L104: This implies that the data presented are from 14 animals of many ages. This is only relevant if the pooled data is analyzed and presented.

We agree that the original phrasing was ambiguous. We have modified the sentence for clarity, and explain in the Methods that 14 animals were filmed to refine the pipeline and explore experimental conditions, while the analyses shown are from a single animal.

(7) L111: HDBSCAN should be defined.

Addressed. The acronym has been expanded.

(8) L173: Figure 6D doesn't exist.

Addressed. Reference to the inexistent 6d figure was removed.

(9) L193: "excluding negative (contraction) phases" This phrase requires clarification.

Addressed. Added “see Methods” in the legend and added clarification on the reasoning in Methods.

(10) L204: Should explain why the switch to affinity-propagation clustering was made when a different method was used for E. berryi.

Addressed in discussion.

(11) Figure 3: I recommend including a diagram or image of a whole cuttlefish and showing what the corresponding imaging area was in relation to the animal so the reader gets an intuitive sense of scale.

Thank you. We have added a supplementary figure to give the reader a sense of scale.

(12) L221/Fig 3b: These colors are supposed to represent clusters of 3 to 5 chromatophores? The clusters look much bigger.

The figure shows clusters of 3 to 5 chromatophores, but many adjacent clusters were assigned the same color. We have changed the colors to remove this ambiguity.

(13) Figure 3c: This would be more powerful if it represented the combined data of many experiments to draw a general conclusion. Also, shouldn't these cluster sizes match those in 2e, e.g. they get as big as 40?

We assume the reviewer is referring to a comparison between Figures 3c and 2e. For visualization purposes, the graph in 3c was truncated to display over 90% of the data, which explains why the largest clusters appear smaller than in 2e. We modified the legend accordingly. We agree that the results would be strengthened by pooling data from additional experiments; however, acquiring high-quality, artifact-free recordings suitable for motor unit analysis is extremely challenging. We hope that our framework will enable future studies to extend this analysis.

(14) Figure 4: I would show some of these examples earlier, to give the reader an intuitive sense of the data and claims (though it doesn't need its own figure - provide a couple of examples, and the diagram of how much of the mantle you're sampling) then put the rest in the supplement, and include some videos too.

We agree that providing spatial context is important for readers to develop an intuitive understanding of the dataset. However, introducing examples of motor units earlier in the manuscript would, in our view, interrupt the logical progression of the Results, where motor unit identification builds on prior analyses. To address the reviewer’s concern, we have added a new supplementary figure (Fig. S1) illustrating the size and location of the sampled mantle region. In addition, we now provide representative videos in the Data Availability section to give readers direct visual access to the underlying dynamics.

(15) Figure 4f: Is the location of the split color in each dot accurate? It's surprising that each one is split down the middle, and the pink side is always on the right - this is unintuitive given where the motor neuron is likely to be located.

The dots and half dots represent the membership of a chromatophore to a particular cluster.

(16) Figure 5: I didn't find this figure sufficiently justified in the text. I would move this to the supplement.

Addressed in General point #7.

(17) L350: States that 12 animals were patched, but the data isn't shown. It's important to show all of this data (some of which can be in the supplement).

Addressed. We provided the data in the Data Availability Section.

(18) Figure 5: I would quantify how many chromatophores were in each motor group across all the recording sessions, and compare this to the equivalent behavioral analysis.

We assume the reviewer means Fig. 6. We calculated and stated the size of motor units across patching sessions.

(19) Figure 5c: I recommend labeling each panel with a different number so you can refer to specific data.

We assume the reviewer means Fig. 6c. We consider the figure layout clear enough to allow readers to follow the data without additional panel numbers.

(20) L379: Typo: repeat of "quantitative"

Addressed.

(21) L576: Salinity should be 33-36 ppt, not %

Addressed.

(22) L877: The salinity units are sg? That should be stated. Though I would use the same units for salinity throughout.

Addressed.

Overall, this work introduces a potentially valuable quantitative framework for studying chromatophore dynamics. Addressing the points above would substantially strengthen the manuscript and clarify the scope and support for its conclusions.

We thank the reviewer for these many helpful comments.

Reviewer #2 (Recommendations for the authors):

(1) Line 64 - missing references for chromatophore colour with age.

Addressed. Added missing refs.

(2) Line 64-65 - would be good to have a little more detail about what is meant by 'migrating through the skin'. Is this a lateral process, or depth in the skin?

Addressed. Changed “migrating in the thickness..” with “through the thickness..” to emphasize verticality.

(3) Line 72 - typo, should read '...individual and groups...'

Addressed.

(4) Remove 'In Fig 1, ...' from line 104.

Addressed.

(5) Figure 1 - It's unclear why some chromatophores are uncoloured with a red dot in the centre. Are these chromatophores that do not share a cluster with neighbours? If so, wouldn't it make more sense to colour the chromatophore with a unique colour of its own? Or, at the very least, make a note in the caption to indicate that all white chromatophores are not clustered with neighbours.

Segmented chromatophores are shown in white, with coloured slices highlighting cluster membership. Uncoloured slices represent outliers. Addressed in the figure legend.

(6) Line 119 - the concept of a 'closed virtual chromatophore' needs a few more words of explanation. The way I interpret the text as it is, is that the motor units driving colour change are not necessarily the individual chromatophores, but a motor region containing a mixture of whole and partial chromatophores innervated by the same motor neuron. If this is the case, a few extra words of description would help here to remove any ambiguity as I think this is an important concept for the paper.

Addressed. We added a sentence clarifying the concept.

(7) Line 173 - Figure 6d doesn't exist in the paper. Was a different panel intended? If so, please make sure to number the figures in order of appearance in the manuscript.

Reference to the inexistent figure 6d was removed.

(8) Figure 3b is very difficult to see. Perhaps consider lightening the background image. Please also indicate whether the individual colours refer to individual clusters. If this is the case, then some of these clusters look much larger than the 3-5 suggested in the caption.

This issue has been corrected.

(9) Line 210 - remove the bold type.

Addressed.

(10) Line 211 - please specify which 'two groups' you are referring to here. Presumably, this is anaesthetised and non-anaesthetised.

Addressed.

(11) I think that the text is missing any indication of the pixel sizes involved in extracting slice metrics, particularly from the S. officinalis data. It would be great to include some data on how many pixels span the radius of an expanded chromatophore. There is some small indication of this in Figure 2a, but a panel or two with details about the pixel size of S. officinalis chromatophores and their slices would be welcome. This would help with the judgment of the robustness of the resolution of the analysis. Looking at the y-axis in Figure 5a, there is some indication that the chromatophore radius is only 1 to 8 pixels. Is this the case?

Figure 5a doesn’t show chromatophore radius but instead the relative change in peak amplitude during an expansion event. At that point the chromatophore has likely a larger radius as you sum the baseline radius of the chromatophore + the size of the peak.

(12) Line 246-7 - reword this sentence to avoid referring to Figure 3d in the narrative. Include it in parentheses instead.

Addressed.

(13) Lines 408 and 409 - missing references.

Addressed.

(14) Line 576 - salinity should be reported in parts per thousand, not per cent.

Addressed.

(15) Line 593 - how were animals <50mm fed?

Animals smaller than 50 mm were fed Neomysis spp. or small Palaemonetes spp., as noted a few lines above the description for animals larger than 50 mm.

(16) Line 847 - typo - '...putative motor units' ramifications...'

Addressed.

(17) Line 854 - better to write out the [chrom_id, label] info as narrative text rather than using the variable names.

Addressed.

(18) Line 876 - two typos '...were reared in an artificial...'

Addressed.

(19) Line 877 - please use the same salinity metric as used in the earlier part of the methods.

Addressed.

(20) Section 898-910 - equipment details would ideally include the location of the company. E.g. (BX51W1, Olympus, Tokyo, Japan).

Addressed.

Reviewer #3 (Recommendations for the authors):

I am left with a number of questions that arise from the authors' work, some of which the authors themselves briefly mention in the technical limitations section.

(1) In relation to the first weakness, do the authors know if the recruitment patterns they identify are likely to be the same when octopi perform visually-mediated camouflage to their environment?

Thank you for this comment. We assume the reviewer is referring to S. officinalis. There seems to be a misunderstanding: our approach is designed to reveal the smallest independent functional units—motor units—that together generate skin patterns. The technique is fully applicable to an animal displaying camouflage, but the results would necessarily differ. Camouflage patterns are composed of relatively large shapes compared to individual motor units and arise from the coordinated activation of multiple units. Disentangling motor units requires decorrelated activity, whereas visually-evoked camouflage inherently drives correlated motor-unit activation by premotor control. To use an analogy, if our goal were to map the distribution and wiring of pixels on a screen, it would be more informative to broadcast a noise signal rather than display coherent images, as the noise produces decorrelated activity that allows the underlying structure to be resolved. We have clarified this important point in the early results section.

(2) The authors provide indirect evidence that motor neurons innervate multiple chromatophores. Can sets of radial muscles within a chromatophore be innervated by multiple motor neurons? Is there neuroanatomical evidence or experiments that could perhaps shed light on this?

Addressed above. Same question as #1(8).

(3) Are multi-innervated chromatophores evenly distributed across the octopus's body? For instance, could the authors compare chromatophore recruitment over multiple patches on the animal from multiple regions?

At present, we do not have sufficient data to quantitatively compare motor-unit structure or the distribution of multi-innervated chromatophores across different body regions of cuttlefish. However, we would not necessarily expect uniformity across the skin, as distinct body regions are associated with characteristic pattern elements (e.g., the white square on the central mantle or the thicker zebra stripes along the sides). It is therefore plausible that different motor-unit geometries and densities are differentially represented across regions to support these region-specific patterns. Future recordings spanning multiple patches and body locations will be required to test this question directly.

(4) Relatedly, is there any idea of whether chromatophore size or age corresponds with the number of motor units within a single chromatophore?

At present, our analyses are limited to single developmental time points, and we therefore cannot directly assess whether chromatophore size or age correlates with the number of motor neurons innervating an individual chromatophore. However, this is a question that our analysis framework is explicitly designed to address. Our custom pipeline, CHROMAS, (Ukrow, Renard et al., 2025) includes tools for longitudinal image alignment that allow chromatophores to be tracked within the same animal across development. Applying these scripts to developmental datasets enables future analyses linking chromatophore growth or age to changes in the motor innervation of single chromatophores.

I understand that a full resolution to the issues raised above may require substantial additional experiments. At a minimum, further discussion of these points with integration of existing literature would elevate the paper.

Author response:

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

Reviewer #1 (Public review):

(1) The rationale behind averaging sentence embeddings across multiple transformer models (with different architectures and training objectives) is unclear. These transformer-based models have different training paradigms and model architectures, which may result in misaligned semantic spaces. The averaging operation may dilute the distinct sentence representations learned by each model, potentially weakening the overall semantic encoding for sentences. Please clarify this choice or cite supporting methodology.

The reviewer questions the rationale for averaging sentence embeddings across different models. However, our method involves computing correlations separately for each model, then averaging the correlations. We apologize for the confusion. We have clarified this on page 3:

“Results for the ‘Transformers’ model are computed by computing correlations separately for five different transformer models and then taking a simple average of these correlations. Results for each individual transformer are presented in Supplementary Information Figure S2.”

(2) All structure-sensitive models discussed incorporate semantics to some extent. Including a purely syntactic baseline, such as a model based on context-free grammar, would help confirm the importance of syntactic structures.

Following the suggestion, we have implemented two syntactic models and discuss the results on page 10:

“We also found that purely syntactic models based on constituency parses (see Benepar and CFG) show poor correlations with brain activity (see Supplementary Information Figure S2). Examining the corresponding RSA matrices (see Figure S1), this seems to be due to such models being overly sensitive to syntactic form, and relatively insensitive to which words are assigned to different nodes within the syntactic tree. This is most evident for the edit-distance similarity metric, and to a lesser extent also for the subtree similarity metric. This finding highlights the value of hybrid approaches designed to appropriately balance sensitivity to lexical, syntactic, and compositional information in representing semantic information at the sentence level.”

(3) In Figure 2, human behavioral judgments show weak correlations with neural data, and even fall below those of computational models, suggesting the behavioral judgments may not reflect the sentence structures in a brain-like way. This discrepancy between behavioral and neural data should be clarified, as it affects the interpretation of the results.

While the behavioural judgements are made by different participants and involve a different task than the neuroimaging results, nonetheless we agree the difference is surprising and warrants more detailed consideration. We have included a more detailed discussion of this issue on page 11:

“Our study has several limitations. First, we found a surprisingly low correlation between behavioural ratings and brain activations (see Figure 2). This may be partly explained by differences in task structure. In the behavioural experiment, participants viewed many pairs of related sentences, and were explicitly asked to pay attention to differences in the words of each sentence. In contrast, in the fMRI task, participants read one sentence at a time without an explicit comparison. In addition, we suspect that presentation of so many sentence pairs with highly similar structures may have biased the way in which participants rated sentence similarity. Modifications to the behavioural task to mitigate these aspects may reduce the divergence between behavioural and brain findings.”

(4) To better contextualize model and neural performance, sentence similarity should be anchored to a notion of semantic "ground truth", such as the matrix shown in Figure 1a. Comparing this reference with human judgments, brain responses, and model similarities would help establish an upper bound.

While our design matrix served as the basis for constructing a set of stimuli with systematic modifications, we respectfully suggest that it should not be regarded as a ‘semantic ground truth’. Sentence pairs within each category will not have the same degrees of semantic similarity since the words and context differ across sentences in a graded manner. Furthermore, while we anticipated ‘different’ sentence pairs would be less similar than ‘swapped’ sentence pairs, and that within each of the six block diagonals the ‘modified’ or ‘substituted’ sentence pairs would be the most similar, we did not have any prediction about the magnitude of these differences. Our goal was to construct a set of sentence pairs which spanned a range of semantic similarities, and allowed for dissociation between lexical similarity and overall similarity in meaning. The design matrix is not intended to represent a ‘ground truth’ that human judgements or brain representations would be expected to conform with.

(5) The structure of this paper is confusing. For instance, Figure 5 is cited early but appears much later. Reordering sections and figures would enhance readability.

We agree that placement of figures was not ideal in the previous draft. We have reworked the manuscript so that all figures appear closer to their mention in the text, and the figure (now Figure 3) appears in the correct order. We have also substantially revised the discussion, and included subheadings to help guide the reader through the various different issues we include.

(6) While the analysis is broad and comprehensive, it lacks depth in some respects. For instance, it remains unclear what specific insights are gained from comparing across brain regions (e.g., whole brain, language network, and other subregions). Similarly, the results of simple-average and group-average RSA appear quite similar and may not advance the interpretation.

We included both analyses in line with our preregistration, and also because we believe the fact that two distinct approaches to analyzing the data yield similar results strengthens our conclusions.

(7) While explaining the grid-like pattern due to sentence length is important, this part feels somewhat disconnected from the central question of this paper (word order). It might be better placed in supplementary material.

We believe that the grid-like pattern in the RSA results is an important unexpected finding that warrants discussion in the main manuscript.

Reviewer #1 (Recommendations for the authors):

(1) Consider including a purely syntactic baseline model. For instance, parse each sentence into a constituency tree and compute tree edit distances between pairs of trees. This would allow you to construct a sentence similarity matrix based solely on syntactic structure, and may clarify the role of syntax in sentence representations.

See our response to Public Review comment 2.

(2) Instead of averaging embeddings across different transformer-based models, I recommend reporting RSA results for each model individually. For instance, compare one sentence-level model (e.g., SentBERT or SimCSE) and one general-purpose language model (e.g., GPT-2 or Llama).

See our response to Public Review comment 1.

(3) I suggest revisiting the structure of the Results section to improve the clarity and impact of your key findings. Consider which results are most central to the paper's claims and ensure they are presented in the main text. Less central analyses (e.g., the analysis on the grid-like pattern) might be better suited for the supplementary information. Presenting behavioral results prior to neuroimaging results could also improve logical flow by first validating model similarity estimates behaviorally.

As mentioned in our response to Public Review comment 5, we have revised the ordering of the figures to improve the flow of the main manuscript. We believe that the grid-like pattern in the RSA results is an important unexpected finding that warrants discussion in the main manuscript. In addition, we believe that presenting the neuroimaging results first is appropriate as this is the primary and most important contribution of our study.

Reviewer #2 (Public review):

(1) The stimuli are not fully controlled for lexical content across conditions. Residual lexical differences between sentences could still influence both brain and model similarity patterns. To more cleanly isolate syntactic effects, it would be useful to systematically vary only a single structural element while keeping all other lexical content constant (e.g., the boy kicked the ball / the ball kicked the boy). It would be better to engage more with the minimal pair paradigm, which is widely used in large language model probing research.

The reviewer rightly argues that our stimuli do not fully control for lexical content across conditions, and that a more appropriate paradigm may be to utilise minimal pairs in which only a single variable of interest (such as sentence structure) is modified. We agree that most of our sentence pairs do not constitute minimal pairs; however, this was not our objective. Our study design aimed to synthesise traditional minimal pair approaches with more recent research paradigms using naturalistic stimuli. As such, we selected stimuli which are more complex and contain more variable features than traditional minimal pair studies, but which also are tailored to highlight differences which are of particular theoretical interest.

Because we are interested in comparing the effects of multiple sentence elements and semantic roles, a systematic pairwise comparison of minimal pairs is not necessarily optimal. Instead, we designed our stimuli to leverage the advantage of fMRI in that we can measure the brain representations corresponding to each sentence, and hence can conduct a full series of pairwise comparisons of sentence representations. We do not claim this approach to be universally superior to a minimal pair approach, but we do believe our novel approach provides additional insights and a new perspective on semantic representation relative to minimal pair studies.

We have added the following paragraph on pages 9-10 contrasting our approach to previous minimal-pair studies:

“Another approach that has seen widespread use is the presentation of minimal sentence pairs that differ only in one specified aspect, for example, interchanging subject and object in a sentence (Frankland 2015, Wang 2016, Frankland 2020, Giglio 2024), or altering adjective-noun phrases to influence composition (Graves 2010, Schell 2017, Fyshe 2019, Ciapparelli 2025). Our approach is an extension of these approaches utilising more naturalistic and complex sentences, designed to facilitate comparison of a wider range of structural manipulations (see Table 1). In more completely characterising the representational structure of various computational models in response to different structural contrasts, we can more comprehensively evaluate their adequacy as models of semantic processing in the brain.”

(2) The comparisons are done across fundamentally different model types, including static embeddings, graph-based parsers, and transformers. The inherent differences in dimensionality and training objectives might make the conclusion drawn from RSA inconclusive. Transformer embeddings typically occupy much higher-dimensional, anisotropic representational spaces, and their similarity structure may reflect richer, more heterogeneous information than models explicitly encoding semantic roles. A lower RSA correlation in this study does not necessarily imply that transformers fail to encode syntactic information; rather, they may represent additional aspects of meaning or context that diverge from the narrow structural contrasts probed here.

The reviewer notes that low RSA correlations do not necessarily imply that transformers fail to encode syntactic information. We acknowledge this in our discussion (page 10), where we also highlight that our focus is not on whether transformers encode such information, but rather what transformer representations can tell us about how sentence structure is represented in the brain. Our results indicate that transformer embeddings do not have the same geometric properties as brain representations of sentence meaning, at least for certain types of sentences where lexical information is insufficient to determine overall meaning.

The reviewer also notes that transformer embeddings are highly anisotropic; however, we adjust for this by normalising each feature as discussed on page 14. Finally, the reviewer notes that the transformers we examine differ in architecture and training objectives. This is not critical for our study because we are not seeking to determine which architecture or training objectives are best. Our goal is simply to compare a range of approaches and see which, if any, have similar sentence representations to those formed by the brain. In fact, our results indicate that architecture and training regime make relatively little difference for our stimuli, as shown by the pattern of results for all models in Figure S2.

(3) The interpretation of the RSA correlation largely depends on the understanding of models. The authors suggest that because hybrid models correlate better than transformers, this implies that transformers are inferior at representing syntax. However, this is not a direct test of syntactic ability. Transformers may encode syntactic information, but it may not be expressed in a way that aligns with the RSA paradigm or the chosen stimuli. RSA does not reveal what the model encodes, and the models might achieve a good correlation for non-syntactic reasons (e.g., length of sentence, orthographic similarity, lexical features).

The reviewer argues that RSA correlations do not measure the extent to which a model encodes syntactic information. This is very similar to the previous point. We do not claim that our results show that transformers do not encode syntactic information. Rather, our claim is that sentence embeddings derived from transformers have different geometric properties to brain representations, and that brain representations are better described by models explicitly representing key semantic roles. From this we conclude that, at least for the sentences we present, the brain is highly sensitive to semantic roles in a way that transformer representations are not (at least to the same extent). We have clarified this in a modified paragraph on page 11:

“We emphasise that our results do not show that transformers fail to represent syntactic or semantic role information. Indeed, large language models show clear capabilities of correctly interpreting sentence structure (Chang 2024), and probing studies have found that transformers represent information about syntax and word order (Clark 2019, Manning 2020). This is consistent with our finding that directly prompting GPT-4 to rate sentence similarity yields very high correlations with human judgements (see Supplementary Information Figure S3). Nonetheless, the fact that transformers can encode and utilise structural information to perform linguistic tasks does not mean that they effectively utilise this information to construct a brain-like representation of sentence meaning.”

We also respectfully disagree with the reviewer’s suggestions that sentence length and orthographic or lexical similarities may drive model correlations with brain activity. As we discuss on page 19, we explicitly control for differences in sentence length when computing correlations. Our process for constructing our sentence set also controls for lexical similarity by generating pairs of sentences with all or mostly the same words but different orderings. We did not explicitly address orthographic similarity, but this will be strongly correlated with lexical similarity.

Reviewer #2 (Recommendations for the authors):

(1) Model dimensionality: the interpretability of cosine similarity diminishes as the dimensionality increases, and there are some math tricks to work around it. To make a fair comparison among models with different dimensionalities, it would be better to apply some dimensionality-insensitive distance metrics.

We thank the reviewer for this suggestion. We repeated all vector-based similarity calculations using the Dimension Insensitive Euclidean Metric (DIEM). As shown in Figure S9, the results are broadly similar, though with overall somewhat lower brain correlations for most transformers compared to cosine similarity.

(2) Depending on the scope of the current study, if the authors would like to establish whether transformers are inferior to graph-based models in representing syntax, a linear classifier using the model embeddings would be sufficient. I think this would be a more direct assessment of model syntax ability than correlation with brain data.

As we discuss in our previous responses, our objective in this study was not to assess how well transformers can represent syntax. Rather, the goal was to assess whether internal transformer representations have similar geometric properties to patterns of brain activation. Our results indicate that transformers do represent sentence structure, but in a different manner to the human brain.

Reviewer #3 (Public review):

(1) The interpretation of findings is nuanced. Although Transformers underperform as brain models on the critical subsets of controlled sentences, a Transformer outperforms all other models when evaluated on the union of all sentences when both word-level content and structure vary. Transformers also yield equivalent or better models of human behavioral data. Thus, although Transformers have demonstrable flaws as human models, which are pinpointed here, in the general case, (some) Transformers are more human-like than the other models considered.

The reviewer argues that we overstate some of our conclusions, as several transformers achieve higher brain correlations than the hybrid model when computed over all sentence pairs, as well as on the behavioural data. In response, we first note that our primary interest in this paper is on the block diagonal sentence pairs, as these were specifically designed to interrogate how different models represent sentence structure. The comparison with all sentence pairs is presented for comparison but is not our primary focus on this paper, as also reflected in the pre-registered prediction that our VerbNet-CN hybrid model would show higher brain correlations than transformers over this block diagonal subset.

Second, we have included a new analysis in the revised manuscript (Figure S9) where we compute brain correlations controlling for the pattern of similarities observed in the primary visual cortex (averaged over participants), as a way to control for visual similarity. This added control substantially reduces the brain correlations of the transformers, such that they all have lower correlations than VerbNet-CN and AMR-smatch even over the set of all sentence pairs. We provide interpretation of this result in the discussion.

Third, we would like to note one of the disadvantages of transformers as a model of mind or brain representations is that they are largely a ‘black box’ whose workings are poorly understood. One advantage of hybrid models like our simple semantic role model is that they can be much easier to interpret, thereby enabling them to be used to determine which features are most important for brain representations of sentence meaning, and what mechanisms are used to combine individual words into a full sentence. Given their relative simplicity and interpretability, we believe hybrid models have considerable value as scientific tools, even in cases where they achieve comparable correlations to transformers. We have added a short discussion of this issue in the revised manuscript (page 10).

(2) There may be confounds between the critical sentence structure manipulations and visual representations of sentence stimuli. This is inconvenient because activation in brain regions that process semantics tends to partially correlate with visual cortex representations, and computational models tend to reflect the number of words/tokens/elements in sentences. Although the study commendably controls for confounds associated with sentence length, there could still be residual effects that remain. For instance, the Graph model correlates most strongly with the visual cortex despite these sentence length controls.

We agree with the reviewer that this is a potential confound. As noted in the previous response, we have implemented a new control analysis in which we directly control for visual similarities as reflected in participant-averaged similarities of primary visual cortex activations in response to all stimuli. These results are shown in Figures S8-S11 in the SI. We show that transformer correlations are reduced much more than graph and hybrid models with this control. Also, we note that the AMR-smatch graph model shows high correlations with other brain regions even after removing correlations with the visual cortex (Figure S10). This indicates that the model represents a range of sentence features, including both superficial visual or length-related features, as well as semantic features that are represented in common with language and other cortical regions.

(3) Sentence similarity computations are emphasized as the basis for unifying comparative analyses of graph structures and vector data. A strength of this approach is that correlation is not always the ideal similarity metric. However, a weakness is that similarity computations are not unified across models. This has practical consequences here because different similarity metrics applied to the same model produce positive or negative correlations with brain data.

The reviewer notes that the method for computing similarities differs between the vector-based (mean and transformer) models, and the hybrid and syntax-based models, thereby potentially adding an additional confound to our results. We agree that this is a potential limitation, and our correlations should always be understood as applying to a model paired with a similarity metric. However, we believe that this is mostly unavoidable when comparing different formalisms. In the revised manuscript we have incorporated an entirely new similarity metric for vector-based models (DIEM similarity), as well as an extended discussion of the effect of different similarity metrics for graph and hybrid models.

Reviewer #3 (Recommendations for the authors):

(1) Compute separate RSAs on each sentence pair type (especially Swapped), to quantify how each sentence type manipulation contributed to the divergence between model and brain. Although the manuscript is already brimming with analyses, I think squeezing this in would be helpful because the results currently rely on qualitative inspection of group-average scatter plots to interpret how sentence pair manipulations contributed to the divergence between Transformers and humans. The Swapped condition would appear to be the centrepiece of the title and manuscript, and potentially the only condition for which confounds associated with the surface form of sentence are controlled for (because sentences should be the same words in different orders). Thus, this analysis might see to the inconvenient visual cortex correlations in Figures 3d/e.

We respectfully disagree that computing separate RSA for each sentence pair type would be a useful additional analysis. The motivation for the construction of our stimulus set was to provide a range of variants of a given base sentence that alter the semantic meaning and lexical content (somewhat) independently. The purpose of the ‘modified’ sentences, for instance, is to construct sentences with a similar overall meaning but lower lexical similarity due to the inclusion of many modifier words. It is precisely the comparisons across the different pair types that provide information about how each model represents sentence semantics, so restricting an analysis to only a single subset would not be very informative. Another problem with this approach is that it would dramatically reduce the number of sentence pairs analysed, thereby decreasing statistical power. In the revised manuscript we have provided additional details regarding the motivation and rationale for how our stimulus set of 108 sentences was constructed, which should help to elucidate this point more clearly. The following excerpt is from page 3:

“Within each of the six subsets, we begin with a base sentence such as `the cameraman brought the equipment to the director', which we then systematically modified in various ways to create different combinations of lexical and compositional similarity, in order to dissociate these two aspects of meaning (see Table 1 for further details).”

(2) Explaining the motivation for the sentence stimulus types. I appreciated the careful design of the dataset, but I couldn't immediately work out the motivation for all the different sentence types, and why this selection was ideal to identify divergences with Transformers. For instance, given the goal of (approximately) controlling for lexical similarity whilst varying sentence meaning, I couldn't immediately see why stimulus blocks weren't all built from rearranging the same content words (as in the Swapped condition). The negative RSA correlation with the Mean model also made me stop and think - it seems like the more similar the words in a sentence, the more different their structure, and vice versa, but I wasn't clear that this was a design feature. Thus, a few extra words motivating the conditions could be helpful for the reader, and these might helpfully lead them to anticipate the negative RSA correlation.

As noted in the previous response, in the revised manuscript we have expanded our explanation of the rationale for the construction of our 108 sentences. In particular, Table 1 in the methods section now includes two additional columns which summarise the intended combinations of lexical and overall sentence similarity which our sentence pairs are intended to satisfy.

(3) Explanation for why different implementations and similarity computations between variants of ostensibly equivalent Graph / Hybrid models yielded widely divergent positive vs negative brain correlations, despite both positively capturing behavioural ratings. This might incorporate a brief intuitive explanation of how Graph model similarities were computed (e.g., what SMATCH and WWLK do). In light of the above, why do different similarity algorithms applied to the Graph model yield positive and negative correlations on the same brain (e.g., Figure S2 - Graph / Graph-WL a,b, diag-pairs). Same goes for why Hybrid and Hybrid-AMR yielded positive vs negative correlations (e.g., Figure S2 - Graph / Graph-WL a,b, diag-pairs). Acknowledge that the brain results are sensitive to similarity computations in the Discussion.

We appreciate this suggestion. We have added an extended consideration of these issues to the discussion (pages 10-11), as well as some additional details regarding the differences between the Smatch and WWLK metrics in the methods section (page 17).

(4) Acknowledgement and explanation of why the human similarity ratings were poor at explaining brain data in Figure 2a,b (right column diag-pairs). The poor behaviour vs brain match is indirectly implied in the Discussion as "the comparison between behavioural and fMRI data is somewhat difficult owing to the difference in task structure." However, I would suggest being upfront and explicitly mentioning and explaining the poor brain match in Figures 2a and b, because the reader will notice and wonder - especially because the models correlate strongly with the behavioural data without the models doing the human behavioral task (though this could be a possibility, see later).’

As suggested, we have included a passing reference to this in the presentation of our main results in page 5, and a lengthier discussion on page 11:

“Our study has several limitations. First, we found a surprisingly low correlation between behavioural ratings and brain activations (see Figure 2). This may be partly explained by differences in task structure. In the behavioural experiment, participants viewed many pairs of related sentences, and were explicitly asked to pay attention to differences in the words of each sentence. In contrast, in the fMRI task participants (who were not the same as the behavioural task participants) read one sentence at a time without an explicit comparison. In addition, we suspect that presentation of so many sentence pairs with highly similar structures may have biased the way in which participants rated sentence similarity. Modifications to the behavioural task to mitigate these aspects may reduce the divergence between behavioural and brain findings.”

(5) Brief explanation of why model vs brain correlations tended to be strongest in the visual cortex (Figure 3d,e). Currently, this issue is only mentioned in passing, however, it seems worthy of further comment.

We appreciate the reviewer for highlighting this issue. We have added discussion of the potential for visual confounds to several points in the revised manuscript, including the ‘Neuroscience of semantics’ subsection on page 11. As noted, we have also added a new analysis in which we compute correlations controlling for the average RSA similarities of the primary visual cortex. We find that this additional control significantly reduces correlations for most transformer models, but only has a more modest reduction on the correlations for most of the graph and hybrid models, particularly VerbNet-CN (see Figures S8-S11).

(6) Softening/clarifying some statements that could be misconstrued as suggesting Transformers were universally inferior models. Statements made in the Abstract/Discussion initially came over to me as implying that Transformers were universally inferior models when compared to the Graph/Hybrid models - but this appears only to be true when one looks at analyses conducted within block diagonal sentence subsets. Otherwise, when analyses are conducted on all sentences (between and within blocks, Figure 5) Llama 3 L2 provides by far the strongest brain model. Transformers also appear to yield the strongest accounts of the behavioural data, whether tested on block diagonal or all sentence pairs (Figure S3). To remedy this, I would suggest softening some statements in the Abstract/Discussion that could be misconstrued as suggesting that Transformers were universally inferior. I would also suggest explicitly acknowledging that when the entire dataset was analyzed, Transformers were most accurate, and that (some) Transformers best accounted for the behavioural data.

We agree that there was some lack of precision in certain sections of the previous draft regarding the conclusions to be drawn regarding the representational capacities of transformers. We have revised the abstract and conclusion to better reflect our intended message, which is that transformers certainly can represent sentence structure and semantic roles, but that the way in which they do this (through vector representations in their hidden layers) is significantly different to how such features are represented in the human brain. In particular, we have included this new text on page 10:

“We emphasise that our results do not show that transformers fail to represent syntactic or semantic role information. Indeed, large language models show clear capabilities of correctly interpreting sentence structure, and probing studies have found that transformers represent information about syntax and word order. This is consistent with our finding that directly prompting GPT-4 to rate sentence similarity yields very high correlations with human judgements (see Figure S3). Nonetheless, the fact that transformers can encode and utilise structural information to perform linguistic tasks does not mean that they effectively utilise this information to construct a brain-like representation of sentence meaning.

(7) Given that GPT-4 was already deployed to parse semantic roles for the hybrid model, and GPT-4 should be able to generate reasonable similarity ratings between sentence pairs, it struck me that an interesting addendum could be to use GPT-4 similarities derived from the human behavioral task to interpret both brain and human behavioral data. This might also help support the case for conducting analyses within a similarity-based framework.

We appreciate this suggestion. We have added this model (GPT-4 ratings of sentence similarity) to the revised manuscript (see Figures S1-S3).

Other changes

As noted by reviewer 3, the full set of sentence pairs was missing from the previous draft. They have been added to the SI of the revised manuscript.

We have renamed the Graph and Hybrid models in the manuscript to AMR-Smatch and Verbnet-CN respectively, for greater clarity as to which models these terms refer to, and also to better differentiate from the newly added constituency parse graph models.

We have thoroughly revised the discussion section, incorporating feedback from all reviewers regarding areas needing additional depth.

We have added subsections to the discussion to aid the reader navigating the now lengthier section.

Author response:

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

Joint Public Review

This manuscript puts forward the provocative idea that a posttranslational feedback loop regulates daily and ultradian rhythms in neuronal excitability. The authors used in vivo long-term tip recordings of the long trichoid sensilla of male hawkmoths to analyze spontaneous spiking activity indicative of the ORNs' endogenous membrane potential oscillations. This firing pattern was disrupted by pharmacological blockade of the Orco receptor. They then use these recordings together with computational modeling to predict that Orco receptor neuron (ORN) activity is required for circadian, not ultradian, firing patterns. Orco did not show a circadian expression pattern in a qPCR experiment, and its conductance was proposed to be regulated by cyclic nucleotide levels. This evidence led the authors to conclude that a post-translational feedback loop (PTFL) clockwork, associated with the ORN plasma membrane, allows for temporal control of pheromone detection via the generation of multi-scale endogenous membrane potential oscillations. The findings will interest researchers in neurophysiology, circadian rhythms, and sensory biology. However, the manuscript has limited experimental evidence to support its central hypothesis and is undermined by several questionable assumptions that underlie their data analysis and model builds, as well as insufficient biological data, including critical controls to validate and/or fully justify the model the authors are proposing.

We thank the reviewers for their thorough and thoughtful comments and believe that the manuscript is much stronger now after the revision which incorporates the requested changes. We added results of new experiments and additional analyses. Although these new insights did not change the previous conclusions, we significantly reworked the Discussion and added further references to clarify the conclusions we want to make.

Please note that we used ORN as acronym for “olfactory receptor neuron” throughout the manuscript. ORNs contain odorant receptors (ORs), and in insects these ORs associate with the olfactory receptor co-receptor (Orco) to be trafficked to the membrane of the cilium of the ORN, where they can be contacted by pheromones and odorants. In Manduca sexta, evidence is accumulating for G-protein coupled metabotropic pheromone transduction and not for OR-Orco dependent ionotropic transduction, as shown for Drosophila melanogaster. In both insect species, besides its chaperone function, Orco can form leaky cation channels, which can regulate the spontaneous spiking activity of ORNs. In this study, we explored this role of Orco.

Strengths:

The study is notable for its combination of long-term in vivo tip recordings with computational modeling, which is technically challenging and adds weight to the authors' claims. The link between Orco, cyclic nucleotides, and circadian regulation is potentially important for sensory neuroscience, and the modeling framework itself - a stochastic Hodgkin-Huxley formulation that explicitly incorporates channel noise - is a solid and forward-looking contribution. Together, these elements make the study conceptually bold and of clear interest to circadian and olfactory biologists.

Major weaknesses:

At the same time, several limitations temper the conclusions. The pharmacological evidence relies on a single antagonist and concentration, without key controls. The circadian analysis is based on relatively small numbers of neurons, with rhythms detected only in subsets, and the alignment procedure used in constant darkness raises concerns of bias. The molecular evidence is sparse, with only three qPCR timepoints, and the model, while creative, rests on assumptions that are not yet fully supported by in vivo data.

Please see our responses to the detailed comments.

Detailed comments are provided below:

(1) The role for Orco proposed in the authors' model largely stems from the effects seen following the administration of (a single dose) of the Orco antagonist, OLC15. However, this hypothesis is undercut by the lack of adequate pharmacological controls, including a basic multipoint OLC15 dose-response series in addition to the administration of blockers for the other channels that are embedded in their model, but which were ruled out as being involved in the modulation of biological rhythms. In addition, these studies would (ideally) also benefit from the inclusion of the same concentration (series) of an inactive OLC15 analog to better control for off-target effects.

The Orco agonist VUAA1 (Jones et al., 2011) binds directly to Orco and increases the channel open time probability. In M. sexta hawkmoths, we have already published that VUAA 1 increases the low spontaneous activity of ORNs in a dose-dependent fashion (Nolte et al., 2013). Chen and Luetje (2012) systematically varied the chemical structure of VUAA1 to identify new Orco ligands and discovered 22 Orco ligand candidates (OLCs) that either activated or inhibited Orco. In their heterologous expression system, Orco was most sensitive to inhibition by OLC15. Based on these results, we published a dose-response curve of OLC15 inhibition (1-100 µM) using in vivo tip recordings of pheromone-sensitive long trichoid sensilla of M. sexta (Nolte et al., 2016). There, we also demonstrated that OLC15 dose-dependently antagonizes the VUAA1-dependent activation of Orco.

Furthermore, we tested other published Orco antagonists, which were characterized in heterologous assays, in primary cell cultures of hawkmoth ORNs, as well as in in vivo assays in intact hawkmoths. We focused on amiloride-derived antagonists, because we previously identified an amiloride-sensitive cation channel in hawkmoth ORNs. We found that, in contrast to OLC15, the amilorides HMA and MIA were not Orco-specific antagonists but instead affected different ion channel targets depending on the time of day (Nolte et al., 2016). Based on those experiments and the dose-response curves we determined that the Orco agonist VUAA1 (Jones et al., 2011) and the Orco antagonist OLC15 (Chen and Luetje, 2012) worked best in hawkmoth ORNs to target Orco pharmacologically. Due to those results and other comparative tests with other published Orco antagonists we settled since then in all further experiments on a dose of 50 µM OLC15 as most adequate to antagonize Orco functions in Manudca. In the current study, we focus on Orco without excluding the possibility that other ion channels in the ORNs contribute to the control of membrane potential rhythms.

We have clarified the Methods section accordingly.

(2) The expression pattern of Orco was assessed using qPCR at only three timepoints. Rhythmic transcripts can easily be missed with such sparse sampling (Hughes et al., 2017). A minimum of six evenly spaced timepoints across a 24-hour cycle would be required to confidently rule out circadian transcriptional regulation. In addition, the use of the timeless mRNA control from another study is not acceptable. Furthermore, qPCR analysis measures transcript abundance, not transcription, as the authors repeatedly state. Transcriptional studies would require nuclear run-off or, more recently, can be done with snRNAseq analysis. Taken together, these concerns undermine the authors' desire to rule out TTFL-based control that directly led them to implicate a PTTF-based model.

We agree with the referees that more time points and a direct comparison between timeless and Orco mRNA levels should be included in this manuscript. We included these additional qPCR experiments and edited the manuscript to make clear that we measure transcript abundance, but we will not perform snRNAseq analysis due to time- and financial constraints.

(3) The modelling presented is based on Orco as a ZT-dependent conductance tied to the cAMP oscillations that were reported by this group in the cockroach and from the presence and functionality in Manduca of homomeric Orco complexes that are devoid of tuning ORs. While these complexes have been generated in cell culture and other heterologous expression systems, as well as presumably exist in vivo in the Drosophila empty neuron and other tuning OR mutants, there is no evidence that these complexes exist in wild-type Manduca ORNs. While this doesn't necessarily undermine every aspect of their models, the authors should note the presence of Orco/OR complexes rather than Orco homomeric complexes.

Our ELISAs found circadian oscillations in cAMP levels not only in antennae of the Madeira cockroach (Schendzielorz et al., 2014, 2012), but also in hawkmoth antennae (Schendzielorz et al., 2015). For clarification, we added the 2015 citation to the Modeling chapter in the Methods section.

We agree with the referees that we cannot distinguish between Orco homo- and heteromers in the different compartments of our hawkmoth ORNs but we know that both are expressed in the pheromone-sensitive ORNs. Thus, as the referee suggests, we added text regarding the presence and localization of OR-Orco heteromers. Consistent data collected across different experiments (heterologous expression systems, primary cell cultures of hawkmoth ORNs, in vivo/in situ studies) support that Orco homomers are present in hawkmoth ORNs. In addition to co-expression of MsexOrco and MsexSNMP-1 with either MsexOr-1 or MsexOr-4 in a heterologous expression system, MsexOrco expression alone was already sufficient to increase intracellular Ca²⁺ levels spontaneously as a result of its property as leaky, non-specific cation channel, and in response to VUAA1 application (Nolte et al., 2013). Both in developing hawkmoth pupae and differentiating primary cell cultures of hawkmoth ORNs, Orco expression started during a developmental time window where ORNs did not yet express pheromone receptors but where Orco affected spontaneous activity and intracellular Ca²⁺ levels dependent on VUAA1 (Nolte et al., 2016). In vitro patch clamp studies of differentiating cultured hawkmoth ORNs during this time window of pupal development characterized ion channels/currents with properties of Orco as a leaky, non-specific cation channel/current that depends on protein kinase C and cyclic nucleotides (Dolzer et al., 2021, 2008; Krannich and Stengl, 2008; Stengl, 1993). Thus, Orco homomers are present in developing hawkmoth ORNs during a time window where ORNs already express spontaneous activity but they do not heteromerize with pheromone receptors. However, we do not know whether and in what ratio homo- and heteromers of Orco and ORs are present in the respective sensillum compartments of adult hawkmoths because all OR-specific antibodies tested did not work in immunocytochemical studies of hawkmoth antennae (Nolte et al., 2013; Stengl, 1994; Stengl and Hildebrand, 1990). Our hypothesis of differential distribution of Orco homomers in the some and dendrite compartment, and OR-Orco heteromers in the cilia is based on differential immunocytochemical localization of Drosophila ORs mainly in the cilia compartment (Benton et al., 2006).

We clarified our manuscript accordingly.

(4) Some aspects of the authors' models, most notably the decision to phase align/optimize their DD and OLC15 recordings, are likely to bias their interpretations.

It is consensus that insects display daily and circadian rhythms in pheromone-dependent mating, odor-gated feeding, and egg-laying behavior that phase-locks to environmental rhythms, corresponding with daily/circadian rhythms of sensory neuron physiology (e.g., Merlin et al., 2007; Rymer et al., 2007; Schendzielorz et al., 2015, 2012). However, circadian rhythms can be easily masked by stress, like the disturbances during an experimentally very challenging long-term recording experiment over several days. In addition, we observed over the years in our animal raising facility that in 17:7 light-dark cycles the originally nocturnal hawkmoths M. sexta distribute their activity patterns over the course of the day, finding nocturnal as well as diurnal hawkmoths. Thus, light-dark cycles were not enough to ensure phase-synchronized behavioral rhythms, and it is very likely that the nocturnal hawkmoths, next to stress signals, rely heavily on pheromone/odor dependent synchronization as also found in other moth species (Ghosh et al., 2024). Because we focus on spontaneous activity and not on pheromone-dependent physiology in this study, we used isolated males that were never exposed to the female pheromones, taking phase dispersal into account. Therefore, it became necessary in free-running conditions to first determine the respective behavioral rhythm for each animal, and then to phase-align their activity patterns to allow for statistical analysis. Otherwise, circadian differences would average out in a phase-dispersed free-running population. As requested by the referees in point (7), we added RAIN to test for rhythmicity in each of our recordings and revised the manuscript accordingly.

Furthermore, in preliminary experiments we briefly exposed hawkmoths to pheromone the night before the start of the experiment. However, we failed to obtain phase-synchronized spiking rhythms. Most likely, a circadian pattern of pheromone exposure would have been necessary as zeitgeber, which could not be used here due to long-term pheromone-dependent effects in spiking activity. These results are added as supplementary figure to Fig 3.

(5) The tip recordings from long trichoid sensilla are critical aspects of this study. These recordings were carried out on upper sensillar tips located on the distal-most second annulus. Since there are approximately 80 annuli on the Manduca antennae, it is unclear whether the recordings are representative of the antennal response.

We think the reviewers might have misinterpreted our description of the recording site. In the Methods, we state that we clip off the 20 most distal annuli (leaving a stump of about 60 annuli) and insert the reference electrode into the flagellum up to the second annulus from the cut end, i.e., the recording sites are located at 2/3 – 3/4 of the antenna length as seen from the head of the animal. We clarified this in the Methods section.

In addition, our lab did show with antibody stainings against Orco that apparently all ORNs that innervate long and short trichoid sensilla along the whole flagellum express the same staining pattern (Nolte et al., 2016). Lee and Strausfeld (1990) mapped all types of antennal sensilla, and together with pheromone-dependent tip-recordings of Kaissling et al. (1989) it was shown that most of the male antennal sensilla are pheromone-sensitive long trichoid sensilla, with one of the two innervating ORNs always responding to bombykal, ensuring high sensitivity to pheromone detection. Furthermore, our patch clamp recordings of primary cell cultures of whole male antennae found largely overlapping ion channel populations across ORNs (review: (Stengl, 2010)). This would indicate that all ORNs, whether they express ORs sensitive to pheromone or general odorants, could potentially share the same Orco-dependent spontaneous activity rhythms. Furthermore, in our lab, different experimenters from different years that recorded from long trichoid sensilla on different annuli did not detect obvious differences in neither the spontaneous activity nor the pheromone responses (c.f., Dolzer et al., 2003; Gawalek and Stengl, 2018; Schneider et al., 2025). Thus, it is very likely that we are reporting a general encoding mechanism that is not locally restricted along the antennal flagellum and is very likely shared by all types of OR-Orco expressing ORNs.

(6.1) The authors do not provide any data in support of their cAMP/cGMP-based Orco gating…

There are publications supporting cyclic nucleotide gating of Orco in Drosophila, but only after previous phosphorylation via protein kinase C (PKC; review: (Wicher and Miazzi, 2021)). Since Orco is very conserved among insect species, it is likely that PKC- and cGMP/cAMP-dependent regulations are present for Orco in other insect species. To test this, we are currently characterizing second messenger-dependence of spontaneous spiking activity, which is the focus of a follow-up manuscript. Nevertheless, to provide more evidence for our hypothesis of the current manuscript, we added a new set of tip-recording experiments that demonstrate cAMP-dependent gating of Orco. Because of the addition of this figure, we merged figures 8-10 into Figure 8 and added the cAMP data as Figure 9.

(6.2) … and the PTTF model proposed is somewhat disappointing.

For a detailed introduction of our PTFL membrane clock hypothesis please see our opinion paper that we refer to in the manuscript (Stengl and Schneider, 2024). We added clarification of how Orco activation can influence cAMP levels. A more elaborate PTFL clock model including many more of the identified ion channels in hawkmoth ORNs is the focus of another manuscript to come.

(6.3) The model seems to be influenced by their long-held proposal that insect olfactory signaling has a critical metabotropic component involving cyclic nucleotides, PKC, etc, a view that may be influenced by the use of Orco homomeric complexes generated in HEK cells.

Indeed, we propose a metabotropic pheromone-transduction cascade, which in moths and cockroaches is based on G-protein-mediated activation of phospholipase C but not on adenylyl cyclase activation. Our hypothesis is not influenced by HEK cell heterologous expression studies of Orco but is supported by our own work comparing in vivo tip recordings of intact hawkmoths with patch clamp experiments on hawkmoth primary cell cultures of olfactory receptor neurons, which are able to respond to their species-specific pheromones in vitro (Schneider et al., 2025; Stengl, 2010; Stengl and Funk, 2013; Wicher and Miazzi, 2021). In addition, a multitude of publications by other laboratories with in vivo and in vitro studies using physiological, genetic, and immunocytochemical assays all support a metabotropic signal transduction cascade in insect olfaction (Stengl, 2010; Stengl and Funk, 2013; Takagi et al., 2025; Wicher and Miazzi, 2021). In contrast, the hypothesis suggesting a solely ionotropic pheromone- and general odor-dependent transduction cascade for all insect species is based on very sparse experimental evidence, based primarily on heterologous expression studies such as HEK cells that lack the insect’s WT molecular surroundings, and thus, cannot predict OR-Orco function in vivo. Furthermore, the ionotropic hypothesis is heavily based upon the argument that an inverse 7TM receptor cannot couple to G-proteins, which lacks careful backup via biochemical and structural studies. In addition, the ionotropic hypothesis lacks support via carefully performed physiological in vivo studies in different insect species that paid attention to analysis of the distinct kinetic components of ORN´s odor/pheromone responses and that employ physiological concentrations and durations of odor/pheromone stimuli (please see our most recent publication by Schneider et al. (2025)). We added references to the possible odor transduction mechanisms to the introduction.

(6.4) Nevertheless, structural studies on Orco do not support a cyclic nucleotide binding site, although PKC-based phosphorylation has been implicated in the fine-tuning/adaptation of olfactory signaling.

While structural studies did not find evidence for conserved known cyclic nucleotide binding sites on Orco, this does not exclude the presence of indirect cAMP effects via e.g., Orco subunits complexing with other molecules under direct cAMP control, such as other ion channel subunits. Furthermore, it does not exclude so far unknown binding sites, or via sites that fold out only after a specific sequence of previous phosphorylations of the many phosphorylation sites on Orco. Indeed, physiological studies in Drosophila presented evidence for cyclic nucleotide dependence of Orco after previous PKC-dependent phosphorylation (Getahun et al., 2013). Our ongoing in vivo experiments in hawkmoths further corroborate a zeitgeber time-dependent PKC- and cyclic nucleotide-dependent modulation of Orco. These detailed studies will be published in a follow-up publication. In the revised version of this manuscript, we added tip-recording experiments that indicate cAMP involvement in Orco gating (new Figure 9).

(7) Because only 5/11 LD and 7/10 DD animals showed daily rhythms, with averages lacking clear daily modulation, the methods are not sufficiently reliable enough to reveal novel underlying mechanisms of circadian rhythm generation. The reported results are therefore not yet reliable or quantifiable. To quantify their results, the authors should apply tests for circadian rhythmicity using methods such as RAIN, JTK CYCLE, MetaCycle, or Echo. The use of FFT and Wavelet is applauded, but these methods do not have tests of significance for rhythms and can be biased when analyzing data in which there could only be 1-3 circadian cycles. Because the conclusions appear to be based on 11-12 neurons that were recorded for 2-4 days, the reader is concerned that the methods are not yet perfected to provide strong evidence for circadian regulation of spontaneous firing of ORNs. The average data (e.g., Figure 3Bii and 3Cii) highlight the apparent lack of daily rhythms. In summary, the results would be more compelling if more than 50% of the recordings had significant circadian amplitudes and with similar periods and phases.

The long-term tip-recordings of intact hawkmoths are very challenging and take a very long time to accomplish, thus, we are very happy that we succeeded in obtaining so many of them (N=40). We are thankful to the reviewers’ suggestion to use RAIN since this analysis revealed circadian rhythms in 7 of 11 LD recordings, 8 of 12 DD recordings, and 2 of 12 OLC15 recordings. Please see also our response to (4) above, commenting the phase-dispersal of activity rhythms observed in our experiments, as well as in the behavior of hawkmoth males in the mating cage.

(8) The statement that circadian patterns of ORN firing are lost with the Orco antagonist (OLC15) is not strongly supported. The manuscript should be revised to quantify how Orco changed circadian amplitude in the 12 recorded neurons. Measures of circadian amplitude can avoid confusing/vague statements like Line 394 “low and high frequency bands appeared to merge during the activity phase around ZT 0 in the animals that showed clear circadian rhythms (N = 5 of 11 in LD)”. The conclusion that Orco blocks circadian firing appears to be contradicted by Figure 6, which indicates that ~6 of these neurons had circadian periods detected by wavelet. The manuscript would be strengthened with details about the specificity and reproducibility of the Orco antagonist. The authors quantify the gradual decrease in firing with the slope of a linear fit to estimate how the “effectiveness [of OLC15] increased over time.” They conclude that the drug “obliterated circadian rhythms and attenuated the spontaneous activity in several, but not all experiments (N = 8 of 12).” The report would be greatly strengthened with corroborating data from additional Orco antagonists and additional doses of OLC15 (the authors use only 50 uM OLC15).

According to the valuable suggestions of the referees, we used RAIN to detect circadian rhythms in the spiking attributes in each individual animal. Since only 2 of 12 animals displayed a circadian rhythm in OLC15, statistical comparison of circadian amplitudes is not possible. We revised the results section accordingly and added to the figure legend to make it clearer that the heat maps in Fig 5 are representative from one animal each and not averages across animals.

As the reviewer states correctly in (7), wavelet results of circadian rhythmicity must be interpreted carefully because of the low number of circadian cycles in ~3-4 day recordings. Since the heatmaps in Figure 5 visually revealed the presence of ultradian rhythms, the main focus of the wavelet analysis in Figure 6 is in the detection and quantification of ultradian periods up to 20 h.

We revised the Methods section to include references to previous experiments that characterized the effect of different doses of OLC15 and other Orco antagonists and agonists in M. sexta antennae (Nolte et al., 2016). Please see also our response to (1).

(9) The manuscript includes several statements that are more speculation than conclusion. For example, there is no evidence for tuning or plasticity in this report. Statements like the following should be removed or addressed with experiments that show changes in odor response specificity or sensitivity: "ORN signalosomes are highly plastic endogenous PTFL clocks comprising receptors for circadian and ultradian Zeitgebers that allow to tune into internal physiological and external environmental rhythms as basis for active sensing." (Discussion Line 622). The paper concludes that (line 380) "mean frequency of spontaneous spiking and the frequency of bursting expressed daily modulation, and are both most likely controlled via a circadian clock that targets the leak channel Orco." This is too bold given the available results.

We revised the manuscript accordingly and clarified which statements are supported via published evidence and which are predictions based upon our novel hypothesis published in our opinion paper (Stengl and Schneider, 2024).

(10.1) Because Orco conductance is modulated by cyclic nucleotides, it remains highly plausible that circadian regulation occurs upstream at the level of signaling pathways (e.g., calcium, calcium-binding proteins, GPCRs, cyclases, phosphodiesterases).

We agree with the referees that it is very likely that there are multiple layers of interconnected feedback cycles that control Orco localization and activity. Our novel hypothesis suggests interlocked TTFL and PTFL control of physiological circadian rhythms, not strictly hierarchical TTFL control, which would require a daily turnover of membrane proteins and transcriptional control via the established TTFL clock in insect ORNs. We are currently searching for TTFL control at all levels of odor/pheromone transduction using ZT-dependent transcriptomics in combination with qPCR and single-nucleus transcriptomics, involving also all the molecules suggested by the referees. These studies are ongoing, are very time- and money-consuming, and are beyond the scope of this manuscript. However, we added a set of experiments to this manuscript in which we demonstrate that the effect of increased cAMP on the spontaneous spiking activity is mediated by Orco (new Figure 9).

(10.2) The possibility that circadian oscillations of cyclic nucleotides are generated by the canonical TTFL mechanism has not been excluded. In fact, extensive work in Drosophila has demonstrated that the TTFL-based molecular clock proteins are required for circadian rhythms in olfaction.

Our experiments that test circadian TTFL control at different levels of the cAMP transduction cascade in hawkmoth antennae are on the way and are part of another publication. In section 6.2 we already stated that our experiments do not exclude that Orco is under indirect control of the TTFL. We revised our discussion accordingly.

The experiments published for TTFL dependent control of Drosophila olfaction that we are aware of (Krishnan et al., 1999; Tanoue et al., 2004) do not exclude interlinked PTFL and TTFL clocks. Krishnan et al. (1999) demonstrated that the TTFL clock in antennal olfactory receptor neurons correlates with circadian rhythms in odor responses measured in electroantennogram (EAG) recordings, not in single sensillum recordings as in our experiments. EAG recordings comprise not only voltage responses of the olfactory sensory neurons but also voltage changes generated in non-neuronal antennal cells such as trichogen and tormogen cells that built the transepithelial potential gradient via vATPases that generates the high K⁺ concentration in the sensillum lymph (Jain et al., 2024; Klein, 1992; Thurm and Küppers, 1980). In addition, EAG recordings most likely contain responses of afferent neurons originating from somata in the brain that maintain central control of the antennae. Thus, EAG recordings are difficult to interpret.

(11) A defining feature of circadian oscillators is the feedback mechanism that generates a time delay (e.g., PERIOD/TIMELESS repressing their own transcription). While the authors describe how cyclic nucleotides can regulate Orco conductance, they do not provide a convincing explanation of how Orco activity could, in turn, feed back into the proposed PTFL to sustain oscillations. For these reasons, the authors should consider:

(a) Providing a broader discussion of non-TTFL models of circadian rhythms (e.g., redox cycles, post-translational modifications).

We revised the discussion accordingly.

(b) Reassessing Orco expression using a higher-resolution temporal sampling ({greater than or equal to}6 timepoints per 24 h).

We added those experiments to the revised version of the manuscript (see our response to (2)).

(c) Clarifying or revising the PTFL model to explicitly address how feedback would be achieved. Alternatively, the data may be more consistent with Orco conductance rhythms being regulated by post-translational mechanisms downstream of the canonical TTFL oscillator, as suggested by the Drosophila olfactory system literature.

We added possible negative feedback elements to the Discussion to explain how our proposed PTFL could in principle work independent of TTFL clock.

Minor weaknesses:

(1) The authors should compare the firing patterns of ORN neurons to the bursts, clusters, and packets of retinal efferent spikes reported in Liu JS and Passaglia CL (2011; JBR). By comparing measures in moths to measures in Limulus, the authors might be able to address the question: Is the daily firing pattern of ORN neurons likely a conserved feature of circadian control of sensory sensitivity?

We have revised the discussion accordingly.

(2) The methods need further details. For example, it is unclear if or how single neuron activity was discriminated and whether the results were compromised by the relatively large environmental fluctuations in temperature (21-27oC), humidity (35-60%), or other cues known to modulate spontaneous firing.

These large fluctuations stem from doing experiments at different seasons (higher temperature and humidity in the summer months, lower temperature and humidity in winter). Throughout each individual experiment, conditions were stable. We clarified the Methods section accordingly.

Recommendations for the authors:

The authors should post the code for their computational model to a repository like GitHub.

The code for the computational model is now available at https://github.com/a-c-schneider/VijayanForlinoEtAl2025_Model.git

References

Benton R, Sachse S, Michnick SW, Vosshall LB. 2006. Atypical Membrane Topology and Heteromeric Function of Drosophila Odorant Receptors In Vivo. PLOS Biology 4:e20. DOI: https://doi.org/10.1371/journal.pbio.0040020

Chen S, Luetje CW. 2012. Identification of New Agonists and Antagonists of the Insect Odorant Receptor Co-Receptor Subunit. PLOS ONE 7:e36784. DOI: https://doi.org/10.1371/journal.pone.0036784

Dolzer J, Fischer K, Stengl M. 2003. Adaptation in pheromone-sensitive trichoid sensilla of the hawkmoth Manduca sexta. Journal of Experimental Biology 206:1575–1588. DOI: https://doi.org/10.1242/jeb.00302

Dolzer J, Krannich S, Stengl M. 2008. Pharmacological Investigation of Protein Kinase C- and cGMP-Dependent Ion Channels in Cultured Olfactory Receptor Neurons of the Hawkmoth Manduca sexta. Chemical Senses 33:803–813. DOI: https://doi.org/10.1093/chemse/bjn043

Dolzer J, Schröder K, Stengl M. 2021. Cyclic nucleotide-dependent ionic currents in olfactory receptor neurons of the hawkmoth Manduca sexta suggest pull–push sensitivity modulation. European Journal of Neuroscience 54:4804–4826. DOI: https://doi.org/10.1111/ejn.15346

Gawalek P, Stengl M. 2018. The Diacylglycerol Analogs OAG and DOG Differentially Affect Primary Events of Pheromone Transduction in the Hawkmoth Manduca sexta in a Zeitgebertime-Dependent Manner Apparently Targeting TRP Channels. Frontiers in Cellular Neuroscience 12:218. DOI: https://doi.org/10.3389/fncel.2018.00218

Getahun MN, Olsson SB, Lavista-Llanos S, Hansson BS, Wicher D. 2013. Insect Odorant Response Sensitivity Is Tuned by Metabotropically Autoregulated Olfactory Receptors. PLOS ONE 8:e58889. DOI: https://doi.org/10.1371/journal.pone.0058889

Ghosh S, Suray C, Bozzolan F, Palazzo A, Monsempès C, Lecouvreur F, Chatterjee A. 2024. Pheromone-mediated command from the female to male clock induces and synchronizes circadian rhythms of the moth Spodoptera littoralis. Current biology 34:1414-1425.e5. DOI: https://doi.org/10.1016/j.cub.2024.02.042, PMID: 38479388

Jain K, Prelic S, Hansson BS, Wicher D. 2024. Expression of Drosophila melanogaster V-ATPases in Olfactory Sensillum Support Cells. Insects 15:1016. DOI: https://doi.org/10.3390/insects15121016

Jones PL, Pask GM, Rinker DC, Zwiebel LJ. 2011. Functional agonism of insect odorant receptor ion channels. Proceedings of the National Academy of Sciences 108:8821–8825. DOI: https://doi.org/10.1073/pnas.1102425108

Kaissling KE, Hildebrand JG, Tumlinson JH. 1989. Pheromone receptor cells in the male moth Manduca sexta. Archives of Insect Biochemistry and Physiology 10:273–279. DOI: https://doi.org/10.1002/arch.940100403

Klein U. 1992. The insect V-ATPase, a plasma membrane proton pump energizing secondary active transport: immunological evidence for the occurrence of a V-ATPase in insect ion-transporting epithelia. Journal of Experimental Biology 172:345–354. DOI: https://doi.org/10.1242/jeb.172.1.345

Krannich S, Stengl M. 2008. Cyclic Nucleotide-Activated Currents in Cultured Olfactory Receptor Neurons of the Hawkmoth Manduca sexta. Journal of Neurophysiology 100:2866–2877. DOI: https://doi.org/10.1152/jn.01400.2007

Krishnan B, Dryer SE, Hardin PE. 1999. Circadian rhythms in olfactory responses of Drosophila melanogaster. Nature 400:375–378. DOI: https://doi.org/10.1038/22566

Lee JK, Strausfeld NJ. 1990. Structure, distribution and number of surface sensilla and their receptor cells on the olfactory appendage of the male mothManduca sexta. Journal of Neurocytology 19:519–538. DOI: https://doi.org/10.1007/BF01257241

Merlin C, Lucas P, Rochat D, François M-C, Maïbèche-Coisne M, Jacquin-Joly E. 2007. An Antennal Circadian Clock and Circadian Rhythms in Peripheral Pheromone Reception in the Moth Spodoptera littoralis. Journal of Biological Rhythms 22:502–514. DOI: https://doi.org/10.1177/0748730407307737

Nolte A, Funk NW, Mukunda L, Gawalek P, Werckenthin A, Hansson BS, Wicher D, Stengl M. 2013. In situ Tip-Recordings Found No Evidence for an Orco-Based Ionotropic Mechanism of Pheromone-Transduction in Manduca sexta. PLOS ONE 8:e62648. DOI: https://doi.org/10.1371/journal.pone.0062648

Nolte A, Gawalek P, Koerte S, Wei H, Schumann R, Werckenthin A, Krieger J, Stengl M. 2016. No Evidence for Ionotropic Pheromone Transduction in the Hawkmoth Manduca sexta. PLOS ONE 11:e0166060. DOI: https://doi.org/10.1371/journal.pone.0166060

Rymer J, Bauernfeind AL, Brown S, Page TL. 2007. Circadian rhythms in the mating behavior of the cockroach, Leucophaea maderae. Journal of Biological Rhythms 22:43–57. DOI: https://doi.org/10.1177/0748730406295462, PMID: 17229924

Schendzielorz J, Schendzielorz T, Arendt A, Stengl M. 2014. Bimodal Oscillations of Cyclic Nucleotide Concentrations in the Circadian System of the Madeira Cockroach Rhyparobia maderae. Journal of Biological Rhythms 29:318–331. DOI: https://doi.org/10.1177/0748730414546133

Schendzielorz T, Peters W, Boekhoff I, Stengl M. 2012. Time of Day Changes in Cyclic Nucleotides Are Modified via Octopamine and Pheromone in Antennae of the Madeira Cockroach. Journal of Biological Rhythms 27:388–397. DOI: https://doi.org/10.1177/0748730412456265

Schendzielorz T, Schirmer K, Stolte P, Stengl M. 2015. Octopamine Regulates Antennal Sensory Neurons via Daytime-Dependent Changes in cAMP and IP3 Levels in the Hawkmoth Manduca sexta. PLOS ONE 10:e0121230. DOI: https://doi.org/10.1371/journal.pone.0121230

Schneider AC, Schröder K, Chang Y, Nolte A, Gawalek P, Stengl M. 2025. Hawkmoth Pheromone Transduction Involves G-Protein–Dependent Phospholipase Cβ Signaling. eNeuro 12:ENEURO.0376-24.2024. DOI: https://doi.org/10.1523/ENEURO.0376-24.2024, PMID: 39880675

Stengl M. 2010. Pheromone Transduction in Moths. Frontiers in Cellular Neuroscience 4:133. DOI: https://doi.org/10.3389/fncel.2010.00133

Stengl M. 1994. Inositol-trisphosphate-dependent calcium currents precede cation currents in insect olfactory receptor neurons in vitro. Journal of Comparative Physiology A 174:187–194. DOI: https://doi.org/10.1007/BF00193785

Stengl M. 1993. Intracellular-Messenger-Mediated Cation Channels in Cultured Olfactory Receptor Neurons. Journal of Experimental Biology 178:125–147. DOI: https://doi.org/10.1242/jeb.178.1.125

Stengl M, Funk NW. 2013. The role of the coreceptor Orco in insect olfactory transduction. Journal of Comparative Physiology A 199:897–909. DOI: https://doi.org/10.1007/s00359-013-0837-3

Stengl M, Hildebrand JG. 1990. Insect olfactory neurons in vitro: morphological and immunocytochemical characterization of male-specific antennal receptor cells from developing antennae of male Manduca sexta. Journal of Neuroscience 10:837–847. DOI: https://doi.org/10.1523/JNEUROSCI.10-03-00837.1990, PMID: 2319305

Stengl M, Schneider AC. 2024. Contribution of membrane-associated oscillators to biological timing at different timescales. Frontiers in Physiology 14:1243455. DOI: https://doi.org/10.3389/fphys.2023.1243455

Takagi S, Abuin L, Mermet J, Lee D, Benton R. 2025. A GPCR signaling pathway in insect odor detection. DOI: https://doi.org/10.1101/2025.10.03.680299

Tanoue S, Krishnan P, Krishnan B, Dryer SE, Hardin PE. 2004. Circadian Clocks in Antennal Neurons Are Necessary and Sufficient for Olfaction Rhythms in Drosophila. Current Biology 14:638–649. DOI: https://doi.org/10.1016/j.cub.2004.04.009, PMID: 15084278

Thurm U, Küppers J. 1980. Epithelial physiology of insect sensilla. In: Locke M, Smith DS (Eds). Insect Biology in the Future. Academic Press. p. 735–763. DOI: https://doi.org/10.1016/B978-0-12-454340-9.50039-2

Wicher D, Miazzi F. 2021. Functional properties of insect olfactory receptors: ionotropic receptors and odorant receptors. Cell and Tissue Research 383:7–19. DOI: https://doi.org/10.1007/s00441-020-03363-x

Author response:

Public Reviews:

Reviewer #1 (Public review):

This rigorous and creative study uses an elegant combination of metabolomics, transcriptomics, and budding yeast molecular genetics to discover that (i) activating AMPK to maintain mitochondrial respiration fueled by cytosolic Acetyl CoA and (ii) increasing fatty acid synthesis independent of respiration drive independent pathways that increase the fitness of replicatively-aged budding yeast cells, albeit without increasing their lifespan. This work will be of interest to scientists in the field of aging and metabolism. Some clarifications in the text would address the following concerns, which would increase the impact of the study:

(1) What does activation of AMPK (via PGDP-Sak1 expression) do to the replicative lifespan? How many bud scars, in general, do the subpopulations that are older - yet have less Tom70 (increased mitochondrial fitness) - have, after the 48 hrs time point that they are examining? How many divisions occurred in this 48hr time period - i.e. is it long enough to have all cells reach the end of their replicative lifespan? This information is important to rule out that a subset of the mutant cells just divided faster and hence had more divisions within 48 hrs (growing faster and living longer are different things). Having identical growth curves doesn't indicate per se that they all divide at the same rate, as there may be a subpopulation that divides faster and a subpopulation that doesn't grow so well.

Increasing AMPK activity increases replicative lifespan [PMID: 25869125], but given our finding that AMPK activation splits the population, such replicative lifespan assays are hard to interpret. Bud scar counts have a similar issue. Hence we restricted the lifespan and bud scar analyses to wt and A2A which are more homogenous (Figures S2 B and E). A2A cells at 48h have ~25% more bud scars than wt cells. Yes, by 48h most of the cells have lost viability (Figure 2E). The reviewer is correct that you can't properly compare the lifespan curves if the cells divide at different rates, hence our follow-up test of wt at 48h vs A2A at 40h viability after we had confirmed that these timepoints captured cells at equivalent replicative ages (Figure 2D,E). This shows that viability of A2A is slightly lower than wt at matched age, indicating a slightly shorter lifespan.

(2) A2A cells do not have an extended replicative lifespan (RLS) but show an increase in the "low senescence" population (Figure 2). If the cells are not becoming senescent, why don't they have longer RLS? Not having a longer lifespan seems inconsistent with the statement that "bud scar counting confirmed that A2A cells reach a higher age than wild type", which comes back to how many times the cells can divide in the 48hr timepoint studied and their rate of cell division? Also, the lifespan curve shown is plotted against time, not cell division number, which does not take into account different division times of cells within the population (described above). It would be much more useful to show standard lifespan curves showing cell division numbers per lifespan per cell.

Our observation that cells can reach the end of life without senescing is consistent with other studies that have studied the life course of individual cells by microscopy [PMID: 31291577, 32675375]. These studies always highlight some proportion of the cells that reach the end of life with no or minimal senescence, though this fraction varies with the experimental system. The question of why cells lose viability without senescing is a complete unknown in the field, but reflects a wider lack of consensus as to why yeast lose viability with replicative age.

We are wary about making strong statements on lifespan for exactly the reason the reviewer picks out. In liquid culture we can only assess viability over time, and it is clear from the comparison of liquid and solid media lifespans performed by the Gottschling lab [PMID: 19652178] that culture system has a huge effect on lifespan, with cells in classical microdissection-based lifespan assays living far longer than they do in liquid. This of course means that classical microdissection assays are not very useful for A2A so we are left with an unsatisfactory approximation. We have therefore restricted our conclusion on lifespan to simply say that lifespan of A2A cells is not extended which our data in Figures 2D,E,S2B does support (see also answer to Q1), and therefore with the majority of A2A cells showing low senescence marks and high fitness at 48h we can conclude that lifespan and fitness loss must be separable.

We will note these limitations of lifespan measurements in the manuscript.

(3) Increased "fitness" of the old cells is implied from the increased size of the colonies that the old cells can make. However, this is a measure of the fitness of the daughters per se, not the old mother cells. Are the old mothers just passing on healthier mitochondria and more lipids to the daughters, such that they can divide more times? If the aged cells have an "increased fitness", why don't they divide more times themselves (i.e. live longer?).

Yes, colony growth speed is defined by daughter cell replication, and as long as the daughters and subsequent generations divide at the same rate irrespective of whether they come from a young or old mothers then the size of the colony after 24 hours varies based on the time it took the initial mother to produce a daughter. This is what the assay really measures. We note that aged wildtype mothers often do not divide at all in the first 24 hours after being put on an agar plate (hence the tiny reported colony size), even though they do eventually produce a daughter which then forms a colony, whereas A2A cells tend to produce the first daughter rapidly whether young or old. It is known that daughters of aged wildtype mothers also divide slower, which will also contribute to differences in colony size, and this may well result from a lipid and/or mitochondrial contribution, but the primary driver of colony size in 24 hours is the time the mother took to initially divide. We will add this detail to the manuscript.

As noted above, the mechanistic basis of lifespan is unknown, but although senescence can shorten lifespan, our work and that of others shows that lifespan is still limited in the absence of senescence.

(4) The statement is made that "these experiments define two classes of aging cells with distinct metabolic needs, coherent with the model of two aging trajectories previously proposed (referencing Nan Hao's work)". However, the big difference here is that in Nan Hao's work, their two aging trajectories influenced the length of lifespan, but that does not appear to be the case here. That distinction should be made clear. Perhaps the authors could also speculate as to why the A2A yeast stops dividing after presumably the same number of cell divisions, even though they have an activated AMPK and activated fatty acid synthesis pathway.

We will add this distinction. As noted above, we are wary of making strong statements regarding lifespan as the assays we can do in liquid culture are limited. We are therefore similarly wary about speculating about causes for the lack of lifespan difference because in reality all we can do is rule out a big effect. We would love to speculate on why the A2A cells don't have an extended lifespan, but at this point we don't have any good ideas on this point!

(5) I am a bit confused by the use of the word "senescence" by this lab here and in their previous growth on galactose studies. If yeast don't senesce, which is usually defined as an irreversible arrest of the cell cycle where cells stop dividing, shouldn't the yeast that do not senesce still be dividing and hence have a longer lifespan? Should a different term be used rather than senescence? Such as "fitness late in life". The authors giving their definition of senescence may help reduce this apparent contradiction.

We completely agree, this is confusing and noted this distinction in the Introduction. Use of the term senescence to mean a loss of fitness late in life in yeast stems from the classical definition of senescence as applied to whole organisms. However, the term senescence as applied to cells has a more specific meaning in terms of the cell cycle as the reviewer notes. As an individual S. cerevisiae is both a cell and an organism, the terminology clashes. However, the marker we largely employ (Tom70-GFP) which in our hands is a very good proxy for fitness was originally defined as marking the senescence entry point (SEP), so overall we feel we can't avoid the term.

Reviewer #2 (Public review):

Summary:

In this study, the authors investigate how cytosolic acetyl-CoA metabolism influences replicative aging in budding yeast. They propose that acetyl-CoA regulates aging through three major pathways: (1) mitochondrial transport to support mitochondrial function, (2) fatty acid synthesis, and (3) global protein acetylation. The data show that AMPK activation promotes mitochondrial import of acetyl-CoA and partially mitigates mitochondrial decline in a subset of aging cells.

Furthermore, the engineered A2A strain, which enhances mitochondrial acetyl-CoA utilization while relieving inhibition of fatty acid synthesis, increases the proportion of cells exhibiting a "low senescence" phenotype.

Overall, this is a thoughtful and potentially impactful study that advances our understanding of metab to olic control of aging. Addressing the points below, particularly by refining interpretations and, where feasible, incorporating additional analyses, will further strengthen the manuscript and its conclusions.

Strengths:

The study has several notable strengths. It addresses an important question by shifting the focus from lifespan to preservation of late-life fitness, which is highly relevant to aging biology. The work integrates metabolic, genetic, and functional analyses to link cytosolic acetyl-CoA flux with distinct aging outcomes, and the engineering of the A2A strain provides a clear and elegant demonstration of how coordinated pathway modulation can improve cellular fitness.

Weaknesses:

(1) While the manuscript focuses on mitochondrial transport and fatty acid synthesis, cytosolic acetyl-CoA is also a key regulator of histone acetylation and chromatin silencing. It would strengthen the study to consider whether acetyl-CoA depletion contributes to improved fitness through enhanced rDNA silencing. Given the well-established role of rDNA instability in yeast aging, additional experiments examining rDNA silencing and stability would be valuable. For example, monitoring rDNA copy number changes (not necessarily ERCs) under AMPK activation, oleic acid supplementation, and in the A2A strain, similar to approaches used in the authors' prior work, would help clarify whether chromatin regulation contributes to the observed phenotypes.

We have data addressing this point that we will add to the manuscript. In short, we see no difference in gene expression from Sir2-repressed sub-telomeric regions or MAT loci, but the genome-wide gene expression dysregulation associated with age is partially suppressed in PGPD-SAK1. However, A2A does not suppress this further, so it is not critical for the suppression of senescence in A2A though we are following this up. ERC accumulation is higher in A2A at 48h, consistent with the cells being older, meaning that ERCs are unlinked to senescence onset as we have previously reported. There is a strong upregulation of transcripts from Sir2-repressed rDNA intergenic spacers with age in all genotypes, but we attribute this simply to the copy number increase of these regions on ERCs rather than a defect in silencing. We have previously looked for heritable changes in rDNA copy number arising during ageing and found (to our surprise) absolutely nothing, so we don't expect any changes under these conditions.

(2) The current data do not fully distinguish whether AMPK activation and oleic acid supplementation act on distinct subpopulations of aging cells. An alternative explanation is that oleic acid supplementation enhances mitochondrial function and acts additively with AMPK activation, thereby increasing the fraction of cells in the "low senescence" state. Since this distinction is not central to the main conclusions, I suggest softening the language around subpopulation specificity. Emphasizing instead that the A2A strain coordinately modulates multiple branches of acetyl-CoA metabolism to improve late-life fitness would maintain the strength of the central message without overinterpretation.

We agree that oleic acid and the lipids produced downstream of Acc1 in A2A may improve late life fitness via enhanced mitochondrial function, and in support of this Oxygen Consumption Rate is marginally (though significantly) higher in A2A than PGPD-SAK1. We will add this data to the manuscript. However, we disagree with the interpretation of an additive effect as we report throughout the study that AMPK activation and lipid biosynthesis/supplementation affect different sub-populations of cells. We do not observe populations of intermediate senescence cells, rather by flow cytometry and fitness assays we observe individual cells in binary low senescence or high senescence states.

(3) The manuscript proposes that lipid starvation and excess acetyl-CoA are major drivers of senescence in distinct subpopulations of wild-type aging cells. This conclusion is not yet fully supported by the presented data. Direct measurements of age-dependent divergence in acetyl-CoA and fatty acid levels at the single-cell level would be needed to substantiate this model. Based on the current evidence, a more conservative interpretation would be that aging cells exhibit differential sensitivity to perturbations in acetyl-CoA and lipid metabolism. Accordingly, I recommend revising the statement in the Abstract ("We further implicate lipid starvation and excess acetyl coenzyme A availability as major drivers of senescence...") and the corresponding discussion text to better align with the data.

We agree and will adjust the abstract to make it clearer that the lipid starvation / excess acetyl coA interpretation is a model.

Reviewer #3 (Public review):

Summary:

These findings suggest that PGPD-SAK1 yeast show a subpopulation with lowered TOM70-GFP expression in high bud scar staining aged cells. Deletion of CAT2 or MLS1 reduces this effect. A PGPD-SAK1 acc1S1157A double mutant (called "A2A" here) shows an even larger effect of lowered tom70 expression in high bud scar staining aged cells. Utilization of various additional mutants involved in acetyl-CoA transport, carnitine shuttle, respiration, etc., leads the authors to conclude that these shifts in TOM70-GFP in aged cells are linked to the AMPK-fatty acid metabolic regulatory system.

Strengths:

These extensive and clearly described experiments reveal interesting changes in TOM70-GFP intensity in subsets of aged yeast in several mutants eventually identified as linked to the AMPK-fatty acid metabolic regulatory system.

Weaknesses:

(1) 3 biological replicates for mRNASeq is low.

Thank you for pointing this out. We performed another replicate after posting the initial preprint but didn’t update the figure in the eLIFe-reviewed version. We will add this to the scatter plots and analysis in Figure 1, the findings have not changed.

(2) While "Traditional conceptions of ageing implicate a progressive accumulation of damage leading to systemic degradation in performance until death, with evolutionary pressures acting to maximise early life fitness and fecundity at the expense of ageing health." is tangential perhaps to the data and conclusions of the study, both claims of this sentence are at best controversial, and the manuscript is no weaker for their omission.

We actually feel that this sentence is very important to the message of the manuscript, which is that ageing does not necessarily have to involve a loss of fitness before death. Ageing is often described as the progressive wearing out of components leading to decline and death (with an old car often used as an analogy); in the ageing field this is certainly controversial, but outside the field this remains the normal understanding. We think it is important to state this widely held viewpoint with which our findings are hard to reconcile.

Our interpretation that yeast are bet-hedging as a population growth strategy and this drives ageing in the long term is a classic antagonistic pleiotropy - we will add this term (from the citation that is already in the manuscript) and clarify in the discussion to make it obvious why we are introducing this concept in the introduction.

(3) The statement that "Here, we determine the basis of senescence and fitness loss in replicatively ageing yeast" is a bit strong as a summary of the present careful work presented here. If the authors had created yeast mutants that retained fitness indefinitely, this would be a more appropriate strength of claim to summarize the work.

Indeed - we will refine this sentence.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work the authors investigate the molecular dynamics of MinD, a component of the Bacillus subtilis Min system, in vitro and in vivo. In Escherichia coli the Min system is highly dynamic and displays rapid pole to pole oscillation whereby a time average minimum of the Min proteins at mid cell is established. However, in B. subtilis, this is not the case, and there is no MinE present. MinD in B. subtilis dynamically relocalizes from the poles to division sites, and binds to MinC and MinJ, which mediates its interaction with DivIVA. This paper reports biochemical characterization of B. subtilis MinD in vitro and dynamics of MinD variants in vivo, providing mechanistic insight into the mechanism of dynamic localization.

Strengths:

In the current study, the authors perform a detailed biochemical characterization of the in vitro ATPase activity of MinD and demonstrate that rapid hydrolysis is elicited by adding phospholipids. They further show using a collection of substitution mutants of MinD that both monomers and dimers bind to the membrane, and ATP occupancy changes the on and off rates. Identification, quantification, and tracking of discrete Halo-MinD populations was nicely done and showed that mutations in MinD alter dynamic localization, correlating with PL binding on and off rates in vitro.

In the revised manuscript, the authors now demonstrate localization and tracking data for minC and minJ deletion strains, which suggest that MinJ impacts MinD membrane cycling, but MinC does not. Additional in vitro work showed that the PDZ domain of MinJ modifies MinD ATP hydrolysis rates, and the authors propose that MinJ may promote MinD dimer formation.

Weaknesses of the revised version: No major weaknesses.

We thank this reviewer for the positive evaluation of our manuscript and the precise summary of our findings.

Reviewer #2 (Public review):

Summary:

Feddersen & Bramkamp determined important characteristics of how MinD protein binds/dissociates to/from the membrane, and dimerizes in relation to its ATPase activity. The presented data clearly shows the differences in function of MinD homologs from B. subtilis and E. coli.

Strengths:

The work presents well-executed experiments that lead to interesting conclusions and a new model of how Min system works during B. subtilis mid-cell division. Importantly, this model is supported by in vitro characterization of well-chosen mutants in the functional domains of MinD. Outstandingly, most of the in vitro data are confirmed by single-molecule localization microscopy.

Weaknesses:

The authors immobilized liposomes, for which they used E. coli total lipids, to measure ATPase activity and liposome association and dissociation of B. subtilis MinD. For these experiments would be more suitable to use B. subtilis total lipids as more biologically relevant data could be gained.

Although the work is in detail and nicely compares the function of B. subtilis Min system with E. coli Min system, it lacks the comparison of the Min system function in other rod-shaped Gram-positive bacteria. I would suggest including in the Discussion the complexity of other Min systems. Especially, this complexity is seen in other rod-shaped and spore formers such as Clostridial species in which one of these Min systems or both are present, an oscillating E. coli Min system type and more static as in B. subtilis.

Comments on revisions:

I'm satisfied with the authors response to my private recommendation points. However, I thought that they would also respond to my points mentioned in Public Review part, weaknesses as shown above and update the revised version accordingly.

We are very grateful to the reviewer for the positive comments and fully agree with the points raised. Due to the overall length of the manuscript, we initially omitted a discussion of the complexity of the Min system in certain Firmicutes. However, we agree that this aspect should be considered. Accordingly, we have now added a dedicated paragraph to the Discussion section addressing this point.

We also agree that investigating different lipid compositions, including native membranes from Bacillus subtilis, represents a logical next step to further elucidate the influence of lipids on the MinD activity cycle. However, we consider this to constitute a separate project and therefore beyond the scope of the present study.

Recommendations for the authors:

Reviewing Editors:

Some minor corrections are requested-the addition of a bit more details about the complexity of Min systems in other bacteria in particular to the discussion as suggested by Reviewer 2 would be very much appreciated.

We thank the editors for their positive assessment and the clear recommendations. We have now added a dedicated paragraph to the Discussion section addressing the complexity of the Min system in Clostridioides.

Reviewer #1 (Recommendations for the authors):

The following corrections are requested:

Abstract - Line 29 - Remove the word "solely" from this statement of the abstract. It would be wise to not be so rigid for a biological system that is only partially characterized and to allow for the possibility that biological factors, including local concentrations and/or other molecules, may yet be discovered to impact MinD activation under certain conditions.

We agree and have amended the text to avoid a to restrictive statement.

Line 38 - Remove "do not require any unknown protein component" for the reason stated above. Currently, the experiments recapitulate activation suggesting the membrane binding and release controls dynamics without additional factors. This allows for the possibility that biological factors may yet be shown to impact MinD activation under certain conditions.

We agree and have change the text.

Discussion - Line 526 - Thermus thermophilus is misspelt.

Corrected.

Author response:

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

eLife Assessment

This study reports a dynamic association/dissociation between malate dehydrogenase (MDH1) and citrate synthase (CIT1) in Saccharomyces cerevisiae under different metabolic conditions that control TCA pathway flux rate. The research question is timely, the use of the NanoBiT split-luciferase system to monitor protein-protein interactions is innovative, and the significance of the findings is valuable. However, the strength of evidence needed to support the conclusions was found to be incomplete based on a lack of critical control and mechanistic experiments.

We thank the editor for this thoughtful assessment of our work. We are encouraged that the research question, experimental approach, and overall significance were viewed positively.

To address the concern regarding the strength of evidence, we have implemented additional controls in the revised manuscript. Specifically, we have repeated all MDH1CIT1 interaction measurements alongside strains expressing full-length NanoLUC fusion proteins to assess MDH1 and CIT1 protein abundance. The resulting data, now included as supplementary figures (Figure 2 – figure supplement 2, Figure 2 – figure supplement 3, Figure 3 – figure supplement 1, Figure 4 – figure supplement 2), demonstrate the reproducibility of the findings and indicate that the observed changes in MDH1-CIT1 interaction are not attributable to protein abundance variations.

We agree that a detailed mechanistic dissection of how the MDH1–CIT1 complex influences metabolic pathway flux is an essential piece of evidence for establishing the functions of the metabolon. However, such analyses require extensive additional investigation beyond the scope of the present study. Accordingly, we have clarified the aims of this work in the revised manuscript to emphasize that our primary objective is to characterize the dynamic behavior of the MDH1–CIT1 interaction under different metabolic conditions and to identify key factors associated with its regulation.

We believe these revisions strengthen the rigor of the study, better define its scope, and provide a solid foundation for future mechanistic investigations.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by the Obata group characterizes the dynamics of the canonical malate dehydrogenase-citrate synthase metabolon in yeast.

Strengths:

The study is well-written and appears to give clear demonstrations of this phenomenon.

Studies of the dynamics of metabolon formation are rare; if the authors can address the concern detailed below, then they have provided such for one of the canonical metabolons in nature.

We sincerely thank the reviewer for their positive assessment and for recognizing the value of our study in characterizing the dynamics of the MDH1-CIT1 metabolon. We appreciate the recognition that studies of metabolon dynamics are rare and that our work provides a clear demonstration of this phenomenon for a canonical metabolon. We have carefully addressed the methodological concerns regarding the NanoBiT system as detailed below to further strengthen the evidence for our findings.

Weaknesses:

There is a fundamental issue with the study, which is that the authors do not provide enough support or information concerning the split luciferase system that they use.

We agree that a detailed description of the NanoBiT system is essential to ensure the reliability of the methodology. As suggested, we have added a dedicated paragraph to the Introduction (Lines 90–103) to clarify these technical aspects, supported by the foundational work of Dixon et al. (2016).

Is the binding reversible or not? How the data is interpreted is massively influenced by this fact.

Yes, the NanoBiT system is specifically designed to be reversible. The intrinsic affinity of the subunits is low (K_D = 190 μM), and the association and dissociation rate constants (k_on = 500 M^-1s ^-1, k_off = 0.2 s^-1) are well outside the range of typical protein-protein interactions (Dixon et al., 2016). These kinetics ensure that the assembly and disassembly of the luminescent complex are dictated solely by the interaction characteristics of the target proteins (MDH1 and CIT1) and not by the tags themselves. This allows for real-time monitoring of both the association and dissociation phases.

What are the pros and cons of this method in comparison to, for example, FLIM-FRET?

We have now explicitly addressed the pros and cons of our methodology compared to fluorescence-based systems:

Pros: The NanoLUC-based reporter is 150 times brighter than conventional luciferases and has a significantly higher dynamic range (Hall et al 2016), allowing detection of weak transient interactions. Importantly for this study, fluorescence-based methods such as FLIM-FRET and BRET are difficult to implement in yeast microplate assays due to the high levels of cellular autofluorescence. NanoBiT bypasses this issue, providing a high signal-tonoise ratio.

Cons: Unlike FRET, NanoBiT requires the application of a substrate (furimazine). We did not include this disadvantage in the manuscript because it is not critical in a yeast study. Furimazine can be applied directly to the medium and readily permeates cells.

The authors state that the method is semi-quantitative - can they document this?

The semi-quantitative nature of the system is supported by its high dynamic range and the linear relationship between the luminescence signal and the amount of protein complex formed, as documented in Dixon et al. (2016). By using this system in a microplate setting, we were able to monitor relative increases or decreases in interaction levels over time across multiple metabolic conditions, providing a robust comparative analysis of metabolon dynamics.

All of the conclusions are based on the quality of this method. I know that it has been used by others, but at least some preliminary documentation to address these questions is required.

We acknowledge the reviewer’s concern regarding the reliance on the NanoBiT system. To ensure the reliability of our conclusions, we have included several lines of evidence to validate the method and demonstrate that the observed luminescence signals accurately reflect protein-protein interaction dynamics.

To confirm the NanoBiT results using an independent biochemical approach, we performed an in vivo pull-down assay following glucose addition (Figure 2 – figure supplement 1A). The results demonstrate a reduction in the physical association between MDH1 and CIT1. This biochemical validation directly supports the reduction in interaction observed with the NanoBiT system during the Crabtree effect.

We have provided protein abundance data for both MDH1 and CIT1 across the experimental conditions (Figure 2 – figure supplement 1&3; Figure 3 – figure supplement 1; Figure 4 – figure supplement 2). These results show only minor changes in protein levels, confirming that the fluctuations in the NanoBiT signal are independent of protein expression and represent genuine changes in metabolon assembly.

To ensure the findings are reproducible, we have included MDH1-CIT1 interaction results from repeated independent experiments (Figure 2 – figure supplement 1&3; Figure 3 – figure supplement 1; Figure 4 – figure supplement 1). The consistency of the results across these trials confirms the robustness of the system in monitoring the metabolic regulation of this complex.

We hope that these additional experimental validations, alongside the detailed technical description based on the established properties of the NanoBiT system (Dixon et al., 2016; Hall et al., 2012), provide the necessary documentation to satisfy the reviewer’s concerns regarding the quality and reliability of the method.

Reviewer #2 (Public review):

This study explores the dynamic association between malate dehydrogenase (MDH1) and citrate synthase (CIT1) in Saccharomyces cerevisiae, with the aim of linking this interaction to respiratory metabolism. Utilizing a NanoBiT split-luciferase system, the authors monitor protein-protein interactions in vivo under various metabolic conditions.

Major Concerns:

(1) NanoBiT Signal May Reflect Protein Abundance Rather Than Interaction Strength

In Figure 1C, the authors report increased MDH1-CIT1 interaction under respiratory (acetate) conditions and decreased interaction during fermentation (glucose), as indicated by NanoBiT luminescence. However, this signal appears to correlate strongly with the expression levels of MDH1 and CIT1, raising the possibility that the observed luminescence reflects protein abundance rather than specific interaction dynamics. To resolve this, NanoBiT signals should be normalized to the expression levels of both proteins to distinguish between abundance-driven and interaction-driven changes.

We agree that distinguishing between abundance-driven and interaction-driven changes is vital. To address this, we have included new data showing the relative protein levels of MDH1 and CIT1 across all experimental conditions. The protein levels were assessed using yeast lines expressing these proteins tagged with full-length NanoLUC luciferase (Figure 2 – figure supplement 1&3, Figure 3 - figure supplement 1, Figure 4 – figure supplement 2). Using the luminescence data of these relative protein levels, we have included plots showing normalized interaction index (Figure 2 – figure supplement 1G & 3D,H,L; Figure 3 - figure supplement 1D,H,L P; Figure 4 – figure supplement 1D,H,L). This index was calculated by dividing the NanoBiT interaction signal by the product of the relative abundances of both proteins:

In this formula, NanoBiT, MDH1, and CIT1 are the relative luminescence levels at each time point. This analysis clarified that the changes in the interaction signal significantly exceeded the fluctuations in protein levels, confirming that the dynamics are interactionspecific and not abundance-driven. To provide the most direct and transparent representation of the experimental measurements, we have chosen to keep the raw RLU data in the main figures and have moved the data related to protein abundance and normalization to figure supplements.

(2) Lack of Causal Evidence

The study presents a series of metabolic perturbation experiments (e.g., arsenite, AOA, antimycin A, malonate) and correlates changes in metabolite levels with NanoBiT signals. However, these data are correlative and do not establish a functional role for the MDH1CIT1 interaction in metabolic regulation. To demonstrate causality, the authors should implement approaches to specifically disrupt the MDH1-CIT1 interaction. One strategy could involve using a 15-residue peptide (Pept1) derived from the Pro354-Pro366 region of CIT1, previously shown to mediate the interaction, or introducing the cit1Δ3 (Arg362Glu) mutation, which perturbs binding. Metabolic flux analysis using ^13C-labeled glucose and mitochondrial respiration assays (e.g., Seahorse) could then assess functional consequences.

We agree with the reviewer that the current dataset correlates metabolon assembly with metabolic states rather than establishing a direct causal proof of its functional role in regulating pathway flux.

However, the primary objective of this manuscript was to establish the dynamic nature of the MDH1-CIT1 metabolon and to demonstrate the causal relationship between the changes in cellular conditions and metabolon dynamics through in vitro and in vivo assessments. Demonstrating that this canonical multienzyme complex undergoes reversible assembly and disassembly in vivo represents a major advance, as metabolon dynamics is a critical, yet previously unrevealed, factor involved in metabolic regulation. We aimed to define the specific environmental triggers that govern these dynamics, providing the necessary foundation for defining the functions of metabolons.

We completely agree that establishing causality using interaction-deficient mutants coupled with metabolic flux analysis is another critical experiment to establish the functions of the TCA cycle metabolon. We have, in fact, been conducting these precise metabolic flux analyses on CIT1 mutants with disrupted interaction with MDH1. Because the functional consequences of complex disruption involve wide-reaching metabolic rerouting that requires extensive data presentation and modeling, this work forms a separate, comprehensive follow-up study that is currently in preparation for submission in the near future.

To address this limitation in the current manuscript, we have carefully reviewed and revised the Abstract, Results, Discussion, and Conclusion sections (Lines 19-22; 205; 322-327; 341-342; 458-466). We have removed any language that may have inadvertently implied direct causality. We now explicitly state that our findings indicate the relationship between metabolon dynamics and respiratory conditions, and we have added a clear statement noting that the direct effects of this assembly on metabolic flux are the focus of our forthcoming studies.

(3) Absence of Protein Expression Controls Under Perturbation Conditions

In experiments involving acetate, arsenite, AOA, antimycin A, and malonate, the authors infer changes in MDH1-CIT1 association based solely on NanoBiT signals. However, no accompanying data are provided on MDH1 and CIT1 protein levels under these conditions. This omission weakens the conclusions, as altered expression rather than interaction strength could underlie the observed luminescence changes. Immunoblotting or quantitative proteomics should be used to confirm constant protein expression across conditions.

In response to your first concern, we have now performed protein expression assessments for all experiments, including the perturbation conditions, such as acetate, arsenite, AOA (Figure 3 – figure supplement 1), antimycin A, cyanide, and malonate (Figure 4 – figure supplement 2). The results demonstrate that the protein levels of MDH1 and CIT1 remain relatively stable throughout these treatments and do not correlate with the large changes observed in the interaction signals. This is also demonstrated by the normalized interaction index, which confirms that the shifts in luminescence are driven by the dynamic assembly and disassembly of the MDH1-CIT1 metabolon rather than changes in protein concentrations.

Conclusion:

Although the central question is compelling and the use of NanoBiT in live cells is a strength, the manuscript requires additional experimental rigor. Specifically, normalization of interaction signals, introduction of causative perturbations, and validation of protein expression are essential to substantiate the study's claims.

We sincerely thank the reviewer for recognizing the value of our central question and the strength of the live-cell NanoBiT system, as well as for your rigorous critique that has strengthened this manuscript. To address the concerns regarding experimental rigor, we have now provided extensive validation of MDH1 and CIT1 protein expression across all experimental conditions using yeast lines tagged with the full-length NanoLUC luciferase. These data demonstrate relatively stable protein expression, allowing us to calculate a normalized interaction index that substantiates that the observed luminescence shifts are driven by dynamic metabolon assembly rather than protein concentration. Regarding causative perturbations, we agree that introducing interaction-deficient mutants coupled with isotopic flux analysis is the critical next step to establish functional consequences. Because defining these pathway-wide rerouting events requires extensive modeling, this work will be reported in a follow-up study currently in preparation. Accordingly, we have carefully revised the manuscript to remove language implying direct causality, explicitly framing metabolon dynamics as an integral factor in metabolic regulation closely related to pathway activity and cellular metabolic states. We believe these new quantitative controls, normalizations, and textual clarifications thoroughly address the need for additional rigor and solidly substantiate our findings.

Reviewer #3 (Public review):

Summary:

Metabolons are multisubunit complexes that promote the physical association of sequential enzymes within a metabolic pathway. Such complexes are proposed to increase metabolic flux and efficiency by channeling reaction intermediates between enzymes. The TCA cycle enzymes malate dehydrogenase (MDH1) and citrate synthase (CIT1) have been linked to metabolon formation, yet the conditions under which these enzymes interact, and whether such interactions are dynamic in response to metabolic cues, remain unclear, particularly in the native cellular context. This study uses a nanoBIT protein-protein interaction assay to map the dynamic behavior of the MDH1-CIT1 interaction in response to multiple metabolic stimuli and challenges in yeast. Beyond mapping these interactions in real time, the authors also performed GC-MS metabolomics to map whole-cell metabolite alterations across experimental conditions. Finally, the authors use microscale thermophoresis to determine components that alter the MDH1-CIT1 interaction in vitro. Collectively, the authors synthesize their collected data into a model in which the MDH1CIT1 metabolon dissociates in conditions of low respiratory flux, and is stimulated during conditions of high respiratory flux. While their data largely support these models, some key exceptions are found that suggest this model is likely oversimplified and will require further work to understand the complexities associated with MDH1-CIT1 interaction dynamics. Nonetheless, the authors put forth an interesting and timely toolkit to begin to understand the interaction kinetics and dynamics of key metabolic enzymes that should serve as a platform to begin disentangling these important yet understudied aspects of metabolic regulation.

We thank the reviewer for this thoughtful and constructive summary of our work. We appreciate the recognition of the novelty and utility of our experimental approach and the integrated analysis of MDH1–CIT1 interaction dynamics.

We agree with the reviewer that, although our data largely support a model in which MDH1– CIT1 interaction correlates with respiratory activity, there are conditions that do not fully conform to this simplified framework. In the revised manuscript, we have addressed these apparent inconsistencies by providing detailed interpretations of the counterintuitive observations (e.g., ETC inhibition) and emphasizing that the MDH1–CIT1 interaction is modulated by changes in the mitochondrial matrix microenvironment associated with respiratory activity.

Furthermore, we have revised the Discussion to highlight that the regulation of the MDH1– CIT1 interaction is likely multifactorial, involving the combined effects of pH, metabolites, and other unknown factors, which together enable fine-tuning of metabolic flux in fluctuating environments. This expanded perspective is now more clarified.

We agree that identifying the precise molecular determinants of MDH1–CIT1 interaction dynamics will require additional mechanistic studies, such as systematic analyses using yeast mutants. While these experiments are an important next step, they are beyond the scope of the present study. We anticipate that the toolkit and framework established here will facilitate such future investigations.

Strengths:

(1) The authors address an important question: how do metabolon-associated proteinprotein interactions change across altered metabolic conditions?

(2) The development and validation of the MDH1-CIT1 nanoBIT assay provides an important tool to allow the quantification of this protein-protein interaction in vivo. Importantly, the authors demonstrate that the assay allows kinetic and real time assessment of these protein interactions, which reveal interesting and dynamic behavior across conditions.

(3) The use of classic biochemical techniques to confirm that pH and various metabolites can alter the MDH1-CIT1 interaction in vitro is rigorous and supports the model put forth by the authors.

We thank the reviewer for these positive and encouraging comments. We are pleased that the importance of the research question, the development of the MDH1–CIT1 NanoBiT assay, and the integration of in vivo and in vitro approaches were recognized. We especially appreciate the acknowledgment of the assay’s ability to capture dynamic and kinetic changes in protein–protein interactions, as well as the support provided by the biochemical analyses. We hope that the experimental framework established in this study will serve as a useful platform for further investigations into metabolon dynamics and metabolic regulation.

Weaknesses:

(1) Some of the data collected seem to be merely reported rather than synthesized and interpreted for the reader.

We agree that explicitly synthesizing these findings is essential for clarity. To improve this, we have revised the Results section to include concise summary statements at the conclusion of each major experimental paragraph (Lines 190-191, 201, 218-219, 229-231, 241-242, 272-274, 282-283; 291-293). These additions interpret the data in relation to our main hypothesis. The discussion section was thoroughly revised to more precisely explain the logic supporting the model (Lines 381-393; 433-443, 458-466). Additionally, to bring together the entire dataset, we introduced a new summary schematic (Figure 6A). This figure visually and conceptually integrates our diverse findings, covering metabolic treatments, pH fluctuations, and complex metabolite profiles, showing how these signals work together to control multienzyme complex assembly.

This is particularly true for data that seem to reflect more complex trends, such as the GCMS experiments that map metabolites across multiple experiments, or treatments that show somewhat counterintuitive results, such as the antimycin A treatment, which promotes rather than disrupts the MDH1-CIT1 interaction.

We agree that our complex datasets, including the metabolomics and the seemingly counterintuitive Antimycin A results, required deeper synthesis. To clarify the broader metabolic trends, we have added Figure 6A to visually map which factors, specifically pH, malate, fumarate, and aspartate, most consistently align with complex assembly. We revised the Discussion (Lines 390-393, 439-443) to explicitly conclude that no single variable predominantly governs the interaction, but it is coordinately regulated by multiple microenvironmental cues.

Regarding the Antimycin A (and other ETC inhibitors) discrepancy, where the interaction is enhanced despite suppressed respiration, we have expanded our interpretation (Lines 346–358) to explain this as a transient response that is not directly reflected by steadystate respiratory activity. Specifically, we propose that acute perturbations of the mitochondrial matrix microenvironment, particularly changes in pH, temporarily promote MDH1–CIT1 interaction. Thus, under these conditions, transient microenvironmental changes can dominate over steady-state respiratory output in regulating metabolon assembly.

The discussion paragraph about the imperfect relationship between pH and interaction has been revised to highlight our conclusion that mitochondrial matrix pH can be a contributing factor rather than the primary regulator (Lines 386-393).

(2) Some of the assertions put forth in the manuscript are not substantiated by the data presented, and the authors are at times overly reliant on previous findings from the literature to support their claims. This is particularly notable for claims about "TCA cycle flux"; the authors do not perform flux analysis anywhere in their study and should be cautious when insinuating correlations between their observations and "flux".

We appreciate the reviewer’s careful evaluation of our terminology and fully agree that claims regarding "flux" should be reserved for studies that employ direct isotopic flux measurements. In response to this constructive feedback, we have thoroughly reviewed the manuscript to ensure that our assertions are substantiated by the presented experimental data. We have carefully evaluated the use of the term "flux" throughout the Abstract, Introduction, and Discussion, replacing it with more accurate phrases such as "pathway activity," "respiratory activity," or "mitochondrial respiration" depending on the specific context (Lines 11; 20-21; 50; 111-112; 322-327; 329; 345; 349-350; 442-443; 458466).

We also removed a paragraph discussing the potential role of the MDH1-CIT1 metabolon in the malate-aspartate shuttle (Line 361). We realized the paragraph is highly speculative, and our data do not directly support the hypothesis. The influence of the MDH1-CIT1 on the malate-aspartate shuttle is a major finding of the upcoming manuscript reporting its effects in metabolic network flux. We apologize for mixing up the results of two separate studies.

Furthermore, we have revised our conclusions to avoid over-reliance on prior literature in making causal claims. We now explicitly frame the dynamic assembly of the MDH1-CIT1 metabolon as an integral factor in metabolic regulation, closely related to cellular metabolic states, rather than stating that it controls pathway flux (Lines 454-462). We believe these textual revisions accurately align our claims with our current observations and remove any unsubstantiated assertions.

(3) The manuscript presentation could be improved. For figures, at times, the axes do not have intuitive labels (example, Figure 1A), data points and details about the number of samples analyzed are missing (bar graphs and box plots), and molecular weight markers are not reported on western blots. The authors refer to the figures out of order in the text, which makes the manuscript challenging to navigate as a reader.

We thank the reviewer for these helpful suggestions to improve the clarity and presentation of the manuscript. We have made several revisions accordingly.

First, axis labels have been revised throughout the figures to improve clarity and make them more intuitive. Second, we have added the number of biological replicates to the figure captions and updated bar graphs and box plots to display individual data points. Third, to improve the transparency of the immunoblot data, we have included molecular weight marker position in Figure 1C and corresponding full gel images in a new Figure 1 – figure supplement 2. Other immunoblot images have been moved to Figure 2 – figure supplement 1 since they lack molecular marker images.

In addition, we have reorganized the figure panel labeling and corresponding text to improve the flow of the Results section. Specifically, figure subpanels are now arranged according to the measured parameters rather than treatment conditions, and the relevant sections describing TCA cycle manipulation and ETC inhibition have been revised to follow this updated figure order (Lines 208–231; 251–274). These changes improve the readability and logical progression of the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The grammar in the abstract in the sentence which states called metabolon. This needs to be fixed.

We thank the reviewer for pointing this out. We have revised the sentence in the Abstract to improve clarity. The revised sentence reads: “The tricarboxylic acid (TCA) cycle enzymes malate dehydrogenase (MDH1) and citrate synthase (CIT1) form a multienzyme complex, referred to as a metabolon, that channels intermediate oxaloacetate between their reaction centers.” (Lines 7-9)

Reviewer #3 (Recommendations for the authors):

Major points:

(1) Much of the data reported in this manuscript reads as a summary of what was found, rather than distilling what the trends in the data mean or how they support the proposed model.

We thank the reviewer for this comment. This concern overlaps with your previous point (Weakness 1), which we have addressed through revisions to improve synthesis and clarity. Specifically, we have added concise summary statements at the end of each major experimental section (Lines 190-191, 201, 218-219, 229-231, 241-242, 272-274, 282-283; 291-293), and we have included a new summary schematic (Figure 6A) that integrates the findings to illustrate how metabolic conditions and mitochondrial microenvironments relat to MDH1–CIT1 interaction. Together, these revisions improve the interpretation and clarify how the results support our model.

For instance, in Figure 3, the authors use one metabolic treatment to activate the TCA cycle and two to inhibit the TCA cycle. In Figure 3M, GC-MS data are reported for select metabolites across these three conditions, as well as a control condition. However, these metabolites don't follow clean "trends" according to the predictions; as one example, malate is down in the TCA active (acetate) and one TCA inhibited condition (arsenite), whereas it is elevated in the second TCA inhibited (aminooxyacetate) condition. As an additional example, glutamate is down in the arsenite (inhibited) condition, slightly down in the acetate (activated) condition, but is unchanged in the AOA (inhibited) condition. Similar variability is seen in Figure 4M. What do these discrepancies mean? How do they support the model? As written, these data bring forth more questions than they answer.

We appreciate the reviewer’s careful analysis of the metabolomics data in Figures 2E, 3M, and 4M. The reviewer notes that the levels of certain metabolites show complex patterns that do not simply reflect overall TCA cycle activity. We have acknowledged that our metabolomics dataset is a valuable resource for the research community and have added a brief paragraph to emphasize the complex metabolic phenotypes resulting from chemical treatments (Lines 422-431).

As mentioned in the paragraph, this complexity is biologically expected. It is likely from the distinct primary targets of each inhibitor, such as arsenite affecting redox-sensitive enzymes and AOA disrupting the malate-aspartate shuttle, as well as off-target effects and the adaptive reorganization of intersecting metabolic networks to bypass local blockades. Rather than viewing these diverse metabolic phenotypes as discrepancies, we leveraged them to uncouple general respiratory suppression from specific metabolite pools, allowing us to independently assess their relationship with metabolon assembly.

Furthermore, we note that our GC-MS analysis measures whole-cell metabolite levels, which represent the sum of multiple subcellular compartments and may not precisely reflect localized concentrations within the mitochondrial matrix that is directly affected by the TCA cycle. The description of this limitation of whole-cell metabolomics has been revised in Lines 417-420.

(2) Why do the authors propose that antimycin A increases the interaction between MDH1 and CIT1 despite decreasing respiratory activity? Given the generalities proposed in Figure 6, this is important to address.

We thank the reviewer for this comment. This point overlaps with Weakness 1, where we have addressed the apparent discrepancy associated with antimycin A (and other ETC inhibitors). Briefly, we have expanded our interpretation (Lines 349–360) to explain this effect as a transient response that is not directly aligned with steady-state respiratory activity. We propose that acute perturbations of the mitochondrial matrix microenvironment, particularly changes in pH, temporarily promote MDH1–CIT1 interaction. In addition, we have revised the Discussion (Lines 386–404) to clarify that mitochondrial matrix pH acts as a contributing factor rather than the primary regulator of the interaction. Together, these revisions reconcile the ETC inhibition by antimycin A with the overall model presented in Figure 6.

(3) The authors use acetate to "activate" the TCA cycle; do other non-fermentable carbon sources also promote the MDH1-CIT1 interaction?

We thank the reviewer for this insightful question. We have tested additional nonfermentable carbon sources and found that they did not significantly affect MDH1–CIT1 interaction (Figure 3—figure supplement 1). We note that raffinose present in the medium likely provides a baseline carbon source supporting oxidative metabolism, which may limit the observable effects of these treatments (Lines 149-150).

In addition, we performed a new experiment using ethanol. While ethanol treatment enhanced the MDH1–CIT1 interaction signal, it also increased the abundance of MDH1 and CIT1, resulting in a reduced interaction index. Because ethanol induces protein accumulation under our experimental conditions, this result is not straightforward to interpret. We have included this observation and its interpretation in the revised manuscript (Lines 208–211).

(4) The authors show that the MDH1-CIT1 interaction is sensitive to pH. Is the MDH1-CIT1 interaction affected by uncouplers in vivo?

We thank the reviewer for suggesting a meaningful experiment. We performed a new experiment examining the effect of the uncoupler CCCP on MDH1–CIT1 interaction in vivo (Figure 4—figure supplement 4). We found that CCCP treatment increased the interaction signal, consistent with the idea that acidification of the mitochondrial matrix promotes MDH1–CIT1 association.

However, we observe that CCCP treatment also decreased the luciferase signals from MDH1 and CIT1 fused to full-length NanoLUC in an abnormal way, making it harder to interpret the interaction index. Therefore, although these results support a possible role for pH in regulating the interaction, they should be viewed with caution and included as a figure supplement. This experiment and its interpretation have been added to the revised manuscript (Lines 276–283).

(5) NADH is a potent suppressor of many enzymes within the TCA cycle, including MDH1 and CIT1. Can the authors modulate mitochondrial NADH through genetic manipulation of Ndi1, or through overexpression of mito-Lb-NOX (PMID: 27124460)?

We thank the reviewer for this insightful suggestion. We agree that the mitochondrial NADH is a potential regulator of the MDH1-CIT1 interaction as it is a potent suppressor of many TCA cycle enzymes, and indeed, we have previously shown that NADH inhibit the MDH-CS interaction in vitro (Omini et al 2021 PMID: 34548590). For this reason, we investigated the mitochondrial matrix redox state that is related to the NADH levels in the current study. The reviewer’s proposed strategy of using targeted genetic tools like mito-Lb-NOX or Ndi1 manipulation to specifically influence the NADH level is an elegant approach to isolate this variable. However, implementing this system requires generating, optimizing, and validating new yeast strains that harbor the targeted NADH-modulating constructs alongside NanoBiT and full-length NanoLUC sensor systems. Because this extensive strain engineering and subsequent live-cell validation fall outside a feasible timeframe for the current manuscript revision, we must respectfully defer these experiments. We view the precise manipulation of the mitochondrial redox state via tools like mito-Lb-NOX as a complementary approach for our future work to systematically pinpoint the individual regulatory factors. We have expanded our Discussion (Lines 417-420; 462-465) to highlight the targeted genetic manipulation of the possible regulatory factors including the NADH pool, as a critical future direction for dissecting these dynamics.

(6) The authors should correct their figures:

(a) Axes should be easy to interpret on graphs.

(b) Individual datapoints should be shown on bar graphs and box plots. Minimally, the number of samples evaluated should be reported.

(c) Molecular weight markers should be reported on blots.

We thank the reviewer for these helpful suggestions. Points (a) and (b) overlap with Weakness 3, which we have addressed through revisions to improve figure clarity and data presentation. Specifically, axis labels have been revised to be more intuitive, the number of samples is now reported in the figure captions, and bar and box plots have been updated to include individual data points. For time-course data, we retained point-line plots, as alternative formats (e.g., bar or box plots) would reduce clarity due to the density of time points.

For point (c), we have added molecular weight markers to the immunoblot data where available (Figure 1C). In the time-course experiment in the original Figure 2, molecular weight markers were absent from the gel images. Although we are confident in the identity of the detected signals, we have moved these data to a figure supplement (Figure 2—figure supplement 1C) to reflect this limitation. Similarly, the corresponding Co-IP data are now presented as a figure supplement (Figure 2—figure supplement 1A).

Minor points:

(1) In the last paragraph before the results, the authors refer to "the fluorescent biosensors", but start the paragraph discussing the nanoBIT PPI. After reading the manuscript, these seem to be distinct experimental setups, but that was not evident in the first read through of the paper.

We thank the reviewer for pointing out this source of confusion. We apologize for the lack of clarity in distinguishing between the experimental approaches. In this study, the NanoBiT system was used to measure MDH1–CIT1 interaction, whereas fluorescent biosensors were used to assess mitochondrial matrix pH, redox state, and ATP levels. We have revised the paragraph to more clearly distinguish these methodologies and their respective roles in the study (Lines 105–112).

(2) As mentioned above, referring to multiple figures out of order within the manuscript is very jarring for the reader. The authors should consider reworking the narrative or figures to be presented in order.

We thank the reviewer for this comment. This concern overlaps with the previous comment regarding figure organization, which we have addressed by revising both the figure labeling and the corresponding text. Specifically, figure subpanels have been reorganized to follow the measured parameters rather than treatment conditions, and the Results sections describing TCA cycle manipulation and ETC inhibition have been revised to follow the updated figure order (Lines 208–231; 251–274). These changes improve the logical flow and readability of the manuscript.

Author response:

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

Reviewer #1 (Public review):

Summary:

This study investigated how visuospatial attention influences the way people build simplified mental representations to support planning and decision-making. Using computational modeling and virtual maze navigation, the authors examined whether spatial proximity and the spatial arrangement of obstacles determine which elements are included in participants' internal models of a task. The study developed and tested an extension of the value-guided construal (VGC) model that incorporates features of spatial attention for selecting simpler task mental representation.

Strengths:

(1) Original Perspective:

The study introduces an explicit attentional component to established models of planning, offering an approach that bridges perception, attention, and decisionmaking.

(2) Methodological Approach:

The combination of computational modeling, behavioral data, and eye-tracking provides converging measures to assess the relationship between attention and planning representations.

(3) Cross-validated data:

The study relies on the analysis of three separate datasets, two already published and an additional novel one. This allows for cross-validation of the findings and enhances the robustness of the evidence.

(4) Focus on Individual Differences:

Reports of how individual variability in attentional "spillover" correlates with the sparsity of task representations and spatial proximity add depth to the analysis.

We thank the Reviewer for their overall positive assessment of our work and their helpful comments. We have addressed each point below.

Weaknesses:

(1) Clarity of the VGC model and behavioral task:

The exposition of the VGC model lacks sufficient detail for non-expert readers. It is not clear how this model infers which maze obstacles are relevant or irrelevant for planning, nor how the maze tasks specifically operationalize "planning" versus other cognitive processes.

The method for classifying obstacles as relevant or irrelevant to the task and connecting metacognitive awareness (i.e., participants' reports of noticing obstacles) to attentional capture is not well justified. The rationale for why awareness serves as a valid attention proxy, as opposed to behavioral or neurophysiological markers, should be clearer.

We thank the reviewer for urging further clarity here. Our work builds closely on the previous maze navigation paradigm and VGC model developed and reported by Ho et al. Nature (2022). We directly adopted variants of their maze stimuli, computational model and obstacle awareness measures, and married these with an investigation of the role of visuospatial attention. We agree that it would be useful for the reader to have a more in-depth description of the paradigm and model, and how it operationalises planning, without needing to refer back to the original Ho et al. paper. We have now added additional explanatory sections to the Introduction and Methods as follows:

On page 4:

“One elegant approach to forming such a simplified representation is to adaptively select the granularity of information required to complete the task (Ho et al., 2022), known as value-guided construal (VGC). Unlike previous accounts, which model human planning as a search over all items (e.g.., tube lines), the VGC model predicts that a cognitively limited decision-maker selects a manageable subset of information over which to plan— i.e., a task representation—balancing utility and complexity (Ho et al., 2022). In our example, the VGC algorithm would plan over a few relevant tube lines rather than planning over all possible stations. To select the representation that achieves the best balance between utility and complexity, the model searches across all possible combinations of tube lines, computing the value (i.e., the plan’s utility minus its cost) of each representation for planning a specific journey. The algorithm then selects the representation with the highest value, which ensures that an ideal observer selects a representation which only includes the items (i.e., tube lines) that lead to successful planning while excluding as many items as possible to keep the plan as simple as possible. For our purposes, items included in the representation are considered taskrelevant, while items that are not represented are considered task-irrelevant. This algorithm, therefore, provides a normative standard of an efficient plan to which we can compare people’s actual plans.”

On page 6:

“We operationalized planning using a maze navigation paradigm, akin to our tube-related example, where participants were required to plan a route through the maze, avoiding obstacles that blocked their path. Obstacles predicted by the sVGC model to be included in the representation were considered task-relevant.”

“At the end of every trial, participants reported their awareness of specific obstacles (see Methods for details). The level of awareness reported for different obstacles provides a read-out of what features of the environment individuals were subjectively representing while solving a particular maze. While other markers of attention and awareness (for instance, behavioural or neurophysiological variables) could also be used, here we focused on direct awareness reports in order to relate our findings both to those of Ho and colleagues and to the subjective awareness reports used in consciousness science (e.g. the Perceptual Awareness Scale (Barnett et al., 2024; Overgaard & Sandberg, 2021; Ramsøy & Overgaard, 2004; Samaha et al., 2015)). Participants were instructed to maintain central fixation while planning (see dataset dSC 1), in line with previous empirical work using this task (Ho et al., 2022).”

To visualize our effects, we binarized the predictions of the sVGC model such that obstacles with a marginalized probability greater than 0.5 were considered taskrelevant, while other obstacles were considered task-irrelevant (e.g., Figure 2b). We now clarify this point in the caption of Figure 2.

(2) Attention framework:

The account of attention is largely limited to the "spotlight" model. When solving a maze, participants trace the correct trail, following it mentally with their overt or covert attention. In this perspective, relevant concepts are also rooted in attention literature pertaining to object-based attention using tasks like curve tracing (e.g., Pooresmaeili & Roelfsema, 2014) and to mental maze solving (e.g., Wong & Scholl, 2024), which may be highly relevant and add nuance to the current work. This view of attention may be more pertinent to the task than models of simultaneously tracking multiple objects cited here. Prior work (notably from the Roelfsema group) indicates that attentional engagement in curve-tracing tasks may be a continuous, bottom-up process that progressively spreads along a trajectory, in time and space, rather than a "spotlight" that simply travels along the path. The spread of attention depends on the spatial proximity to distractors - a point that could also be pertinent to the findings here.

Moreover, the tracing of a "solution" trail in a maze may be spontaneous and not only a top-down voluntary operation (Wong & Scholl, 2024), a finding that requires a more careful framing of the link to conscious perception discussed in the manuscript.

Conceptualizing attention as a spatial spotlight may therefore oversimplify its role in navigation and planning. Perhaps the observed attentional modulation reflects a perceptual stage of building the trail in the maze rather than a filter for a later representation for more efficient decision making and planning. A fuller discussion of whether the current model and data can distinguish between these frameworks would benefit readers.

We thank the reviewer for highlighting relevant findings in the attention literature that were missing from our discussion. We fully agree that a complete account of the interplay of planning, navigation, and attention is likely to recruit the kind of curvetracing processes highlighted by the reviewer. However, we emphasise that our current focus is not on the process of navigation through a maze, but on the process of construing the maze itself. In other words, we are focused not on how people represent their path from A to B, but how they represent the maze itself, which they then use as a basis for planning between A and B. The VGC model predicts that a subset of obstacles will be included in this construal. We think that a spotlight model is a good starting point for this work, because attention is being deployed across the whole maze stimulus, and then becomes attached to particular objects located in particular positions. This is a distinct process from that involved in navigating the path itself. Accordingly, our stimuli were designed such that task-relevant obstacles could be presented either proximally or distally to the optimal path (e.g., Figure 1a and Supplemental Figures S1-6). An obstacle that blocks any possible path on one side of the maze is task-relevant but located a long way from the optimal path. The results of Ho and colleagues’ (2022) third experiment demonstrate how task-relevant yet distal obstacles are better remembered than task-irrelevant proximal obstacles (see Figure 4 of Ho et al., 2022). We also observed that obstacles further away from the navigation path were often represented by participants (see Figures S1-6), which cannot be explained by curve tracing alone.

While these results cannot definitively rule out the possibility that participants automatically trace the path while also construing the maze, they suggest that the value-guided construal process is an independent predictor of participants’ representations beyond proximity to the navigated path. To make this distinction clearer, we now cite the papers alluded to by the reviewer, in the Discussion on pages 28-29, while also acknowledging the potential for investigating attention during the navigation process itself:

“Future work may also wish to examine the relevance of visuospatial attention for the navigation process itself in this task. While our present findings speak to how individuals perceive the maze while planning, it remains unclear how attention is deployed during navigation along a path, such as how object-based attention progressively spreads along trajectories in time and space(Pooresmaeili & Roelfsema, 2014; Wong & Scholl, 2024).”

There is also one additional nuance to the current spotlight model that we were inspired to consider by the reviewer’s comment. This is the idea that attentional effects may spread within or along the obstacles themselves. We cannot explore this in the current data because we asked for awareness of the entire obstacles, not parts of obstacles, but it may be possible to explore this in future work, for instance, with eye tracking measures.

More generally, the growth-cone (i.e., zoom lens) model of attention for curve tracing proposed by Roelfsema and colleagues shares considerable similarities with the spotlight of attention model. Both models argue for the grouping of spatially proximal items based on attention. While the growth-cone model argues for varying sizes of zoom lenses (i.e., receptive fields of neurons) that facilitate the tracing of proximal items, both models predict that spatially proximal items are preferentially processed together because of attention. Indeed, the spotlight model could model these varying zoom lenses by altering the width of the attentional spotlight dynamically across the visual scene based on the spatial proximity of obstacles. Following related comments by Reviewer 2, we now investigate inter-individual differences in the attentional spotlight of participants and observed that these differences significantly predict participants’ mental representations (see Attentional spotlight model of task representations). We have now updated the Discussion to include consideration of these alternative model frameworks:

On page 27:

“Second, in the current work we were unable to distinguish whether these attentional effects are driven by a fixed spotlight of attention, or whether attention operates akin to a zoom lens, shifting the ‘width’ of the focus of attention according to the task demands (Eriksen & St. James, 1986; Müller et al., 2003; Schad & Engbert, 2012). The latter view would be consistent with growth-cone models of attention in which the focus of attention expands and contracts in accordance with task demands, mirroring the various receptive field sizes in the visual hierarchy (Pooresmaeili et al., 2014; Pooresmaeili & Roelfsema, 2014). In partial support of this idea, we found significant inter-individual differences in the width of participants’ attentional spotlight (Figure S11). It is also possible that attention is deployed within or along parts of obstacles, rather than on entire obstacles. Future work using naturalistic measures of eye movements may be able to address these questions.”

(3) Lateralization of attention:

The analysis considers whether relevant information is distributed bilaterally or unilaterally across the visual display, but does not sufficiently address evidence for attentional asymmetries across the left and right visual fields due to hemispheric specialization (e.g., Bartolomeo & Seidel Malkinson, 2019). Whether effects differ for left versus right hemifield arrangements is not made explicit in the presented findings.

We thank the reviewer for this suggestion. To address this point, we fitted a three-way interaction model between VGC model prediction, lateralization index, and side (left vs right hemifield). We did not find evidence for the three-way effect (β= 0.01, SE= 0.02, 95% CI [-0.03, 0.04], p = 0.738; ΔBIC = 58.30 in favour of the null effect; see table below), suggesting that the side to which participants lateralized their attention did not influence their task representations. This result is now reported on page 12:

“This effect did not vary significantly as a function of the specific hemifield (i.e., left vs right) in which task-relevant information was presented (β= 0.01, SE= 0.02, 95% CI [-0.03, 0.04], p = 0.738; ΔBIC = 58.30 in favour of the null effect; see table S14).”

We also explored inter-individual differences in participants’ tendency to lateralize their attention (see also the next point). We observed that participants tended to lateralize their attention slightly more to the right-hand side for non-lateralized maze stimuli, despite the normative sVGC model predicting that participants should not lateralize their attention for these stimuli (Figure 3c). These results may speak to potential asymmetries in lateralization, but given the exploratory nature of these analyses, they should be verified and replicated in future work.

(4) Individual differences:

Individual differences in attentional modulation are a strength of the work, but similar analyses exploring individual variation in lateralization effects could provide further insight, and the lack of such analyses may mask important effects.

Thank you for this suggestion. In new analyses, we explored whether i) participants exhibited differences in their tendency to lateralize their awareness reports, and ii) whether the degree to which they tended to lateralize their awareness predicted their performance on a separate set of maze stimuli. In short, we observed substantial variation in participants’ tendency to lateralize their awareness (Figure S11) and found that this tendency reflected an inter-individual difference which was stable across maze types. We report these new findings on pages 14-16.

“Inter-individual variation in lateralization of attention

Next, we investigated participants’ tendency to pay attention to obstacles within a single hemifield (left vs right) regardless of the sVGC model predictions. To do so, we computed an awareness lateralization index (ALI) based on participants’ self-reported awareness reports of obstacles on each trial (Figure 3a). Large positive values indicate that participants were preferentially aware of the right hemifield, whereas negative values indicate preferential awareness of the left hemifield. Values close to zero indicate that participants paid attention to both hemifields equally (see Methods for details). We observed that participants’ tendency to lateralize their awareness varied greatly across the Ho datasets 1 and 2 (Figure 3b); some participants preferentially paid attention to a single hemifield, regardless of whether the sVGC model predictions were lateralized. For the dSC1 dataset, we observed that on some trials, participants significantly lateralized their awareness (|ALI| > 0.5; Figure 3c) even though the sVGC model predictions were non-lateralized. These findings suggest that participants’ tendency to pay attention to a single hemifield may represent an observable inter-individual difference in how they allocate their awareness to form task construals.”

“To further explore these inter-individual differences, we tested whether participants’ tendencies to lateralize their attention to a single hemifield was consistent across trials and maze stimuli. We observed that participants’ tendency to lateralize their attention to a single hemifield was similar for left and right lateralized maze stimuli (Spearman ⍴= 0.72, Figure 3d). This suggests that participants who preferentially attended to a single hemifield did so regardless of which hemifield they should attend to. More consequentially, the tendency for participants to lateralize their awareness on maze stimuli whose model predictions were also lateralized linearly correlated with participants’ tendency to lateralize their attention on non-lateralized maze stimuli (Spearman ⍴= 0.88, Figure 3d). Taken together, these findings emphasize that some individuals tend to preferentially attend to a single hemifield when planning. This tendency, importantly, represents an inter-individual difference in how participants allocate their attention across various maze types.”

(5) Distinction between overt and covert attention:

The current report at times equates eye movement patterns with the locus of attention. However, attention can be covertly shifted without corresponding gaze changes (see, for example, Pooresmaeili & Roelfsema, 2014).

We fully agree, and thank the reviewer for prompting further reflection on this distinction. In the online experiments run by Ho and colleagues (i.e., datasets Ho1 and Ho2), participants’ eye movements were not tracked, and therefore, they could not disambiguate whether participants were engaging in covert or overt attention to sample maze obstacles. In our third experiment (i.e., dataset dSC1), we both recorded eye movements and explicitly instructed participants to fixate centrally while viewing the maze. This ensured that participants oriented their attention only covertly during planning (see Figure S13-14).

We now elaborate on this important distinction in the Results section of the manuscript, page 12:

“In addition, we monitored participants’ eye movements in dataset dSC 1 to ensure that attention shifts would be covert as opposed to overt—a distinction which could not be determined in the online samples of datasets Ho 1 and 2.”

On page 28:

“Importantly, while the visuospatial attention effects observed in the Ho 1 and 2 datasets are likely driven by both covert and overt shifts in attention, the findings presented in experiment 3 (i.e., dSC1 dataset) rule out the contribution of overt shifts in attention through the use of eye tracking (see Figure S13-14)(Carrasco, 2011; Pooresmaeili & Roelfsema, 2014).”

The implications for interpreting the relationship between eye movement, memory, and attention in this setting are not fully addressed. The potential dynamics of attention along a maze trajectory and their impact on lateralization analysis would benefit from further clarification.

We thank the reviewer for urging more clarity here. The attentional dynamics we document in our study concern how people perceive / construe the maze itself, rather than how they deploy their attention to guide active navigation. We have now sought to make this distinction clear at a number of points in the paper. The core idea is that attention acts as an early filter to select which obstacles are part of a task construal, which then affects both awareness and memory.

We have now clarified the focus of our study in the introduction on pages 5-7:

“Our focus in this study was to examine how participants perceive and represent their environment (the maze stimulus). This is a distinct process to how participants orient their attention during navigation itself, which is not part of our current study. To do so, we harness classical signatures of attentional selection to characterise how visuospatial attention shapes awareness of maze obstacles during planning.” … “Our focus in the present study was to examine attentional effects on participants’ perception of the maze stimulus. We did not quantify how individuals deploy their attention in the phase in which they were navigating through the maze.”

We did not explicitly test for memory effects in our new experiments, but Ho and colleagues demonstrated that the sVGC model predicted not only awareness reports, but also participants’ memory of obstacles (see Ho et al., 2022). Indeed, task representations computed from memory or awareness reports were strikingly similar in their experiments (Spearman ⍴ = 0.86 between memory accuracy and awareness; ⍴ = 0.86 between confidence in memory and awareness). In relation to eye movements, we refer the reviewer back to our previous response, which details how eye movements were measured and controlled during maze construal.

Figure 1 legend (b) --> (c)

We have corrected this typo in the figure caption.

Reviewer #2 (Public review):

Summary:

Castanheira et al. investigate the role of spatial attention for planning during three maze navigation experiments (one new experiment and two existing datasets). Effective planning in complex situations requires the construction of simplified representations of the task at hand. The authors find that these mental representations (as assessed by conscious awareness) of a given stimulus are influenced by (spatially) surrounding stimuli. Individual participants varied in the degree to which attention influenced their task representations, and this attentional effect correlated with the sparsity of representations (as measured by the range of awareness reports across all stimuli). Spatially grouping taskrelevant information on either the left or right side of the maze led to mental representations more similar to optimal representations predicted by the valueguided construal (VGC) model - a normative model describing a theoretical approach to simplifying complex task information. Finally, the authors propose an update to this model, incorporating an attentional spotlight component; the revised descriptive model predicts empirical task representations better than the original (normative) VGC model.

Strengths:

The novelty of this study lies in the proposal and investigation of a cognitive mechanism through which a normative model like value-guided construal can enable human planning. After proposing attention as this mechanism, the authors make concrete hypotheses about mismatches between the VGC predictions and real human behavior, which are experimentally validated. Thus, not only does this study describe a possible mechanism for simplification of task information for planning, but the authors also propose a descriptive model, revising VGC to incorporate this attentional component.

A strength of this paper is the variety of investigative approaches: analysis of existing data, novel experiment, and a computational approach to predict experimental findings from a theoretical model. Analyzing pre-existing datasets increases the size of the participant cohort and strengthens the authors' conclusions. Meanwhile, comparing the predictions of the existing normative model and the authors' own refined model is a clever approach to substantiate their claims. In addition, the authors describe several crucial controls, which are key to the interpretability of their results. In particular, the eye tracking results were critical.

In summary, this paper constitutes an important step toward a more complete understanding of the human ability to plan.

We thank the Reviewer for their thoughtful and positive assessment of our findings. We also appreciate the constructive feedback on our methodology, which we believe has substantially improved our manuscript.

Weaknesses:

(1) There is a critical conceptual gap in the study and its interpretation, mainly due to the reliance on a self-report metric of awareness (rather than an objective measure of behavioral performance).

a. Awareness is tested by a 9-point self-report scale. It is currently unclear why awareness of task-irrelevant obstacles in this task would necessarily compromise optimal planning. There is no indication of whether self-reported awareness affects performance (e.g., navigation path distance, time to complete the maze, number of errors). Such behavioral evidence of planning would be more compelling.

We thank the reviewer for prompting further reflection on the connection between construal and navigation performance. We wish to emphasise that the primary focus of our study was on measuring and modeling participants’ task construals using perceptual awareness judgments, building on the methods developed by Ho and colleagues, rather than on navigation performance itself. However, as the reviewer points out, there is a natural relationship between construal and performance – if you represent the wrong obstacles, plans may be disrupted.

To explore the relationship between task construals and performance on the navigation task we first regressed out the effects of the sVGC model on participants’ awareness reports and computed the mean squared residuals for each trial. We then used these values to predict participants’ navigation response times on each trial. We observed a significant negative relationship, suggesting that on trials where participants’ representations showed greater deviations from the normative model, they were in fact faster at navigating the mazes. This relationship was surprising, and at odds with the initial idea that adhering to normative VGC aids in task performance. However, we think that this direction of effect may make sense if one considers that a large part of the actual construal (rather than the normative prediction) in our data was in fact driven by effects such as lateralisation which are not accounted for by the sVGC model. If one is faster at harnessing inductive biases such as lateralisation, then one may be faster to complete the maze but also show a greater deviation from the predictions of the original model.

To further explore these effects, we next focused on the distinction between lateralised and non-lateralised mazes. Here, we reasoned that the initial phase of lateralised attentional selection would lead to lateralised mazes being easier to navigate than nonlateralised ones. We conducted new analyses to determine whether participants navigated lateralized maze stimuli faster and with fewer moves than maze stimuli with non-lateralized model predictions. As detailed in Methods, we excluded trials in which participants significantly deviated from the optimal number of moves (9 or more moves) and took longer than 20 seconds to solve the maze. In line with our interpretation that attention operates as an inductive bias, participants were faster and deviated less from the optimal path on lateralized compared to non-lateralized mazes.

We now report these new results on navigation performance on pages 20-21:

“Maze navigation performance

The previous analyses focused on participants’ task representations during planning. We next sought to explore links between participants’ task representations and maze navigation performance. Participants performed the maze navigation task near-ceiling: they solved 95% of maze stimuli in under 20 seconds, with minimal deviation from the optimal path (i.e., 9 moves or fewer). Notwithstanding this limited variance in task performance, we explored whether participants’ task construals may have impacted their navigation speed. To do so, we first regressed out the effects of the sVGC model from participants’ awareness reports and used the mean squared residuals for each trial to predict response times (see Methods for details). Surprisingly, we observed a negative relationship between mean squared residual variance and response times (β = -0.31, SE = 0.05, 95% CI [-0.41, -0.21], p < 0.001), indicating that participants were faster on trials where the sVGC model explained less variance in their awareness reports. In other words, trials in which participants deviated more from the sVGC model predictions were solved faster. We note that one reason for this may be the strong influence of the lateralisation effect on navigation performance (see paragraph below), which itself is not part of the sVGC model prediction.”

“We then explored whether participant performance differed between lateralised and nonlateralised mazes. Here, we reasoned that the initial phase of lateralised attentional selection would lead to lateralised mazes being easier to navigate than non-lateralised ones. Consistent with this hypothesis, participants were faster (β = -0.04, SE = 5.91*10³, 95% CI [-0.06, -0.03], p< 0.001) and followed the optimal path more closely (β = -0.59, SE = 0.09, 95% CI [-0.78, -0.40], p< 0.001) when maze stimuli were more lateralized.”

And in the Discussion section, on page 23:

“Mental representations and task performance

We observed that participants were faster and deviated less from the optimal path on maze stimuli that were lateralized. This effect is not predicted by the original sVGC model but dovetails with the interpretation that early visuospatial attention operates as an inductive bias to guide the formation of simplified task representations. Surprisingly, we also observed that participants were faster to navigate mazes on trials where their simplified task representation deviated from the sVGC model prediction. We interpret this seemingly contradictory finding in the following way: there are several factors beyond the sVGC model – including, for instance, maze lateralisation – that predict both construal and performance on the maze navigation task. Further work is needed to understand how inductive biases such as lateralisation shape both construal and performance, and the real-world benefits that such strategies might afford for naturalistic stimuli.”

b. Relatedly, it would have been more convincing to have an objective measure of awareness, for instance, how the presence or absence of a "task-irrelevant" obstacle affects performance (e.g., change navigation path distance or time to complete the maze), or whether participants can accurately recall the location of obstacles.

We thank the reviewer for prompting further reflection on the validity and robustness of our awareness measures. We emphasise however that our focus is not (primarily) on maze navigation performance, but on task construal, which as noted in our previous response may come apart from navigation performance for a variety of reasons. Our primary goal is to measure participants’ subjective awareness of the maze as a marker of their idiosyncratic (conscious) mental representation on each trial. In doing so, we build on a rich tradition of measuring subjective awareness in consciousness and perception science (for instance, work using the Perceptual Awareness Scale, or detection judgments). In this sense, we think our awareness scale (following Ho et al.) represents a valid and straightforward way of assessing our target psychological construct. However, we also agree with the Reviewer that convergent evidence from other measures is always valuable. In Ho and colleagues’ original paper, they developed a variant of the maze task where participants had to recall the location of obstacles, as well as rate their awareness (Exp 3) and a variant in which participants could hover their mouse over hidden obstacles in the maze to reveal their location – an online metric of attentional deployment (Exp 4). These data afforded us the opportunity to validate the awareness reports against an objective measure of recall, as suggested by the Reviewer. In reanalysing these data, we observed that the obstacle awareness and memory/hover measures were strikingly correlated within two independent samples of participants (Spearman ⍴ = 0.86 between memory accuracy and awareness; ⍴ = 0.86 between confidence in memory and awareness; ⍴ = 0.76 between the probability of hovering over the obstacle and awareness; ⍴ = 0.65 between the duration of the mouse hovering and awareness). These re-analyses are now reported on page 22 of our manuscript, to highlight the convergent validity of the awareness metric:

“Finally, we examined the convergent validity of participants’ awareness reports by reanalyzing the memory recall data reported in Ho and colleagues’ experiment(Ho et al., 2022). We reasoned that participants should demonstrate similar task representations regardless of the measure used to probe the construal. In line with this prediction, we observed that the obstacle awareness reports and memory/hover measures were strikingly correlated within three independent samples of participants (Spearman ⍴ = 0.86 between memory accuracy and awareness; ⍴ = 0.86 between confidence in memory and awareness; ⍴ = 0.76 between the probability of hovering over the obstacle and awareness; ⍴ = 0.65 between the duration of the mouse hovering and awareness; see Tables S18 and S19).”

c. Consequently, I'm not sure that we can conclude that the spatial context does impact participants' ability to plan spatial navigation or to "incorporate taskrelevant information into their construal". We know that the spatial context affects subjective (self-reported) awareness, but the authors do not present evidence that spatial context affects behavioral performance.

Following the line of argument above, we think it’s important to separate out task construal (the simplified representation of the maze, measured by awareness reports), and the impact of this on navigation and other aspects of behaviour. The awareness reports (and other convergent measures) show that task-relevant information (as predicted by the VGC) is incorporated into the construal, a process which is modulated by spatial context. These are the key targets of our modeling. Whether this impacts performance is a distinct question, and one that we now address in our response to point a above.

d. Another concern that may complicate interpretation is the following: Figure 3c shows improved VGC model predictions (steeper slope) for mazes with greater lateralization. However, there are notable outliers in these plots, where a high lateralization index does not correspond to good model performance. There is currently no discussion/explanation of these cases.

The Reviewer astutely points out some outliers in our analysis. While on average lateralized maze stimuli are represented more closely to the sVGC model, there are indeed some noticeable outlier mazes. These mazes represent stimuli in which participants tended to lateralize their attention to the ‘wrong hemifield’—e.g., participants were more aware of obstacles in the right hemifield despite sVGC model predicting that obstacles on the left hemifield were task-relevant. We believe this explains the poor sVGC model fits on these trials. We note, however, that on average participants were capable of attending to the correct hemifield without explicit instructions (i.e., 9 out of 12 mazes).

We have now included a discussion of these outliers in the results section of the paper on page 12:

“We note that for three maze stimuli whose model predictions were lateralized there was nevertheless a poor fit to the sVGC model (see Figure 2c, right panel). These outliers correspond to maze stimuli where participants, on average, lateralized their attention to the incorrect hemifield (i.e., the opposite hemifield to that predicted by the sVGC model).”

(2) I noticed an issue with clarity regarding task-relevance. It is currently not fully clear which obstacles are "task irrelevant". Also, the term is used inconsistently, sometimes conflating with "awareness". For example, in the "Attentional spotlight model of task representations" section, the authors state that "taskrelevant information becomes less relevant when surrounded by task-irrelevant information". But they really mean that participants become less aware of those task-relevant obstacles. I assume task-relevance is an objective characteristic related to maze organization, not to a participant's construal. Indeed, the following paragraph provides evidence of model predictions of awareness.

We apologize for any confusion regarding the terminology of our manuscript. We indeed use the terms task-relevant and task-irrelevant to refer to obstacles that are objectively predicted by the normative sVGC model or the attentional spotlight model to be included in (>0.5) or excluded from (<0.5) task construals, respectively. This designation reflects the predictions from the computational model and does not reflect participants’ reported awareness. We then ran linear hierarchical models to predict participants’ awareness reports from these model predictions. The Reviewer is correct that the task-relevance of obstacles is indeed related to the maze’s organization, and not related to participants’ subjective reports of awareness. We have now clarified this point throughout the manuscript to better emphasize the difference between the model predictions of taskrelevance and participants’ subjective reports.

On page 17:

“To achieve this, we computed the predictions of the existing VGC model for each obstacle’s task relevance in a given maze, and averaged these predictions within an attentional spotlight of 3 squares (Figure 4a & S8, see Methods for details). This process yielded novel model predictions, whereby some obstacles which were once predicted as task-irrelevant by the normative sVGC are now predicted as task-relevant by the attentional spotlight model. We depict the effects of this spatial spotlight in Figure 4a: task-irrelevant stimuli (plotted in grey; see middle left obstacle) neighbouring taskrelevant obstacles (plotted in orange) become more task-relevant, whereas taskrelevant information becomes less relevant when surrounded by task-irrelevant information (see bottom right orange obstacle). This deviation in model predictions from the normative sVGC model was used to predict participants’ awareness reports. We hypothesized that this spotlight-VGC model would predict participants’ reports better than the original VGC model, which does not account for spatial attention.”

(3) The behavioral paradigm has some distinct disadvantages, and the validity of the task is not backed up by behavioral data.

a. I understand the need for central fixation, but it also makes the task less naturalistic.

The fixation cross was required on every trial such that participants could maintain central fixation for our eye tracking experiment. While this design is less naturalistic, it allows us to examine the eye movements of participants. Requiring participants to fixate during the ‘planning’ phase of the experiment allowed us to isolate the effects of covert attention from changes in awareness due to overt shifts in attention. In other words, differences in participants’ awareness reports in the 3rd experiment cannot be explained by longer fixation times to specific obstacles.

b. The task with its top-down grid view does not seem to mimic real human navigation. Though this grid may be similar to mental maps we form for navigation, the sensory stimuli corresponding to possible paths and to spatial context during real-life navigation are very different.

We agree with the reviewer that while our task is engaging for participants and simple to follow, it does not mimic naturalistic navigation in humans. There is a natural tension in computational / experimental work in cognitive science in wanting to build closely on previous results and paradigms, while ensuring that results can generalise to real-world contexts. Here, our choice of paradigm and measures was closely built on previous papers using this task from Ho and colleagues (2022, 2023). While preparing this response, we learnt that the MIT group had also harnessed this same task to develop a novel dynamic variant of the VGC model (Chen et al., 2026) called the Just in Time model (JIT). The advantage of building on this prior work is that we are able to iteratively refine and expand the VGC approach, and (in our case) bring it into closer contact with work on modeling the deployment of spatial attention in human vision. The top-down aspect of the maze notably facilitated the study of the spatial deployment of attention. We now discuss the novel dynamic variant of the VGC model in our paper on page 27:

“We close by reflecting on opportunities for further work in this area. First, an important next step is to explore the process by which task representations are formed, and how inductive biases might affect the process of task construal. The sVGC model is a normative model of the optimal task representation. Since it’s construction involves an exhaustive calculation over possible paths, it is not a plausible basis for a model of the psychological process by which participants actually construct task representations. More recently a process model of task construal has been proposed, the Just in Time model (JIT). The hypothesis of the JIT model is that participants’ task representations are built up over time by iteratively simulating possible paths through the maze, affording insight into the construal process (Chen et al., 2026). In future work, it would be of interest to ask whether the attentional effects we observe in our experiments could be meshed with a dynamic JIT account of construal. We speculate that visuospatial attention may operate as an early filter, limiting the space of potential construals based on coarse spatial features of the environment, constraining a dynamic selection of obstacles. Brain imaging techniques with high time resolution, such as M/EEG, may be able to shed further light on how task representations are formed as participants plan.”

c. Behavioral performance is not reported, so it is unknown whether participants are able to properly complete the task. The task seems pretty difficult to navigate, especially when the obstacles disappear, and in combination with the central fixation.

Behavioural performance is now reported in response to point 1a above.

d. There is no discussion of whether/how this navigation task generalizes to other forms of planning.

We fully agree that an important next step would be to generalise our results on construal to naturalistic forms of planning – for instance, using immersive VR mazes, and or investigating cognitive rather than perceptual construals. We have now added a line to this effect to the Discussion on page 28.

“An important next step to further our understanding of task representations would be to extend the current paradigm to other forms of planning and more naturalistic tasks, such as navigating immersive virtual reality (VR) environments, planning over cognitive rather than perceptual representations (e.g. planning over an abstract space), or internallyguided planning based on working memory.”

Reviewer #2 (Recommendations for the authors):

(1) There are, of course, benefits to simple tasks like the ones described, but it would be interesting to compare the results to a possible experiment in which a top-down grid/map is used for planning, but then task execution is carried out in a simulated environment corresponding to the map. Also, perhaps beyond the scope of the questions addressed in this paper, but I am curious how unexpected obstacles affect representations. For instance, if participants plan based on a topdown map and then begin "real" navigation but encounter an unexpected obstacle that was not indicated on the map, does this modulate representations/awareness of future obstacles (near vs. far)?

We fully agree that all of these lines of investigation would be super interesting to pursue in future studies, and we have added a line to the discussion to that effect on page 28:

“An important next step to further our understanding of task representations would be to extend the current paradigm to other forms of planning and more naturalistic tasks, such as navigating immersive virtual reality (VR) environments, planning over cognitive rather than perceptual representations (e.g.. planning over an abstract space), or internallyguided planning based on working memory.”

(2) Regarding self-reported awareness as a metric, an additional experiment could ask participants to recreate the maze (identify locations of obstacles after they disappear). This would be a more objective measure of awareness.

Yes indeed, and as described above, this was a metric used by Ho and colleagues in their previous experiment. As we describe in more detail above, the task representations obtained via memory or awareness reports demonstrated striking similarity (⍴ = 0.86).

(3) What is meant by "all possible orientations of the maze" in this Methods sentence: "For dataset dSC 1, participants solved each of these 24 mazes four times (i.e., all possible orientations of the maze)"?

We thank the Reviewer for prompting more clarity here. We vertically and horizontally reversed mazes (i.e., left-right flipped) such that participants could not predict the location of the goal or start location. In this way, each maze stimulus had four potential orientations. This resulted in 96 trials of 24 unique mazes. We have clarified this point in the Methods section on page 30:

Maze stimuli were vertically and horizontally reversed (i.e., left-right flipped) such that participants could not predict the location of the start or goal location. This resulted in four potential orientations of each maze across all 24 mazes, 96 trials in total.

(4) For lateralization, it was unclear until reading the Methods that the lateralization index was calculated using the VGC-predicted level of taskrelevance. From the main text and Figure 2, I assumed you were just counting the number of task-relevant obstacles on each side, rather than also quantifying relevance. I understood after reading the Methods, but this could be clarified further.

We agree with the Reviewer that this was not evident from the text. We have now updated the Results section of the manuscript to clarify this point on page 11:

“To test this hypothesis, we derived a measure of task-relevant lateralization inspired by the attention literature (Ghafari et al., 2024; Keefe & Störmer, 2021; Vollebregt et al., 2015) (Figure 2a). Specifically, we separated maze stimuli across the vertical meridian and computed the ratio of task-relevant information presented on the left versus right side derived from the sVGC model. For example, the maze shown in Figure 2a has twice the amount of task-relevant information presented in the left hemifield than in the right (lat. Index= 1/3). A lateralization index of 0.0 indicates that both hemifields contain equal amounts of task-relevant information (i.e., non-lateralized). The lateralization index was computed using the continuous VGC predictions for each obstacle (see Methods).”

(5) The explanation in the Methods of how the width of the attentional spotlight was chosen references Figure 1b and Supplementary Figure S2, but it seems that Supplementary Figure S8 explains this more in the caption. Also, I don't see how Figure S2 supports this.

We apologize for this typo. The explanation of how we selected the width of the attentional spotlight should indeed reference supplemental Figure 15 (previously Figure S8). We have now corrected this and elaborated on this choice in the Methods section on page 35:

“We fixed the ‘width’ of the attentional spotlight to a distance of 3 squares based on the observation that the two neighbouring obstacles positively predicted the awareness of a probe. We observed that the mean and median distance between neighbouring obstacles of the 2nd rank (i.e., second closest) was 3 squares away for all mazes (Figure S15). We therefore opted to fix the value of the attention spotlight to 3 squares based on these observations. Future work utilizing this model should consider the statistics of their maze stimuli when deciding on the ‘width’ of the attentional spotlight.”

(6) The attentional spotlight width was assumed to be 3 squares, based on the linear regression predictions of the effect of neighboring obstacles on stimulus awareness. Given the individual differences across participants, it would be interesting to choose a different attentional spotlight size for each participant. Would a participant-specific attentional spotlight width improve the predictions of the spotlight-VGC model?

The Reviewer highlights a very interesting question: do individuals vary in terms of their attentional spotlight? To test this hypothesis, we first estimated the size of the attentional spotlight for each individual based on lateralized maze stimuli, and then used this to generate personalized attentional spotlight model predictions for each subject based on these values (Figure S11). We restricted this analysis to the dSC1 dataset, where we had substantially more trials (96 in total).

In brief, we observed that indeed the personalized spotlight model fit participants’ awareness reports better than both a normative sVGC model and a group-level attentional spotlight model. We interpret these findings with some caution as i) a subset of individuals had flat attentional slopes and therefore were excluded from these analyses, and ii) we believe we require additional trials to ensure a robust model fit at the individual level. While our results are encouraging, we hope future investigations into inter-individual differences will extend these findings.

We have included these additional analyses in the main text.

On page 18:

“To further explore inter-individual differences in task construal, we tested whether adjusting the attentional spotlight width to each participant’s awareness reports improved the predictions of the attentional spotlight model. To do so, we first determined the width attentional spotlight of each individual in the dSC1 dataset based on lateralized maze stimuli. We then generated person-specific attentional spotlight model predictions for the non-lateralized maze stimuli to avoid overfitting the data (Figure S11). We note that 7 participants had either flat attentional slopes or negative beta coefficients, which prevented the selection of an appropriate attentional spotlight width (see Methods for details). We observed a significant improvement in model fit for the person-specific attentional spotlight model relative to both the group-level attentional spotlight model (ΔBIC= -1487.39) and the normative sVGC model (ΔBIC= -1655.29). While the limited trial numbers per participant in our current dataset warrants caution in interpreting these findings, these findings do encourage further research on inter-individual differences in attentional deployment during planning.”

On pages 23-24:

“Inter-individual differences in attention

We also observed considerable inter-individual differences in attentional effects across participants (Figure 1c). While some participants were strongly influenced by the spatial context of neighbouring stimuli, others showed more limited evidence for an attentional effect (Figure 1b). Inter-individual differences in attention predicted the sparsity of participants’ simplified representations: participants with larger attention effects exhibited sparser representations. Moreover, these inter-individual differences in effects of spatial proximity could be incorporated into the attentional spotlight model by varying the width of the spotlight, resulting in better model predictions.”

“Beyond these spatial proximity effects, we also observed that participants varied in their tendency to lateralize their attention to a single hemifield (Figure 3). This tendency was observed across all three datasets, including on maze stimuli whose value-guided model predictions were not lateralized. This suggests that although a strategy of allocating attention is sub-optimal for these maze stimuli, some individuals preferentially attend to a single hemifield in a heuristic-like fashion. This tendency to attend to a single hemifield was a robust inter-individual difference across maze stimuli (Figure 3d), and dovetails with individual-level variation in spatial proximity effects. Taken together, these findings offer novel insights into how people vary in the ways they allocate spatial attention to solve complex problems. Future research could explore how these individual differences constrain performance on other tasks that require planning and search in highdimensional spaces.”

On page 17 of the Supplemental Materials:

(7) The supplementary text about lateralization effects, above Supplementary Table S8, references Table S6, but it is Table S6 does not seem to display lateralization results.

We thank the Reviewer for pointing out this typo: we now refer to the correct supplementary table (S9).

(8) Why does it matter that "the maze stimuli were not designed to test horizontalmeridian lateralization effects"? What is the effect on power? Is it because there is not a good enough range in lateralization indices? It would be good to clarify, or just remove that explanation, since the cortical retinotopy explanation seems more convincing.

We did not specifically design the maze stimuli such that there is an equal number of obstacles above and below the horizontal meridian. As such, the lateralization index derived along the horizontal meridian does not control for the number of obstacles in each hemifield, which may influence participants’ awareness reports. In contrast, we designed maze stimuli such that this would not be a concern for the vertical meridian. We have clarified this point in the discussion on page 27.

“Third, while we observed clear lateralization effects along the vertical meridian (i.e., left vs right hemifield), effects along the horizontal meridian were less clear (i.e., above vs below; see Table S15-16). One potential explanation of this asymmetry is the retinotopic organization of the cortex, in which spatially adjacent stimuli can be retinotopically distant if presented on the opposite side of the vertical (but not horizontal) meridian, facilitating distractor inhibition. Importantly, while the visuospatial attention effects observed in the Ho 1 and 2 datasets are likely driven by both covert and overt shifts in attention, the findings presented in experiment 3 (i.e., dSC1 dataset) rule out the contribution of overt shifts in attention through the use of eye tracking (see Figure S13-14)(Carrasco, 2011; Pooresmaeili & Roelfsema, 2014).”

(9) For Figure 2c, it would be helpful to directly state what each dot and line mean.

We updated the caption of Figure 2c to clarify what we are plotting: each point represents an obstacle, and each line the linear fit for a maze stimulus.

“Each point represents an obstacle in a maze, and each line represents the model fit for that specific maze stimulus.”

(10) Figures and wording imply there is only a single probe obstacle per trial, but methods and model imply that participants are asked to report awareness for every obstacle. This should be clarified.

We apologize for any confusion regarding the methodology of our study. The Reviewer is correct that participants reported their awareness of every obstacle presented on a given trial. We have clarified this in the Results section of the manuscript on page 7:

“Note, participants reported their awareness of every obstacle presented on a given trial.”

We have also updated the caption of Figure 1 to clarify this point:

“Once participants finished navigating the maze, they were asked to report their awareness of every obstacle presented on a given trial in a random order.”

(11) What is the reason for the exclusion of participants (33 for experiment 1 and 26 for experiment 2)?

Participants were excluded from the Ho et al. datasets 1 and 2 based on their preregistered exclusion criteria, as detailed in the Methods section of their paper. In short, trials were excluded if participants took longer than 20 seconds to complete the trial, or if they spent longer than 5 seconds in the initial state. Participants were excluded if less than 80% of trials remained after reaction time exclusions or if they failed 2 out of 3 comprehension checks. We have elaborated on this point in the Methods section on page 31.

“Participants were excluded from analyses based on pre-registered exclusion criteria as detailed in (Ho et al., 2022). In short, participants were excluded if 20% or more of their trials were removed based on reaction times, or if they failed 2 out of 3 comprehension checks.”

(12) The supplemental figures are not referenced in order, and some are not referenced at all; this should be fixed.

We thank the Reviewer for pointing this out and have reorganized our Supplementary materials accordingly.

Reviewer #3 (Public review):

Summary:

The authors build on a recent computational model of planning, the "value-guided construal" framework by Ho et al. (2022), which proposes that people plan by constructing simple models of a task, such as by attending to a subset of obstacles in a maze. They analyze both published experimental data and new experimental data from a task in which participants report attention to objects in mazes. The authors find that attention to objects is affected by spatial proximity to other objects (i.e., attentional overspill) as well as whether relevant objects are lateralized to the same hemifield. To account for these results, the authors propose a "spotlight-VGC" model, in which, after calculating attention scores based on the original VGC model, attention to objects is enhanced based on distance. They find that this model better explains participant responses when objects are lateralized to different hemifields. These results demonstrate complex interactions between filtering of task-relevant information and more classical signatures of attentional selection.

Strengths:

(1) The paper builds on existing modeling work in a novel manner and integrates classic results on attention into the computational framework.

(2) The authors report new and extensive analyses of existing data that shed light on additional sources of systematic variability in responses related to attentional spillover effects

(3) They collect new data using new stimuli in the original paradigm that directly test predictions related to the lateralization of task-relevant information, including eye tracking data that allows them to control for possible confounds.

(4) The extended model (spotlight-VGC) provides a formal account of these new results.

We thank the Reviewer for their positive assessment of our manuscript and their insightful comments, which has improved the clarity of our findings.

Weaknesses:

(1) The spotlight-VGC model has a free parameter - the "width" of the attentional spotlight. This seems to have been fixed to be 3 squares. It would be good if the authors could describe a more principled procedure for selecting the width so that others can use the model in other contexts.

Our choice for this parameter was informed by the spatial effects reported in Figure 1b. We observed that the two closest neighbouring obstacles to a probe had similar awareness (i.e., positive beta weights). We therefore compute the mean and median distances between obstacle pairs that were the second closest obstacle to a probe. This distance was 3 squares away, as depicted in Figure S15. We fixed the width of the attentional spotlight across all studies based on this observation. We agree that future research utilizing this model may need to tune this hyperparameter depending on the mean distance between a probe and its neighbours.

We have clarified this point in the methods section on page 35:

“We fixed the ‘width’ of the attentional spotlight to a distance of 3 squares based on the observation that the two neighbouring obstacles positively predicted the awareness of a probe. We observed that the mean and median distance between neighbouring obstacles of the 2nd rank (i.e., second closest) was 3 squares away for all mazes (Figure S15). We therefore opted to fix the value of the attention spotlight to 3 squares based on these observations. Future work utilizing this model should consider the statistics of their maze stimuli when deciding on the ‘width’ of the attentional spotlight.”

Following the suggestion of Reviewer 2 point 6, we now also explored inter-individual differences in this parameter. To do so, we first used the lateralized mazes in the dSC1 dataset to determine the optimal width of the attentional spotlight for each individual.

Then, we used this spotlight to derive model predictions for each person. We observed that these personalized attentional spotlight model predictions fit participants’ awareness reports on non-lateralized mazes better than the fixed-width spotlight model. We believe this preliminary result suggests the importance of modelling inter-individual differences in attentional deployment during planning. We report these effects on page 17.

(2) Have the authors considered other ways in which factors such as attentional spillover and lateralization could be incorporated into the model? The spotlightVGC model, as presented, involves first computing VGC predictions and only afterwards computing spillover. This seems psychologically implausible, since it supposes that the "optimal" representation is first formed and then it gets corrupted. Is there a way to integrate these biases directly into the VGC framework, perhaps as a prior on construals? The authors gesture towards this when they talk about "inductive biases", but this is not formalized.

We thank the reviewer for bringing up this very important point. We think that a full computational treatment of the inductive bias would be a distinct project, but now seek to expand our discussion on the mechanisms by which representations could be formed. In this context, we specifically highlight novel computational work from the MIT group that was published as a preprint in the time since we submitted our paper, and which proposes a new process account of construal, the “Just in Time” (JIT) model. We also elaborate on a possible mechanism by which visuospatial attention may aid the dynamics of the construal process. In short, we agree with the reviewer that spatial attention may bias individuals to search over a subset of potential representations based on low-level spatial characteristics of the obstacles (e.g., their spatial spread in the visual field), prior to (or in concert with) a dynamic JIT-like selection process. We now elaborate on these possibilities on pages 27-28:

“We close by reflecting on opportunities for further work in this area. First, an important next step is to explore the process by which task representations are formed, and how inductive biases might affect the process of task construal. The sVGC model is a normative model of the optimal task representation. Since it’s construction involves an exhaustive calculation over possible paths, it is not a plausible basis for a model of the psychological process by which participants actually construct task representations. More recently a process model of task construal has been proposed, the Just in Time model (JIT). The hypothesis of the JIT model is that participants’ task representations are built up over time by iteratively simulating possible paths through the maze, affording insight into the construal process (Chen et al., 2026). In future work, it would be of interest to ask whether the attentional effects we observe in our experiments could be meshed with a dynamic JIT account of construal. We speculate that visuospatial attention may operate as an early filter, limiting the space of potential construals based on coarse spatial features of the environment, constraining a dynamic selection of obstacles. Brain imaging techniques with high time resolution, such as M/EEG, may be able to shed further light on how task representations are formed as participants plan.”

[…]

“Fourth, it will also be necessary to elaborate on how bottom-up and top-down aspects of attentional selection are combined to guide complex task representations and plans. Foundational questions remain unanswered, for instance: can multiple spatial locations be preferentially selected at once, i.e. are there multiple spotlights (Awh & Pashler, 2000; McMains & Somers, 2004; Pylyshyn & Storm, 1988; Shaw & Shaw, 1977)? There is also discourse on how spatial attention may move from one location to another: are the intervening visual regions between attended locations similarly selected (Dubois et al., 2009; Kr & Np, 1999; McMains & Somers, 2004, 2005)? Our findings tentatively suggest that individuals are able to attend to disparate spatial regions to form sparse task representations, yet there is substantial variability in how individuals orient their attention during the task. The present paradigm and computational modelling, in conjunction with carefully designed stimuli, may help resolve these outstanding questions.”

(3) Can the authors rule out that the lateralization effects are the result of memory biases since the main measure used is a self-report of attention?

We thank the reviewer for bringing up this important point. In our experiments, we sought to measure participants’ subjective awareness of the maze stimuli as a readout of their conscious task representation on each trial. This approach marries an extensive literature on measures of perceptual awareness in consciousness science (e.g., using the Perceptual Awareness Scale) with computational models of planning. Participants’ memory of (their awareness of) the obstacles is inherent to this approach, but just as with similar approaches in consciousness science (e.g. measures of iconic memory in the Sperling paradigm), we think it provides a reasonably “online” measure of awareness. It’s important of course to ensure that results obtained with awareness reports are not idiosyncratic, and generalise to other approaches to quantifying task representations.

To further bolster the convergent validity of our awareness measure, we reanalyzed the data from Ho and colleagues. In their original paper, they developed a variant of the maze-navigation task where participants were asked to recall the location of obstacles as well as report their awareness (Exp 3) and a third variant of the task where participants could hover their cursors over hidden obstacles to reveal their locations (Exp 4). These data allowed us to validate the awareness reports against objective measures of recall and mouse-tracking data. We observed that the subjective awareness reports of participants were strikingly correlated with recall/hover measures across two independent samples of participants (Spearman ⍴ = 0.86 between memory accuracy and awareness; ⍴ = 0.86 between confidence in memory and awareness; ⍴ = 0.76 between the probability of hovering over the obstacle and awareness; ⍴ = 0.65 between the duration of the mouse hovering and awareness). We believe these findings validate participants’ awareness reports. These findings are now reported on page 22 of the manuscript.

“Finally, we examined the convergent validity of participants’ awareness reports by reanalyzing the memory recall data reported in Ho and colleagues’ experiment (Ho et al., 2022). We reasoned that participants should demonstrate similar task representations regardless of the measure used to probe the construal. In line with this prediction, we observed that the obstacle awareness reports and memory/hover measures were strikingly correlated within three independent samples of participants (Spearman ⍴ = 0.86 between memory accuracy and awareness; ⍴ = 0.86 between confidence in memory and awareness; ⍴ = 0.76 between the probability of hovering over the obstacle and awareness; ⍴ = 0.65 between the duration of the mouse hovering and awareness; see Tables S18 and S19).”

Author response:

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

Reviewer #1 (Public review)

Summary:

In this manuscript the authors derive a mean-field model for a network of Hodgkin-Huxley neurons retaining the equations for ion exchange between the intracellular and extracellular space.

The mean-field model derived in this work relies on approximations and heuristic arguments that, on the one hand, allow a closed-form derivation of the mean-field equations, and on the other hand restrict its validity to a limited regime of activity corresponding to quasi-synchronous neuronal populations. Therefore, rather than an exact mean-field representation, the model provides a description of a mesoscopic population of connected neurons driven by ion exchange dynamics.

Strengths:

The idea of deriving a mean-field model which relates the slow-timescale biophysical mechanism of ion exchange and transportation in the brain to the fast-timescale electrical activities of large neuronal ensembles.

Weaknesses:

The idea underlying this work is not completely implemented in practice.

The derived mean field model do not show a one-to-one correspondence with the neural network simulations, except in strongly synchronous regimes. The agreement with the in vitro experiment is hardly evident, both for the mean-field model and for the network model. The assumptions made to derive the closed-form equations of the mean field model have not been justified by any biological reason, they just allow for the mathematical derivation. The final form of the mean-field equations do not clarify whether or not microscopic variables are used together with macroscopic variables in an inconsistent mixture.

Comments on revisions:

The main weaknesses I listed in the first report are still present, since the authors did not answer my questions on a solid basis. I report the list for completeness:

(1) It seems that the reduction methodology that is employed is not the most suitable one for the single-neuron model they are considering.

(2) The formulation of the mean-field derivation is unnecessarily complicated. It could be heavily simplified by following previously published approaches to derive biologically realistic neural masses.

(3) The model seems to work only for highly synchronized situations and not for the standard asynchronous evolution usually observed in neural circuits.

Therefore, my statement remains unchanged.

Reviewer #2 (Public review)

Summary:

The authors aiming in developing a neural mass model characterized by few collective variables mimicking the dynamics of a network of Hodgkin - Huxley neurons encompassing ion-exchange mechanisms. They describe in details the derivation of the mean-field model , then they compare experimental results obtained for the hippocampus of a mice with the neural network simulations and the mean-field results. Furthermore, they report a bifurcation analysis of the developed model and simulation of a small network containing various coupled neural masses, somehow moving towards the simulation of an entire connectome.

Strengths:

The author attempts to develop a mean-field model for a globally coupled network of heterogeneous Hodgkin-Huxley neurons with explicit ion exchange mechanism between the cell interior and exterior.

Weaknesses:

(1) They do not employ the reduction methodology more suited for the single neuron model they consider.

(2) Their derivation of the neural mass model is based on several assumptions, and not all well justified.

(3) Their formulation of the mean-field derivation is unnecessary complicated, it can be strongly simplified by following previously published approaches to derive biologically realistic neural masses.

(4) Their model seems to work only for highly synchronized situations and not for the standard asynchronous evolution usually observed in neural circuits.

General Statements:

The authors honestly declared the many limitations of their approach, once assumed this the results of the mean-field are somehow inconsistent with the neural network simulations as expected.

The authors suggest to employ this model for the simulations on the whole connectome to follow seizure propagation, however I believe that a simpler model, as the Epileptor, remains superior in this respect to this model. That indeed includes biophysical parameters but their correspondence with the ones employed in the network dynamics remain elusive, due to the many assumptions required to derive this mean field model. Furthermore it is more complicated than the Epileptor, I do not think that the present model will be largely employed by the community.

Comments on revisions:

The authors have corrected mistakes present in the manuscript and put a correct list of references.

However, they refuse

(1) To simplify the formulation of the model, the model contains unnecessary complications, as I have clearly written in my report, the authors agree, but they do not want to change the formulation;

(2) To derive the mean field model in a simpler way, as possible, and as I asked many times in my Referee report, this would help the readers to understand the important aspect of the derivation, without not needed and confusing complicated formulations;

(3) To compare direct simulations of the network with neural mass results in sub-section "Bifurcation analysis: emergent network states and multistability" to show bistability, as I asked.

As a matter of fact the performed modifications do not solve my previous doubts on the validity of the results reported in the manuscript.

Therefore, my previous assessments remain valid.

We thank the editors and the two reviewers for their continued engagement with our manuscript. The three weaknesses retained from the first round are essentially identical between the two public reviews:

(i) The reduction methodology is not the most suitable for the single-neuron model we consider;

(ii) The mean-field derivation is unnecessarily complicated;

(iii) The model works only in highly synchronous regimes and does not reproduce the asynchronous evolution typical of neural circuits.

Both reviewers explicitly note that their assessments remain unchanged and we have decided not to alter the formulation of the model. We use this response to state—on the public record—exactly where we agree with the reviewers, where we disagree, and why.

On point (i): the reduction methodology.

We fully agree with the reviewers' technical observation: the Ott–Antonsen / Lorentzian-ansatz reduction in the form introduced by Montbrió, Pazó and Roxin (2015) is exact for canonical Type I neurons (QIF), whose membrane-potential equation is quadratic, and is not directly applicable to a Type II / Hodgkin–Huxley-type neuron whose voltage dynamics is cubic-like. On this point there is no disagreement.

Where we differ is in the conclusion the reviewers draw from this observation. The reviewers read our work as applying an inappropriate reduction methodology to an inappropriate neuron model. We instead positioned our work, from the outset, as an extension of that methodology: we keep the biophysically detailed Hodgkin–Huxley substrate (because it is the only level at which extracellular ion concentrations, depolarization block, bursting and seizure-like events are biophysically grounded), and we adapt the reduction by approximating the cubic voltage nullcline as a piece-wise quadratic with two parabolas of opposite curvature. This is explicitly an approximate, not exact, mean-field. The Lorentzian ansatz is then applied on each branch of the piece-wise quadratic, with the limitations of this construction analyzed in the manuscript.

The reviewers' alternative—starting from a Type I canonical model and grafting on biophysical features—would indeed yield an exact mean-field, but it would forfeit precisely what motivates our work: a tractable mesoscopic description in which the slow variables are physiologically interpretable ion concentrations rather than phenomenological parameters. The trade-off is that we give up exact rigour in order to construct a bridge between the Montbrió-style next-generation neural mass models on one side and the Epileptor on the other, with the additional benefit that the parameters of the resulting neural mass retain a biophysical correspondence (e.g., [K⁺]_bath, Δ[K⁺]_int, [K⁺]_g, the gating variable n) that the Epileptor does not afford.

We therefore respectfully maintain our position: the methodology is not "the wrong reduction for a Type II neuron"; it is an extended reduction designed to be applicable beyond the Type I case, with explicitly characterized validity.

On point (ii): the formulation is unnecessarily complicated.

We agree with the reviewers that, given the assumptions we ultimately adopt, namely that the gating variable n and the potassium concentrations Δ[K⁺]_int and [K⁺]_g are treated as collective (mesoscopic) variables shared by the population, with n a function of the average membrane potential, the closed neural mass equations could be reached by the more direct path used by Guerreiro et al. (2022) and the related literature (R1–R7). In the revised manuscript we now state this explicitly, and we note that the same five-dimensional system arises under either derivation.

Our choice to follow Chen and Campbell (2022) is motivated by the fact that it makes each approximation visible at the point where it is invoked. In particular, it exposes the moment-closure step (Eq. 19), the vanishing-flux boundary condition (Eq. 28), and the locations where microscopic and mesoscopic variables enter the description. We believe that for a reader trying to extend our framework, for instance to a setting with partial heterogeneity in the slow variables, or with stochastic gating, this is the more useful presentation. We have added a remark stating that the simpler Guerreiro-type derivation reaches the same equations under our assumptions, so that readers can take whichever route they find clearer.

On point (iii): the model only works in highly synchronous regimes.

Here we partially agree and partially disagree, and we would like the partial disagreement to appear on the public record.

We agree that the Lorentzian ansatz is, strictly, valid in regimes where the population's membrane potential distribution is unimodal, that is, when essentially all neurons sit on the same side of the threshold V*. Where we disagree is with the implication that the mean-field model fails outside the strongly synchronous regime. The supplementary analysis in Fig. S2, added in the previous round, quantifies the error introduced by the first-moment approximation of n as a collective variable across the full range of [K⁺]_bath values, spanning quiescent, bursting, seizure-like, sustained ictal and depolarization-block dynamics. The fraction of neurons whose gating variable deviates from the population mean is below 2% for the parameters used throughout the manuscript, and the error becomes appreciable only during the brief transitions between sub- and supra-threshold states. These are precisely the moments at which the population is genuinely bimodal and the single-Lorentzian assumption is theoretically expected to leak. In other words, the error peaks coincide with the moments where our derivation tells us in advance that the assumption is locally invalid; the model "knows where it fails." Away from these transitions, the mean-field tracks the population average across all dynamical regimes shown in Fig. 3, not only in the most strongly synchronized ones.

This is, in our view, the strongest argument we can make: we are not claiming exactness, and we are not unaware of the limitations. We have characterized them analytically (the construction of the piece-wise Lorentzian, and the theoretical reason a closed solution exists only when the two branches collapse onto one), and we have characterized them numerically (Fig. S2). The deviations are bounded, their location in parameter space is well identified, and they coincide with transitions where the underlying assumption is locally violated. We believe this constitutes a controlled approximation rather than an uncontrolled one, and we would like this distinction to be visible to readers of the Reviewed Preprint.

We note, in this connection, that the reviewers' preferred reference point, the next-generation neural mass model of Montbrió et al. (2015), which is exact and one-to-one with its underlying network, is exact precisely because the underlying network is a network of QIF neurons. The corresponding statement for a network of Hodgkin–Huxley-type neurons with explicit ion exchange does not, to our knowledge, exist in closed form, and may not exist at all. The relevant question is therefore not whether our model matches the exactness of the QIF case, but whether the controlled approximation we provide is useful. Given the qualitative agreement with neural-network simulations across the full range of [K⁺]_bath, the qualitative agreement with the in vitro recordings, and the recovery of the expected bifurcation structure with new emergent regimes, we believe the answer is yes.

Other outstanding points in the review.

Reviewer 2 reiterates the view that the Epileptor remains superior for whole-connectome seizure-propagation simulations because it is simpler and better characterized. We do not dispute that the Epileptor is more thoroughly analyzed and more parsimonious. The complementarity we propose is not a replacement but a parameter-grounding, as the Epileptor's phenomenological parameters (excitability, slow permittivity) acquire, in the present framework, an interpretation in terms of measurable biophysical quantities (extracellular potassium, intracellular potassium variation, glial buffering).

We thank the reviewers and editors once again for their careful reading, and we are grateful that the points of disagreement have been sharpened to a state where readers can judge them transparently.

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors derive a mean-field model for a network of Hodgkin-Huxley neurons retaining the equations for ion exchange between the intracellular and extracellular space.

The mean-field model derived in this work relies on approximations and heuristic arguments that, on the one hand, allow a closed-form derivation of the mean-field equations, and on the other hand restrict its validity to a limited regime of activity corresponding to quasi-synchronous neuronal populations. Therefore, rather than an exact mean-field representation, the model provides a description of a mesoscopic population of connected neurons driven by ion exchange dynamics.

We agree with the reviewer's characterization. Our manuscript describes the derivation as relying on "approximations and heuristic arguments" and states that "the derivation is not exact"; what we provide is a controlled, approximate mesoscopic description in which the slow variables are physiologically interpretable ion concentrations rather than phenomenological parameters. An exact closed-form thermodynamic limit is, to our knowledge, available only for canonical Type I (QIF) networks (Montbrió, Pazó and Roxin, 2015) and a few of their extensions; it is not currently known for a Hodgkin–Huxley-type network with explicit ion-exchange dynamics. We acknowledge that the original description of the regime of validity may have caused confusion on this point, and in the revised manuscript we have therefore replaced the looser formulation "strongly synchronous regimes" by the more accurate "regimes where the membrane-potential distribution is unimodal and can be reasonably approximated by a Lorentzian" throughout the manuscript.

Strengths:

The idea of deriving a mean-field model that relates the slow-timescale biophysical mechanism of ion exchange and transportation in the brain to the fast-timescale electrical activities of large neuronal ensembles.

We thank the reviewer for recognizing the motivation behind our work. This explicit coupling between slow biophysical ion dynamics and fast electrical activity is precisely the feature we tried to preserve in the reduction, even at the cost of giving up exactness.

Weaknesses:

The idea underlying this work is not completely implemented in practice.

We address this general statement through the four specific sub-points the reviewer raises in the paragraph that follows.

The derived mean field model does not show a one-to-one correspondence with the neural network simulations, except in strongly synchronous regimes.

We partially agree and partially disagree. We agree that the Lorentzian ansatz is strictly valid where the membrane-potential distribution is unimodal, i.e. when essentially all neurons sit on the same side of the threshold V*. We disagree with the implication that the mean-field fails outside this regime. To make this claim quantitative, we added a new supplementary figure (Fig. S2) that quantifies the deviation of individual neurons' gating variables from the population mean across the full range of [K⁺]_bath values—quiescent, bursting, seizure-like, sustained ictal and depolarization-block dynamics. The fraction of deviating neurons is below 2% for the parameters used in the manuscript, with localized peaks only during the brief, genuinely bimodal transitions between sub- and supra-threshold states—precisely the moments at which the theory predicts the assumption to be locally invalid. Away from these transitions, the mean-field tracks the population average across all dynamical regimes shown in Fig. 3, not only in the strongly synchronized ones.

The agreement with the in vitro experiment is hardly evident, both for the mean-field model and for the network model.

We acknowledge that the experimental and simulated traces in the original Fig. 4 did not match quantitatively; this was never our intention. The figure and its caption have been reorganized in the revised manuscript to frame the comparison as qualitative: we aim to demonstrate the shared structure i.e., the slow modulation of fast population activity by extracellular potassium fluctuations, rather than to claim a quantitative fit.

We also added two clarifications that account for the residual differences: (i) the network simulations were intentionally run with rescaled biophysical parameters (membrane capacitance, gating time constants) to keep the computational cost feasible, a standard practice when the goal is to validate dynamical mechanisms rather than absolute timescales; (ii) the in vitro LFP recordings were AC-coupled, so the slow DC components visible in the mean-field traces are filtered out at acquisition.

The assumptions made to derive the closed-form equations of the mean-field model have not been justified by any biological reason, they just allow for the mathematical derivation.

We agree that the modelling assumptions were scattered through the original derivation. In the revised manuscript, the three core assumptions are stated explicitly at the point of derivation: (i) the gating variable n is treated as a collective, population-averaged variable; (ii) the potassium concentrations Δ[K⁺]_int and [K⁺]_g are homogeneous across the population, biophysically justified by the rapid redistribution of ions through diffusion and electrochemical gradients, which enforces near-instantaneous equilibration at the mesoscopic scale; (iii) no heterogeneity is assumed at the level of ion dynamics. The meaning of "locally homogeneous" is now defined explicitly.

On the biophysical motivation of the in vitro perturbation used in the experiment, we have added a new Methods subsection that explains how low extracellular Mg²⁺ unblocks NMDARs and abolishes the divalent-cation stabilisation of the resting membrane potential, depolarising hippocampal neurons and increasing the driving force for outward K⁺ currents. This provides a biophysical link between the experimental perturbation and the model's main control parameter, the extracellular potassium concentration. We also added a reference to the well-established model of epileptic discharges that underpins the experiment.

The final form of the mean-field equations does not clarify whether or not microscopic variables are used together with macroscopic variables in an inconsistent mixture.

We now explicitly acknowledge that in the spiking-network simulations the gating variable n is microscopic (each neuron has its own n_i), whereas in the mean-field derivation it is treated as mesoscopic and shared by the population. This asymmetry between modalities is discussed both in the Results and in the Limitations sections, and is identified as a likely source of some of the discrepancy between the two modalities.

We have also made the notation in Eqs. (36)–(37) consistent (firing rate r used throughout, full current-based dV/dt̄ restored) and fixed the typos and broken equation/reference labels that contributed to the impression of inconsistency (Eqs. 18, 28, 29; the Fig. 2(c) [K⁺] bath label; the lost reference at line 696).

Reviewer #2 (Public review):

Summary:

The authors aim to develop a neural mass model characterized by a few collective variables mimicking the dynamics of a network of Hodgkin – Huxley neurons encompassing ion-exchange mechanisms. They describe in detail the derivation of the mean-field model, then they compare experimental results obtained for the hippocampus of a mouse with the neural network simulations and the mean-field results. Furthermore, they report a bifurcation analysis of the developed model and simulation of a small network containing various coupled neural masses, somehow moving towards the simulation of an entire connectome.

We thank the reviewer for the accurate summary of the manuscript's structure and aims.

Strengths:

The author attempts to develop a mean-field model for a globally coupled network of heterogeneous Hodgkin-Huxley neurons with an explicit ion exchange mechanism between the cell interior and exterior.

We thank the reviewer for recognizing this objective. The retention of Hodgkin–Huxley dynamics with explicit ion exchange is precisely the feature that distinguishes our framework from QIF-based reductions, and it is what enables the slow variables of the resulting mean-field to retain a direct biophysical interpretation.

Weaknesses:

(1) It seems that the reduction methodology that is employed is not the most suitable one for the single-neuron model they are considering.

We agree, on technical grounds, with the observation: the Ott–Antonsen / Lorentzian-ansatz reduction is exact for canonical Type I neurons (QIF) and is not directly applicable to a Type II Hodgkin–Huxley-type neuron with a cubic-like voltage nullcline. Where we differ is in the conclusion. We did not apply an inappropriate reduction to an inappropriate neuron; we deliberately extended the methodology by approximating the cubic nullcline as a piece-wise quadratic with two parabolas of opposite curvature, and then applying the Lorentzian ansatz on each branch. The result is an explicitly approximate, biophysically grounded mean-field, with its regime of validity stated and quantified (Fig. S2).

To make this positioning explicit, we have added a paragraph to the Introduction that situates our work within the next-generation neural mass literature (Byrne et al. 2020; Montbrió, Pazó & Roxin 2015; Guerreiro et al. 2022; Forrester et al. 2024; Perl et al. 2023; Gerster et al. 2021; and works on short-term plasticity, adaptation, conductance-based reductions,

spike-timing-dependent plasticity, random connectivity and noise) and clarifies that we see our contribution as complementary to these approaches, not as a competitor to the exact QIF reductions.

(2) The authors' derivation of the neural mass model is based on several assumptions, and not all well justified.

We agree that, in the original submission, the modelling assumptions were scattered through the derivation. In the revised manuscript, the three core assumptions are stated explicitly at the point of derivation: (i) the gating variable n is treated as a collective population-averaged variable; (ii) the potassium concentrations Δ[K⁺]_int and [K⁺]_g are homogeneous across the population, biophysically justified by the rapid redistribution of ions through diffusion and electrochemical gradients, which enforces near-instantaneous equilibration at the mesoscopic scale; (iii) no heterogeneity at the level of ion dynamics is assumed. The meaning of "locally homogeneous" is now defined explicitly. In addition, we have added Fig. S2, which quantifies numerically the error introduced by the moment-closure assumption (deviation below 2% for the parameters used in the manuscript).

(3) The formulation of the mean-field derivation is unnecessarily complicated. It could be heavily simplified by following previously published approaches to derive biologically realistic neural masses.

We agree that, under the assumptions ultimately adopted in our model—namely that n, Δ[K⁺]_int and [K⁺]_g are mesoscopic—the final five-dimensional system can be reached by the more direct path used by Guerreiro et al. (2022) and the related literature. We now state this explicitly in the revised manuscript and note that the same system arises under either derivation, so that the reader can take whichever route they find clearer. Our choice to retain the Chen and Campbell (2022) formalism is pedagogical: it exposes the moment-closure step (Eq. 19), the vanishing-flux boundary condition (Eq. 28), and the locations where microscopic versus mesoscopic variables enter the description, which is the more useful presentation for a reader wishing to extend the framework (e.g. to partial heterogeneity in the slow variables or to stochastic gating). We also made the notation in Eqs. (36)–(37) consistent (firing rate r used throughout, full current-based dV/dt̄ restored) and fixed a number of typos and broken equation/reference labels.

(4) The model seems to work only for highly synchronized situations and not for the standard asynchronous evolution usually observed in neural circuits.

We partially agree and partially disagree. We agree that the Lorentzian ansatz is strictly valid where the membrane-potential distribution is unimodal; we have replaced "strongly synchronous regimes" by this more accurate formulation throughout the manuscript. We disagree, however, with the implication that the mean-field is useful only in those regimes. Fig. S2, added in this revision, explicitly quantifies the deviation across all dynamical regimes (quiescent, bursting, seizure-like, sustained ictal and depolarization-block dynamics): it remains below 2% for the parameters used in the manuscript, with localized peaks only during the brief sub-to-supra-threshold transitions where the population is genuinely bimodal. Away from these transitions, the mean-field tracks the population average across all dynamical regimes shown in Fig. 3.

General Statements:

The authors honestly declared the many limitations of their approach. It is assumed that the results of the mean-field are somehow inconsistent with the neural network simulations as expected.

We thank the reviewer for acknowledging that the limitations are honestly declared. As detailed above and quantified in Fig. S2, the deviation from the network simulations is bounded and well characterized; it is not assumed but measured.

The authors suggest employing this model for the simulations on the whole connectome to follow seizure propagation, however, I believe that the Epileptor remains superior in this respect to this model. That indeed includes biophysical parameters but their correspondence with the ones employed in the network dynamics remains elusive, due to the many assumptions required to derive this mean-field model. Furthermore, it is more complicated than the Epileptor, I do not think that the present model will be largely employed by the community.

We do not propose our model as a direct replacement for the Epileptor and we do not dispute that the Epileptor is more thoroughly analyzed and more parsimonious. The complementarity we propose is not a replacement but a parameter-grounding: the Epileptor's phenomenological parameters (excitability, slow permittivity) acquire, in our framework, a concrete interpretation in terms of measurable biophysical variables (extracellular potassium, intracellular potassium variation, glial buffering). Retaining the Hodgkin–Huxley substrate is essential to ground these variables biophysically.

To make this complementarity more visible, the Limitations and Discussion section has been expanded to discuss the choice of a purely excitatory network as a first step (with excitatory–inhibitory generalizations available via the synaptic reversal potential) and to point to additional biological ingredients (calcium and other ions, plastic synapses, random connectivity and noise, adaptation, spike-timing-dependent plasticity) that the framework can accommodate, with reference to the next-generation neural mass literature.

We thank the reviewers and editors for their careful reading. We hope this public response makes our reasoning, the limits of our approach, and the concrete revisions made in this round transparent.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In general, the writing is scattered. Every time a model is introduced, one starts from the general formulation only to find that a very simplified case is used with respect to that formulation, which is very confusing. Authors need to reduce unnecessary formulations that confuse the reader and make it clear which formulations are actually used.

We thank the reviewer for this comment and understand the concern regarding the balance between general formulations and specific approximations. Our intention in including the more general equations and derivations (e.g., Eq. 7 and others) was pedagogical — to ensure completeness and transparency in the modeling steps, especially for readers less familiar with mean-field reductions of biophysically detailed models. These general forms also serve to clarify the assumptions underlying the simplifications we employ. In the latest version, we improved the clarity of core equations (e.g., Eq. 37), which form the basis of all simulations presented (see details below, in the answer to question 14).

(2) The Introduction would benefit from a wider view of the literature. The literature on exact mean field models (i.e. derived from the Lorentzian Ansatz) has flourished in the last years. In particular, it would be worth considering the following papers, where exact neural mass models are applied to perform whole-brain and large-scale brain simulations:

Forrester, M., Petros, S., Cattell, O., Lai, Y. M., O'Dea, R. D., Sotiropoulos, S., & Coombes, S. (2024). Whole brain functional connectivity: Insights from next generation neural mass modelling incorporating electrical synapses. PLOS Computational Biology, 20(12), e1012647.

Perl, Y. S., Zamora-Lopez, G., Montbrio, E., Monge-Asensio, M., Vohryzek, J., Fittipaldi, S.,

Campo, C. G., Moguilner, S., Ibanez, A., Tagliazucchi, E., Yeo, B. T. T., Kringelbach, M. L., & Deco, G. (2023). The impact of regional heterogeneity in whole-brain dynamics in the presence of oscillations. Network Neuroscience, 7(2), 632-660.

Byrne, Aine, James Ross, Rachel Nicks, and Stephen Coombes. "Mean-field models for EEG/MEG: from oscillations to waves." Brain topography 35, no. 1 (2022): 36-53.

Gerster, M., Taher, H., Skoch, A., Hlinka, J., Guye, M., Bartolomei, F.,... & Olmi, S. (2021). Patient-specific network connectivity combined with a next generation neural mass model to test clinical hypothesis of seizure propagation. Frontiers in Systems Neuroscience, 15, 675272.

Byrne, Aine, Reuben D. O'Dea, Michael Forrester, James Ross, and Stephen Coombes. "Next-generation neural mass and field modeling." Journal of neurophysiology 123, no. 2 (2020): 726-742.

Benitez-Stulz, Sophie, Samy Castro, Gregory Dumont, Boris Gutkin, and Demian Battaglia. "Compensating functional connectivity changes due to structural connectivity damage via modifications of local dynamics." bioRxiv (2024): 2024-05.

We have added the following paragraph:

“Recently, a class of these models, called next-generation neural mass models [42], has been developed based on an analytical approach introduced by [25] that allowed for the exact derivation of mean field parameters for a population of quadratic integrate-and-fire (QIF) neurons. These can be linked to EEG/MEG oscillations [43], including epipeltic seizures [43], and have been used to study various aspects of the whole-brain dynamics such as the low-dimensional manifold of the resting state [45,46], aging [47] and neural signatures of consciousness [48].”

We have also modified the preceding paragraph of the introduction that now reads:

“At the mesoscopic level, the observable properties of a neuronal ensemble are generally explained by statistical physics formalism of mean-field theory [19-22]. Mean-field models demonstrated a predictive value for studying the mesoscopic dynamics of neuronal populations [23], providing statistical descriptions of neuronal networks [2, 19, 24-29], which can be used to address questions related to network-level mechanisms [12, 24, 30].

In general, neural mass models have a low enough number of parameters to be tractable and provide general intuitions regarding mechanisms underlying complex neuronal activity [31-36]. For example, statistical population measures, such as the firing rate, can be used to assess mesoscopic dynamics [1, 7, 31, 36-41].”

(3) Moreover, conductance-based models have been already implemented in neural mass models not only in references [69, 71, 95], but also in:

Guerreiro, I. C., Di Volo, M., & Gutkin, B. (2023). A new generation of reduction methods for networks of neurons with complex dynamic phenotypes.

Capone, C., Di Volo, M., Romagnoni, A., Mattia, M., & Destexhe, A. (2019). State-dependent mean-field formalism to model different activity states in conductance-based networks of spiking neurons. Physical Review E, 100(6), 062413.

We have added the following sentence:

“Moreover, conductance-based couplings between the spiking neurons have been already implemented in neural mass models [58, 59, 91, 93, 121], but without an extracellular exchange mechanism.”

(4) Sec. 1.1 As previously established in the literature, a system of all-to-all coupled neuronal equations can be solved exactly in the thermodynamic limit (i.e., infinite neurons limit) if the single neuron membrane potential equation is a quadratic function and if the instantaneous distribution of membrane potentials of neurons in a population is described by a Lorentzian [Montbrió, E., Pazó, D. & Roxin, A. Physical Review X 5 (2), 021028 (2015)]. This means that the thermodynamic limit can be performed for a Canonical Type I model like the quadratic integrate-and-fire.

What is the biological justification and the reason to approximate a different neuron type (a type II neuron model), whose membrane potential equation resembles a cubic function, with a quadratic function? The fact that it can be solved in the quadratic approximation is not, in my opinion, a sufficient justification. It would be more correct to start from a type I neuron at the microscopic level with a quadratic function and then provide additional biological features.

We thank the reviewer for raising this important point. We respectfully disagree with the notion that starting from a canonical Type I model (such as the quadratic integrate-and-fire neuron) would be a more biologically grounded approach. While the quadratic form is analytically convenient, it does not capture certain key features of neuronal excitability particularly those related to bursting, seizure-like events, and depolarization block which are closely tied to the cubic-like nullcline geometry arising in Hodgkin–Huxley-type models, especially in the presence of slow ion dynamics.

Our work seeks to bridge biophysical realism with analytical tractability. The step-wise quadratic approximation we employ is specifically designed to mimic the cubic membrane potential profile that emerges from the full ion-exchange dynamics. While the Lorentzian Ansatz is not strictly justified in this case from first principles, we show that it yields a workable and biologically interpretable mean-field description, which aligns with single-neuron dynamics, population simulations, and even in vitro observations. To our knowledge, this is a novel contribution that extends mean-field modeling beyond currently available approaches, which are often restricted to simplified or phenomenological neuron models.

In this context, using a quadratic approximation is not merely a mathematical convenience — it is a means to retain key dynamical features of more realistic (non-Type I) neurons within a tractable framework, enabling insights into complex behaviors like multistability and pathological bursting.

(5) Sec. 1.2 As shown in Figure 3, the mean-field equations do not show a one-to-one correspondence with the neural network simulations, except in strongly synchronous regimes. This represents a strong limitation in the model, especially because exact neural mass models (as shown in Reference [23]) perfectly fit the dynamics of the underlying network model both in the asynchronous and in the synchronized regime.

We appreciate the reviewer’s observation and acknowledge that our original description may have caused confusion. The model's validity is not strictly limited to strongly synchronous regimes, but rather to regimes where the distribution of membrane potentials across the neuronal population remains unimodal and can be reasonably approximated by a Lorentzian. This includes but is not restricted to—highly synchronized states.

We agree that this distinction is important and have clarified it in the revised manuscript (e.g., “in strongly synchronous regimes” —> “in regimes where the membrane potentials' distribution is unimodal and can be reasonably approximated by a Lorentzian”).

In contrast to exact mean-field reductions based on quadratic integrate-and-fire neurons (e.g., [23]), our model originates from a biophysically grounded HH-type neuron with ion exchange dynamics, and necessarily involves heuristic approximations to achieve a closed-form mean-field description. While this results in a less exact correspondence with network simulations in more heterogeneous or bimodal states, our goal was to retain biological interpretability and account for phenomena such as ion-driven bursting and seizure-like transitions, which are not captured by standard QIF-based neural masses.

We see our contribution as complementary to existing exact reductions — offering a biophysically grounded alternative that remains tractable and informative in a relevant class of unimodal, mesoscopic dynamical regimes.

(6) Sec. 1.3 In this section the authors show the comparison between in vitro experiments and simulations with both the network model and the neural mass model (Figure 4, panels a,b,c). The qualitative agreement that is supposed to be shown is hardly evident. The shape of the signals is different as is the type of bursting. The only agreement results in the fact that there are repeated spiking events at successive times in a periodic manner. However, the time scale of the simulations is different for neural network simulation and mean-field experiment, making it difficult to compare them. While the period of the bursting event is around 2 min for mean field simulation (in according with experiments), the time scale of the network simulation is 60 times smaller, thus meaning that we are considering completely different mechanisms and phenomena. The justification given by the authors, that "the parameters were modified to simulate shorter fluctuations (in the network of Hodgkin-Huxley neurons) for computational efficiency" is inappropriate.

The poor agreement turns out to be even worse in the comparison between experiments and mean-field simulations shown in panels d and e of Figure 4. While the mean field simulation is characterized by a periodic behaviour both in the mean membrane potential and in the external potassium concentration, the in-vitro traces are not periodic and show an increasing irregular activity of the extracellular LFP in correspondence with increasing external potassium concentration.

How it is possible to justify the implementation of this model if the working hypotheses are not supported by the results? The worst agreement of the network simulations with the experiments reinforces the doubt raised in the previous point: what is the reasoning underlying the choice of Hodgkin-Huxley as a single neuron model?

We thank the reviewer for this detailed critique. We acknowledge that the comparisons in Figure 4 involve limitations and we now provide a clearer rationale and context in the revised manuscript. First, we emphasize that our intention is not to claim a quantitative match between the experimental and simulated traces, but rather to demonstrate that our model grounded in biophysical mechanisms such as ion exchange is capable of qualitatively reproducing a key feature observed experimentally: the slow modulation of neuronal activity by extracellular potassium concentration. For example, both in vitro (Fig. 4a, 4d) and in our simulations (Fig. 4b, 4e), bursts of activity ride on slower oscillations of potassium, and the interplay of fast and slow dynamics is central to both.

Regarding the discrepancy in timescales between the neural network and mean-field simulations: the network simulations were intentionally run with accelerated dynamics by rescaling biophysical parameters (e.g., membrane capacitance and gating time constants) to keep the computational cost feasible. We now clarify in the manuscript that this choice is standard practice in computational modeling when the primary goal is to validate dynamical mechanisms rather than replicate absolute timescales.

On the shape of LFP signals: the experimental recordings were AC-coupled, and the DC components associated with slower shifts in membrane potential such as those modeled in the mean-field simulations are not captured in those recordings. This limits the visibility of key features like the underlying potential jumps. Additionally, no claim is made regarding a specific bursting classification in either data or simulation.

We agree that the experimental trace in Fig. 4d shows more complex, non-periodic dynamics (e.g., slowing burst frequency and irregularity), which are not captured by our current deterministic model. These differences could plausibly arise from additional physiological processes (e.g., stochastic transitions between metastable regimes or variability in ion regulation) that are not modeled here. In future work, such phenomena may be captured by introducing noise or parameter variability (see, e.g., Saggio et al., A taxonomy of seizure dynamotypes , elife 2020), or by allowing the parabola coefficients in the nullcline approximation to vary dynamically.

Finally, regarding the choice of a Hodgkin–Huxley-type neuron: this model allows us to incorporate a biophysical description of ion exchange, which is central to the phenomena we study. While modeling the spiking mechanisms explicitly precludes certain mathematical simplifications available to very simplified neuron models with reset, it enables direct links between mesoscopic dynamics and measurable quantities such as extracellular potassium an essential objective of our work. To summarize, we rearranged Fig4:

Potassium can have periodic behavior with V bursting riding on top (Fig.4 a). The model also shows this behavior at different timescales (Fig. b,c,e).

AC LFP recording is filtered so we might not see the V jump during the bursts (because we do not have DC recordings). No claim about bursting class here.

Potassium can also have more complex behavior (e.g., slowing down of burst frequency Fig.4.d), that the deterministic model do not show, but maybe exploring dynamical parameters (e.g., from parabolas or K_bath) or with added noise allowing to jump between regimes (reference Saggio et al. eLife 2020).

(7) Sec. 1.5 Here six neural masses are coupled via long-range structural connections with random weights. Simulations of the system are shown for two different values of the global coupling parameter (G = 0 and G = 100). How many realisations of the network have been considered?

We thank the reviewer for pointing this out. The presented simulation was intended as a proof-of-concept demonstration to illustrate the model’s capacity to support network-level propagation of pathological activity. For this purpose, we considered a single representative realization of the structural connectivity with random weights. Given the deterministic nature of the model and the qualitative focus of the demonstration, additional realizations do not qualitatively change the observed behavior — namely, the transition from localized to network-wide bursting as coupling strength increases. We have now clarified this in the revised manuscript.

“This simulation serves as a proof of concept to illustrate how local pathological activity can propagate through a network depending on the strength of coupling. We used a single representative realization of randomly weighted structural connectivity. While we did not perform a systematic exploration of different realizations or coupling strengths, we observed that the qualitative behavior namely, the emergence of network-wide bursting beyond a critical coupling threshold remains robust across similar setups. The model is compatible with empirical connectome data and can be readily extended to simulations using realistic brain network architectures.”

In future applications involving data-driven network architectures or variability analyses, we agree that exploring multiple realizations or empirical connectomes will be valuable.

How do the results depend on the different choices of the random weights? What is the dependence of the emergent dynamics on G? What kind of dynamics can be observed varying smoothly the parameter G (e.g. from 0 to 100)?

This section serves as a proof of concept to show that pathological activity in one node can propagate through the network when coupling is strong. We used a single random weight configuration and did not systematically explore variations in G or connectivity. While richer dynamics likely emerge across intermediate values of G, a full parameter sweep is beyond the scope of this study. We clarify this in the revised text (see answer above).

(8) Sec. 2.1 In the description of the experiment it is mentioned that only Mg^{2+} is varied. What is the role played by Mg^{2+} variation in influencing the external potassium concentration variation? How the experiment can be linked to the model? How the hypothesis of introducing an equation for the potassium concentration current in the microscopic model is supported by the experiment and vice-versa?

We thank the reviewer for this question. We have added a new subsection in the Methods explaining the.agnesium removal as a mean to influence the external potassium dynamics:

“The membrane of hippocampal neurons is equipped with N-methyl-D-aspartate type glutamate receptors (NMDARs). These receptors have a very high affinity for glutamate and can, in principle, be activated by ambient glutamate present at low concentrations in the brain extracellular fluid (ECF). Under normal physiological conditions, this activation does not occur because extracellular magnesium ions (Mg²⁺) block the NMDAR channel at membrane potentials more negative than about –50 mV; this voltage-dependent block prevents receptor activation at rest. When extracellular magnesium is removed, the block is relieved, allowing NMDARs to be activated, leading to neuronal depolarization toward the action potential threshold [117].”

“In addition, as a divalent cation, Mg²⁺ interacts with the negatively charged neuronal membrane, contributing to the stabilization of the resting membrane potential. Lowering extracellular magnesium concentration disrupts this effect, resulting in membrane depolarization [118].”

“Consequently, magnesium removal not only facilitates NMDAR-dependent depolarization, but also directly depolarizes neurons. This depolarization increases the driving force for outward potassium currents through K⁺ channels, meaning that variations in Mg²⁺ can indirectly influence external potassium dynamics during neuronal activity.”

(9) Sec. 2.6 The modified version of the continuity equation has been derived following Reference [95], where the authors consider a network of Izhikevich neurons, and each neuron is modelled by a two-dimensional system consisting of a quadratic integrate and fire equation plus an equation that implements spike frequency adaptation. In particular, in [95] the authors achieve a closed set of mean-field equations with the inclusion of the mean-field dynamics of the adaptation variable by using a Lorentzian ansatz combined with the moment closure approach. The moment closure condition is also assumed in the present manuscript (Eq. 19). Under which assumptions is the implementation of the moment closure condition justified?

We are thankful to the reviewer (and also to the R2) for pointing out to the validity of the justification of the assumptions that we have used in our formalism. We hence agree that the moment closure is not a sufficient justification for assuming that V depends on the mean n, which is neccessary for the derivation of Eq. 20, but in addition we need the assumption that n can be treated as a collective variable as it is done in the works mentioned by the reviewer 2. In addition we have performed numerical simulations of the full system to calculate the error term introduced by this approximation, and the results in the new Fig. S2 show that this is below 2% for each of the different dynamical regimes.

We have hence modified the justification for Eq. (19) reading:

“Next we assume a first-order moment closure condition for the variable n [59], justified by the numerical simulations of the full network (see Fig. S2) which show that for most of the neurons (close to 99 \% for the value of ∆ same as in the other simulations) the mean of the population is well capturing the behavior of the single neurons [122]. Finally, putting together these factors and assuming that n can be treated as a collective variable for each neuron (see Limitations of the model} section) we arrive to ” and also

“The validity of the first moment closure, Eqs. (19), as in [59], is supported by the numerical simulations, which show that, both, during the silent regime and when seizure-like events occur, n_i for most neurons track the network averaged ⟨n | V, η⟩. In particular, it is less than 2% of the neurons that fire while the mean is low, and vice-versa, Fig. S2. In less synchronized scenarios (larger ∆ or smaller J), however, this value would increase, but the mean would always capture the qualitative behaviour of the population.”

This is also now explicitly mentioned in the following paragraph:

“Unlike the mean membrane potential ⟨V⟩ and the firing rate (r), which can be explicitly derived from the continuity equation under the Lorentzian assumption, the expression for ⟨n(t)⟩ in Eq. (26) is formal. In our mean-field model, the gating variable (n) is treated as a global population variable, evolving deterministically as a function of the average membrane potential. Therefore, ⟨n(t)⟩ corresponds to the collective gating variable assumed to be shared by all neurons, and is not computed by averaging distinct microscopic (n_i) values.”

(10) Considering also the comments reported above, I think that it would make more sense to start from an Izhikevich neuron model as microscopic model and add the equations for the ionic currents as mesoscopic variables (i.e. written as population average variables), instead of starting from the Hodgkin-Huxley single neuron model and trying to make hardly justifiable approximations and simplifications.

We respectfully disagree. While the Izhikevich model is computationally efficient, it lacks the biophysical detail required to capture key ion-driven mechanisms such as depolarization block, slow ion accumulation, and specific burst-initiation dynamics all of which are central to our study. The Hodgkin–Huxley framework, despite requiring approximation, provides the necessary physiological grounding to link microscopic ion exchange with emergent population behavior.

(11) Sec. 2.7 What is the advantage of using six more parameters to fit, like R-,R+,c-,c+,I-,I+?

This is in contradiction with the spirit of deriving a mean-field model, where the number of parameters should be reduced. What is the advantage of this mean-field derivation with respect to other mean-field derivations of Hodgkin-Huxley neurons, like the one in Reference [9]?

The additional parameters (R±, c±, I±) are not arbitrary they compactly parametrize the cubic-like nonlinearity of the membrane potential dynamics in our stepwise-quadratic approximation. This trade-off allows us to preserve essential biophysical features of HH neurons (e.g., bursting regimes, depolarization block) within a tractable analytic framework. Compared to alternative approaches like in ref. [9], which focus on phenomenological reductions and do not yield an ODE system, our model offers more direct interpretability in terms of ion dynamics, providing a closer link between microscopic mechanisms and mesoscopic activity patterns.

(12) Sec. 2.11 The derivation of the mean-field dynamics for the gating variable is rather heavy and difficult to follow. This section could be simplified, whilst also better explaining the underlying approximations and the validity of these approximations, which is currently missing.

We agree that the derivation is technical, but we chose to retain it for transparency, as it follows the Chen and Campbell approach and makes key approximations such as moment closure explicit. We have now added a clarification that n is treated as a collective variable We hope that the current level of detail helps readers understand the assumptions underlying the gating variable dynamics.

(13) Sec. 2.12 The derivation of Eqs. (36) is quite confusing and needs to be re-written in a clearer form. Why are both the variables x and r present in these equations, since they are proportional according to Eq. (25)?

We thank the reviewer for pointing this out. We have adjusted the equations to improve clarity and now consistently express the firing rate in terms of a single variable. This removes the redundancy and simplifies the presentation.

(14) Sec. 2.13 The derivation of Eqs. (37) is quite confusing and needs to be rewritten in a clearer form.

Both the auxiliary variable x and the firing rate r are present in this equation, the same as in Eq. (36). Therefore it is presented as a set of equations for the auxiliary variable x and for the physical variable V. Moreover in the equation for dV/dt, the quadratic term in V has disappeared and it is not clear to me which are the variables corresponding to I- and I+. In particular, in Eqs. (36) there are two different current terms I-,I+ for the two equations related to dy/dt. In Eqs. (37) there is a single term (I_{cl} +I_{Na}+I_K+I_{pump})/C_m which is identical for both equations related to dV/dt. I was expecting two different terms also in Eqs. (37).

We appreciate the reviewer’s close reading. To improve clarity, we now express the dynamics in terms of the firing rate r, replacing \dot{x} with \dot{r} in both Eq. (36) and Eq. (37) to avoid confusion.

As for the current terms: in Eq. (37), we reverse the stepwise quadratic approximation and reintroduce the original ionic currents from Eq. (16). This is why the expressions involving I_{\text{cl}}, I_{\text{Na}}, I_K, and I_{\text{pump}} appear as a single summed term in \dot{V}, rather than the split I_-,I_+ terms used in the stepwise approximation. We now clarify this in the text.

We also write V as \bar{V} to clarify that it refers to the average membrane potential for the neuronal population. Finally, we wrote the final equation in a more compact form to improve clarity (new Eq.38).

(15) Moreover, while the equation for the gating variable n can be considered as a differential equation for a mesoscopic variable since n depends on average values only, it is not clear to me if the remaining variables 𝛥[K+]_{int}, [K+]_g can be considered mesoscopic or not. Since Eqs. (37) represent a mean-field model, I expect every variable to be a mean-field variable. This could be easily achievable for the extracellular potassium concentration, but I do not understand how a site-specific microscopic variable like the intracellular potassium concentration variation can be automatically inserted in a set of mean-field equations without any averaging or intermediate steps. This is a crucial point to be clarified for the validity of the neural mass equations.

We thank the reviewer for raising this important point. In our model, we assume spatial homogeneity at the mesoscopic scale, meaning that ion concentrations — both intra- and extracellular — are uniformly distributed across the population. As a result, variables such as \Delta[K^+]_{\text{int}}, Δ[K+]int and [K+]g are treated as population-level averages, consistent with the mean-field framework.

Moreover, the rate of change of intracellular potassium is tightly coupled to extracellular dynamics via ion exchange mechanisms, justifying its inclusion as a slow, mesoscopic variable. We now clarify this modeling assumption explicitly in the text.

“By locally homogeneous, we mean that all neurons in the population are assumed to share the same extracellular and intracellular ionic environment and are connected with identical coupling rules, allowing us to treat the population as uniform with respect to ion dynamics and connectivity.”

“These slow variables are in addition considered to be mesoscopic, meaning they are identical for every neuron in the population.”

Minor points:

(1) Figure 2, panel d. Please detail the variable on the y-axis, which is not reported in the figure.

Done

(2) Eq. (15) is cited in many parts of the manuscript, while it seems to me it would be more appropriate to reference Eq. (2). Is this a mistake or is there a reason to cite Eq. (15)?

The reviewer is correct, we have had a wrong equation label, which we have now corrected.

(3) Figure 4 Would it be possible to show enlargements of the mean membrane potential traces to directly compare the different bursting types shown by the simulation of the different models?

The panel d already contains enlarged part of the membrane potential traces. For the rest, going back to the Q6, we want to stress again that our intention is not to claim a quantitative match between the experimental and simulated traces.

(4) Figure 5 In the caption the author refers to "the generic model, single neuron model, and epileptor model". Could you please better explain the models referred to and why they are mentioned? Are the generic model and the single neuron model those that are presented in the Materials and Methods section? Or do you refer to completely different models, as for the epileptor?

We have removed the reference to the generic model (we had in mind the canonical model for seizures by Saggio et al. 2017), since it is not mentioned in the paper, and we have clarified that the single neuron model and epileptor model, which were used to simulate seizure like events.

(5) Sec 2.5 As already stated above, the authors need to reduce unnecessary formulations that confuse the reader. Here, for example, Eqs. (6) and (7) are unnecessary, in view of the fact that delta spikes are used (Eq. 8).

We thank the reviewer for the suggestion, but we disagree, and we think it is better to start the derivations from the more general case, as done with Eqs. 6-7.

(6) Sec. 2.6 Could you please better explain why in Eqs. (15) and (16), the variable V0 is introduced, while before and after this, the variable V is used?

We thank the reviewer for the comment. In Eqs. (15) and (16), \dot{V}_0 denotes the free term of the membrane potential equation, i.e., the component driven solely by the intrinsic ionic currents and excluding the synaptic input I_syn. Only this \dot{V}_0 term (a function rather than an independent variable) is approximated by the piece-wise quadratic expression in Eq.(21). In contrast, the variable V represents the membrane–potential variable, which dynamics is obtained by combining \dot{V}_0 with the synaptic current contribution I_syn. In summary, there is no independent variable V_0; only the function \dot{V}_0 is introduced to represent the intrinsic (non-synaptic) component of the membrane–potential dynamics. We have now clarified this in the text.

(7) In the square brackets of the r.h.s. of Eq. (18), for all the intermediate steps, it appears G^n(V,n) ϱ^V, while there should be G^n(V,n) ϱ^n.

We thank the reviewer for catching this typo. We have corrected this in the revised manuscript.

(8) Sec. 2.8 Here the authors affirm that "a double-Lorentzian (or a piece-wise Lorentzian) could be a suitable form for ρ^V (t, V | η). However, it is not clear under which conditions such an assumption would allow a solution to the continuity equation". What are the problems underlying the implementation of the double Lorentzian? It seems to be a more correct form than the single Lorentzian actually implemented.

We thank the reviewer for this thoughtful question. In principle, a double-Lorentzian ansatz for \rho^V can indeed be implemented in several reasonable ways–for example, by enforcing that the combined area of the two Lorentzian components is normalized to one (to preserve the probabilistic interpretation) and by imposing smoothness constraints at their boundaries. However, despite exploring these implementations, we were unable to obtain non-trivial solutions of the continuity equation under this parametrization. The only solvable case we found is the degenerate one in which the two Lorentzians collapse onto each other (i.e., (x_- = x_+) and (y_- = y_+)), which reduces the ansatz to the single-Lorentzian form used in the manuscript. For this reason, although the double-Lorentzian is conceptually appealing, it did not yield practically useful solutions within our framework.

(9) Eq. (28). The symbols used for the flux (especially those used in the second-to-last step once the inner integration is performed) are confusing and it is difficult to understand what they mean.

We thank the reviewer for noting this issue. The problem was due to a LaTeX typo that prevented the vertical lines—indicating that the flux is evaluated at specific points—from rendering correctly. We have now corrected this.

(10) Eq. (29) In the third step there are some misprints that impair comprehension.

We thank the reviewer for noting this. We have corrected these misprints in the revised version.

(11) Line 696. The reference is not displayed.

Fixed.

Reviewer #2 (Recommendations for the authors):

As a really general remark, this manuscript is written in a confusing manner, the authors present their model in a general formulation and their analysis in a complicated way that in the end is not needed, as I will explain in detail in the following.

Another general question is why the authors want to employ the neural mass reduction methodology developed in [23] to obtain exact mean-field evolution for quadratic neurons (like the quadratic integrate and fire (QIF)) for a model that reveals a cubic dependence on the membrane potential, as the FizhHugh-Nagumo neuron (that indeed is a 2d reduction of the Hodkgin-Huxley model), to obtain an approximate neural mass model that somehow works qualitatively only for synchronized dynamics? Why not use another approach more suited to derive the neural mass model for cubic nonlinearity, as the one suggested in [33] and [69] by Di Volo and co-authors? What is the rationale behind the choice of the authors?

We appreciate the reviewer’s critical feedback and the opportunity to clarify our methodological choices. Our decision to base the mean-field model on Hodgkin–Huxley-type neurons stems from the need to retain ion channel dynamics, which are essential to capture the coupling between membrane activity and extracellular ionic concentrations. This biophysical link is central to our study and cannot be achieved using more abstract neuron models such as QIF or FitzHugh-Nagumo alone.

Regarding the mean-field reduction method: while the Ott-Antonsen/Lorentzian framework is indeed exact for QIF neurons, we adopted a stepwise quadratic approximation to apply a similar formalism to the cubic-like dynamics of the HH model. This choice enables us to analytically capture a rich set of behaviors, including bursting, depolarization block, and seizure-like dynamics, in a tractable mean-field system.

We considered the approach of Di Volo and colleagues [33, 69], but their methodology is tailored to asynchronous irregular regimes, whereas our model is specifically designed to capture dynamics in quasi-synchronous or bursting regimes — including epileptiform activity — which are not covered by the assumptions of the Di Volo framework.

We now clarify these modeling choices more explicitly in the revised manuscript.

"Unlike phenomenological or reduced models, the Hodgkin–Huxley framework allows us to retain explicit ion exchange dynamics, which are essential for linking membrane behavior to extracellular potassium fluctuations. This level of biophysical detail is crucial for modeling pathological regimes such as seizure onset and propagation."

Furthermore, the derivation of the neural mass equations is unnecessarily complicated, as a matter of fact, they approximate all the variables (except the membrane potentials of the single neurons) as collective variables (i.e. the gating variable and the potassium concentration) common to all the neurons. The neural network model for which they derive the neural mass model presents microscopic evolutions of the membrane potential cubic-like plus other global variables equal for all neurons, that depend on collective variables such as the mean membrane potential or the mean firing rate. Once clarified, the derivation of the neural mass model is much simpler, and it is not necessary to follow the approach reported in Reference [95] [Chen, L. & Campbell, S. A. Exact mean-field models for spiking neural networks with adaptation. Journal of Computational Neuroscience 50 (4), 445-469 (2022)] which is unnecessarily complicated. The authors can follow a much simpler methodology as explained by Guerriero et al in Reference [R6] (cited below) where the authors consider the same model studied in [95]. Such a methodology has been applied in many cases already, to introduce realistic aspects in the neural mass model [23] (see References [R1-R7] below). I strongly encourage the authors to reformulate their approach in a simpler and clearer manner, by following the approach reported in [R1-R7]. The manuscript will become more readable and it will gain in comprehension.

We thank the reviewer for this helpful suggestion. We agree that, given the assumptions made in our derivation (i.e., shared gating and ion concentration variables across neurons), the mean-field equations could alternatively be obtained using the simpler methodology proposed by Guerriero et al. [R6] and related works [R1–R7]. However, we chose to follow the derivation presented by Chen and Campbell [95] because it makes the approximations (e.g., moment closure, flux boundary assumptions) explicit and generalizable to future extensions. However, we also acknowledge that the assumption of n to be treated as a collective variable is needed, and for clarity, we have now added a remark in the manuscript indicating that the same result could be recovered more directly using the approach of Guerriero et al.

“We note that, under the assumption of globally shared gating and ion concentration variables across the neuronal population, the resulting mean-field equations can also be derived using simpler methods as proposed by Guerriero et al [58]. In this work, we follow the more general formalism of Chen and Campbell [59], which makes the role of key approximations (e.g., moment closure, vanishing flux at boundaries) explicit. This also facilitates potential generalizations to settings with partial heterogeneity or dynamic gating distributions.”

“Finally, putting together these factors and assuming that n can be treated as a collective variable for each neuron”

“Unlike the mean membrane potential ⟨V⟩ and the firing rate (r), which can be explicitly derived from the continuity equation under the Lorentzian assumption, the expression for ⟨n(t)⟩ in Eq. (26) is formal. In our mean-field model, the gating variable (n) is treated as a global population variable, evolving deterministically as a function of the average membrane potential. Therefore, ⟨n(t)⟩ corresponds to the collective gating variable assumed to be shared by all neurons, and is not computed by averaging distinct microscopic (n_i) values.”

Now I will examine in detail all the manuscript and report comments/remarks/suggestions numbered as (Q#) on how to improve the present manuscript to render it easier to read and more comprehensible, these are not minor remarks, just detailed ones.

Introduction

(Q1) The Introduction section needs a part devoted to the reduction methodology developed in [23] for QIF neurons and a presentation of previous works dealing with the introduction of biologically realistic aspects in the neural mass model derived in [23]. Here is a non exhaustive list of such papers concerning the introduction of the following realistic aspects in the neural mass developed in [23]:

(I) short-term synaptic plasticity :

[R1] Exact neural mass model for synaptic-based working memory H Taher, A Torcini, S Olmi, PLOS Computational Biology 16 (12), e1008533 (2020)

[R2] Bursting in a next generation neural mass model with synaptic dynamics: a slow-fast approach H Taher, D Avitabile, M Desroches, Nonlinear Dynamics 108 (4), 4261-4285 (2022)

[R3] Mean-field approximations of networks of spiking neurons with short-term synaptic plasticity R Gast, K Thomas R, H Schmidt, Physical Review E 104 (4), 044310 (2021)

(II) spike frequency adaptation:

[R4] Gast, Richard, Helmut Schmidt, Thomas R. Knösche. "A mean-field description of bursting dynamics in spiking neural networks with short-term adaptation." Neural computation 32.9 (2020): 1615-1634.

[R5] Population spiking and bursting in next-generation neural masses with spike-frequency adaptation, A Ferrara, D Angulo-Garcia, A Torcini, S Olmi, Physical Review E 107 (2), 024311 (2023).

(III) conductance-based neuron with a slow current (Izekievic model):

[R6] A new generation of reduction methods for networks of neurons with complex dynamic phenotypes,IC Guerreiro, M Di Volo, B Gutkin, preprint arxiv: 2206.10370 (2022)

(IV) spike timing-dependent plasticity:

[R7] Mean-field approximations with adaptive coupling for networks with spike-timing-dependent plasticity, B Duchet, C Bick, Á Byrne, Neural computation 35 (9), 1481-1528 (2023).

(V) random connectivity and noise:

[R8] Mean-field models of populations of quadratic integrate-and-fire neurons with noise on the basis of the circular cumulant approach

DS Goldobin Chaos: An Interdisciplinary Journal of Nonlinear Science 31 (8) (2021)

[R9] A reduction methodology for fluctuation-driven population dynamics DS Goldobin, M Di Volo, A Torcini, Phys. Rev. Lett. 127, 038301 (2021)

[R10] Shot noise in next-generation neural mass models for finite-size networks VV Klinshov, SY Kirillov Physical Review E 106 (6), L062302 (2022)

I think the authors should refer in the introduction to these previous papers, where realistic biological aspects have been already introduced in the neural mass model developed in [23].

We have added a whole pragaraph devoted to the next-generation neural mass models and in particular to the other works introducing biological realism in this class of models:

“Recently, a class of these models, called next-generation neural mass models [42], has been developed based on an analytical approach introduced by [25] that allowed for the exact derivation of mean field parameters for a population of quadratic integrate-and-fire (QIF) neurons. These can be linked to EEG/MEG oscillations [43], including epipeltic seizures [44], and have been used to study various aspects of the whole-brain dynamics such as the low-dimensional manifold of the resting state [45, 46], aging [47] and neural sig natures of consciousness [48]. Number of works dealt with the introduction of biologically realistic aspects in the mostly phenomenological neural mass model derived in [25]. These included short-term synaptic plasticity [49–51], spike frequency adaptation [52, 53], spike timing-dependent plasticity [54], synaptic delay [29], random connectivity and noise [55–57], as well as an extension of the conductance-based neurons with a recovery variable [58–60].”

(Q2) Line 117 - Please specify what you mean by locally homogeneous, here.

Thank you for allowing us the opportunity to clarify this. We now report:

"By locally homogeneous, we mean that all neurons in the population are assumed to share the same extracellular and intracellular ionic environment and are connected with identical coupling rules, allowing us to treat the population as uniform with respect to ion dynamics and connectivity."

(Q3) In this sub-section the authors should clarify all the hypotheses they employ to derive the neural mass models, not only the Lorentzian approximation they did for a cubic model, but also the fact that they assume that the gating variable n is a global variable as well as that the potassium concentration are assumed to be the same for all neurons, that they assume no heterogeneity at this level. This is a fundamental aspect that should be clarified at this stage already.

We thank the reviewer for this important observation. We agree and have revised the text in the derivation section to explicitly state all key assumptions. Specifically, we now clarify that:

(1) The gating variable n is treated as a population-average (global) variable;

(2) The potassium concentrations Δ[K+]int and [K+]g are assumed to be homogeneous across the neuronal population; and (3) No heterogeneity is assumed at the level of the ion dynamics.

This assumption is biophysically motivated: ion concentrations — particularly extracellular potassium — tend to redistribute rapidly due to diffusion and electrochemical forces, leading to an effectively well-mixed environment at the mesoscopic scale. As such, assigning separate compartments to individual neurons is not justified in this modeling context. We now explicitly note this in the manuscript to avoid ambiguity.

“3) We assume that the potassium concentrations, both intracellular(\( \Delta[K^+]_{\text{int}} \)) and extracellular (through the buffering variable \( [K^+]_g \)), are homogeneous across the neuronal population. This is justified physiologically by the rapid redistribution of ions through diffusion and electrochemical gradients, which enforce near-instantaneous equilibration at the mesoscopic scale. As such, assigning separate compartments to each neuron is neither practical nor biologically meaningful in this context. We assume that the potassium concentrations, both intracellular (\( \Delta[K^+]_{\text{int}} \)) and extracellular (through the buffering variable \( [K^+]_g \)), are homogeneous across the neuronal population. This is justified physiologically by the rapid redistribution of ions through diffusion and electrochemical gradients, which enforce near-instantaneous equilibration at the mesoscopic scale. As such, assigning separate compartments to each neuron is neither practical nor biologically meaningful in this context; 4) We assume that the gating variable n, which governs potassium conductance, can be treated as a population-averaged variable. This allows us to describe the neuronal ensemble using a reduced set of collective (mean-field) variables.”

Comparison with neural network simulations

(Q4) The comparison the authors perform between the microscopic model and the neural mass is misleading, From what the authors wrote it seems that you are considering 4 variables for each neuron in the network model (this is unclear from how the model is written in Eq (9)), I guess one for the membrane potential, one for the gating variable and two for the potassium concentration. However, this is not the network model for which the neural mass has been developed, the neural mass has been obtained for a network made of N + 3 variables (N membrane potentials and 3 collective variables for gate, and potassium concentrations) this is a sort of mesoscopic network models, analogously to what done previously in references [R1,R3,R4] above and others. If the authors would compare their neural mass with this mesoscopic model the agreement among the two would be improved.

We agree with reviewer’s observation and we now acknowledge this issue in the Results and in the Limitations. We have already modified the text to explicitly state that for the mean filed derivations n is treated as a collective variable and we have added the following statements:

“Also note that the gating variable n is treated as microscopic in the neural network, while in the derivations for the mean-field it is considered as a mesoscopic and identical for the whole population. This is likely responsible for some of the discrepancies between the two modalities.”

“Moreover, the discrepancy between the two modalities would have likely been smaller if for the neural network we also adopted a gating variable that is mesoscopic and identical across the spiking neurons, as in similar works [49–51]. However, here we demonstrate the validity of the mean-field approximation even for the more natural, microscopic representation of the gating variable in the neural network.”

Comparison with in vitro experiments

(Q5) Experiment -- The experiment is performed in vitro on the intact Hippocampus of mice between postnatal days P5-P7. It is known [R1] that neuronal activity at an early developmental stage is provided in the Hippocampus by a network primarily driven by synchronized GABA_A that provides an excitatory action and generates giant depolarizing potentials (GDPs) [R11]. However, GDPs have frequencies in the range of 1 Hz - 0.1 Hz, not matching the oscillation frequencies reported by the authors. I have several questions here:

(E1) At this stage P5-P7 are the interactions among neurons essentially excitatory? Or not, please explain why, Are the oscillations reported by the authors somehow related to GDPs? The depolarizing action of GABAergic transmission and the presence of GDPs during early rodent brain development, as described by Ben-Ari and some others researchers, are characteristics commonly observed in ex vivo brain preparations, but are not evident under physiological in vivo conditions (see doi: 10.3389/fphar.2012.00065).

In our preparation—intact mouse hippocampus—GABAergic synaptic transmission is not depolarizing. This is evidenced by the fact that inhibition of ionotropic GABA_A receptors with bicuculline triggers interictal-like discharges, which are routinely used as a model of epileptiform activity (see doi: 10.1016/j.nbd.2014.12.013). Therefore, in our experiments at P5–P7, neuronal interactions are not purely excitatory, and the observed low Mg2+ induced oscillations are not related to GDP.

(E2) What is the nature of the oscillations reported by the authors in Figure 4 ? Which is their origin, please explain in the text of the paper clearly.

The model of epileptic discharges presented in our study was first introduced over 20 years ago and has since become a well-established paradigm for screening potential antiepileptic drugs and research on the mechanism of epileptic seizure. A detailed description of this model can be found in doi: 10.1046/j.1460-9568.2002.02143.x, and its pharmacological properties are reviewed in doi: 10.1046/j.1528-1157.2003.19503.x. These references have now been added to the manuscript for clarity.

We have added the following:

“The model of epileptic discharges presented in our study was first introduced over 20 years ago [115] and has since become a well-established paradigm for screening potential antiepileptic drugs and research on the mechanism of epileptic seizure [116].”

(E3) How exactly does the concentration of extracellular potassium ions change, this is not clear even in Methods, please clarify.

[R11] Excitatory actions of GABA during development: the nature of the nurture Y Ben-Ari, Nature Reviews Neuroscience 3 (9), 728-739 (2002).

We have now added a new Subsection in the methods explaining how we use Mg2+ variation to influence the external potasium variation.

“The membrane of hippocampal neurons is equipped with N-methyl-D aspartate type glutamate receptors (NMDARs). These receptors have a very high affinity for glutamate and can, in principle, be activated by ambient glutamate present at low concentrations in the brain extracellular fluid (ECF).Under normal physiological conditions, this activation does not occur because extracellular magnesium ions (Mg²⁺) block the NMDAR channel at membrane potentials more negative than about –50 mV; this voltage-dependent block prevents receptor activation at rest. When extracellular magnesium is removed, the block is relieved, allowing NMDARs to be activated, leading to neuronal depolarization toward the action potential threshold [117]. In addition, as a divalent cation, Mg²⁺ interacts with the negatively charged neuronal membrane, contributing to the stabilization of the resting membrane potential. Lowering extracellular magnesium concentration disrupts this effect, resulting in membrane depolarization [118]”

“Consequently, magnesium removal not only facilitates NMDAR-dependent depolarization, but also directly depolarizes neurons. This depolarization increases the driving force for outward potassium currents through K⁺ channels, meaning that variations in Mg²⁺ can indirectly influence external potassium dynamics during neuronal activity.”

(Q6) Lines 187-191 and Figure 4 -- The authors wrote : "In Figure 4.c we show the membrane potential and external potassium for a simulation of N = 3000 coupled HH-like neurons showing a similar behavior, although the parameters were modified to simulate shorter fluctuations for computational efficiency." This sentence is unclear. What is clear from Figure 4 is that the network simulations gave rise to collective oscillations on a completely different scale seconds with respect to minutes and also the profile of the potassium concentration has a clearly different evolution. From Figure 4 one can conclude that network simulations have nothing to do with the neural mass evolution and the experiment. I think the authors should better clarify and describe the results reported in Figure 4.

We thank the reviewer for the observation. We have revised the relevant section of the manuscript to clarify the interpretation of Figure 4 and avoid any implication of quantitative matching. As stated in our response to Reviewer 1 (comment 6), the comparison is intended to highlight the shared qualitative structure across experimental data, the neural mass model, and the network simulation — specifically, the modulation of fast bursting by slow extracellular potassium fluctuations. The difference in timescale in the network simulation arises from rescaled parameters used for computational efficiency. We now explicitly state this and have updated the figure caption and accompanying text accordingly to reflect these points.

(Q7) Why do the authors consider a purely excitatory network to describe the experimental results? What is the reason for this choice? Why they do not consider as usual balanced excitatory- inhibitory networks? Please clarify this point.

We thank the reviewer for raising this point. We chose to model a purely excitatory network as a first step in isolating the role of extracellular potassium dynamics in generating population-level bursting. This allows us to focus on the ion-driven modulation mechanisms without introducing additional complexity from inhibitory feedback. Similar modeling choices have been made in previous studies of bursting and seizure-like dynamics (e.g., Gutkin et al.,), where inhibition is omitted to emphasize intrinsic or modulatory mechanisms. We acknowledge that incorporating inhibitory populations is an important next step for capturing a broader range of dynamics, but for the current study, the excitatory-only network provides a minimal and interpretable framework aligned with our focus.

(Q8) By comparing Figures 4 (a) and (b) it seems that the bursting activity observed in the experiment and in the mean-field simulations seem quite different, originating from different mechanisms and bifurcations, Can the authors comment on this?

We thank the reviewer for this important observation. We have reorganized the presentation of Figure 4 and revised the accompanying text to better clarify the nature of the comparison (see also our response to Reviewer 1, point 6). Our aim is not to claim that the experimental and simulated bursts arise from identical bifurcation mechanisms, but rather to highlight shared qualitative features — in particular, slow modulation of population activity by extracellular potassium. We now also comment on the potential role of more complex or noise-driven bifurcations (see Saggio et al. 2020) in shaping experimental bursting dynamics, which are not fully captured by the current deterministic model.

Bifurcation analysis: emergent network states and multistability

(Q9) This sub-section will gain interest by reporting simulations of the network and of the neural mass model presenting bistable dynamics.

We agree with the reviewer that this would be an important addition, but we believe that it goes beyond the scope of this work (for the computational reasons among others) and it remains for future work. We have however updated the bifurcation analysis section.

Limitations of the model

(Q10) Lines 276- 280 -- I think that the parameters c+,c_,R+,R_ depend not only on the slow variables, potassium concentrations but also on the actual value of the gate variable n. This should be stressed.

We thank the reviewer for this helpful observation. We agree and have clarified in the revised manuscript. This reflects the mean-field assumption that n is treated as a collective variable, and we now make this dependency explicit in the text.

“Furthermore, the parabola coefficients c_-,c_+, R_-, R_+ were fixed as constants, however, these coefficients could be made functions of the slow variables and the gating variable, which might unveil new dynamical regimes and extend the validity of the thermodynamic limit beyond the regimes described in this work. Also, in the case of constant values, an in-depth exploration of the parameter space is required to fully characterize the model and its bifurcation structure.”

(Q11) The authors wrote: " Other limiting assumptions are the moment closure condition (19) and the assumptions that the functions (3) averaged across the neuronal population can be expressed as functions of the average membrane potential V and gating variable n (which is only true in the cases where the functions (3) can be reasonably approximated as linear functions in a range of V and n." Apart from that a parenthesis is lacking, I think that this last aspect has been already taken into account when performing the fit with 2 parabolas to the sum of the currents, or not? In case, please specify.

We thank the reviewer for catching the missing parenthesis — this has been corrected in the revised manuscript. Regarding the modeling point: the two-parabola fit applies specifically to the membrane potential dynamics and captures the nonlinear dependence of the total current on V (eq.16). In contrast, the moment closure assumption involves approximating averages of nonlinear functions of both V and n, such as those appearing in the gating dynamics (e.g., n∞(V)). This is not directly accounted for by the parabola approximation, but is handled separately via the mean-field approximation of G^n as a function of the average variables (eq.15).

(Q12) A limitation that should be stressed is that the authors in the neural mass model consider the gate variable and the potassium concentrations, as global variable equal for all neurons, and where n depends on the mena membrane potential, to write that the moment closure (19) is a limiting assumption is honestly too clear, please be explicit here.

We have now the following two statements:

“These slow variables are in addition considered to be mesoscopic, meaning they are identical for every neuron in the population.”

“In our mean-field model, the gating variable (n) is treated as a global population variable, evolving deterministically as a function of the average membrane potential. Therefore, ⟨n(t)⟩ corresponds to the collective gating variable assumed to be shared by all neurons, and is not computed by averaging distinct microscopic (n_i) values.”

Discussion

(Q13) The authors could discuss in this section the further biological ingredients they can introduce in their neural mass based on the previous works [R1-R9] that have already shown how to include plastic synapses, random connectivity, noise, adaptation, spike-timing-dependent plasticity, etc and which of these ingredients they consider more relevant for the whole brain dynamics.

In order not to repeat the same statements from the Introduction, we have now addded the following sentence:

“This approach, taking into account key biophysical details, offers a first step in considering the role of the glia in neural tissue excitability. Following this direction, other ions, such as calcium should be taken into consideration, as well as other effects such as plastic synapses, random connectivity, noise, adaptation, spike-timing-dependent plasticity, as already discussed in the Introduction.”

(Q14) The authors should also discuss why they limited their analysis to purely excitatory networks, and what would change by including excitatory-inhibitory interactions in each single mass and across neural masses, if this makes sense or not.

As stated in our response to Q7, we chose to focus on purely excitatory networks as a first step to isolate and study the core role of extracellular potassium dynamics in driving bursting behavior. This modeling choice allows for a minimal system where the interaction between intrinsic ionic mechanisms and network coupling is most transparent.

We also note that excitatory and inhibitory effects can be modeled within the same formalism by adjusting the synaptic reversal potential — for example, $E_{syn}=0$mV for excitatory, and $E_{syn}=-80$mV for inhibitory interactions. Including inhibitory populations would introduce additional complexity and richer dynamical regimes (e.g., oscillatory instabilities, balance states), which are certainly of interest but beyond the scope of this study.

Materials and Methods

(Q15) Fig.2 - I think a plus is lost in panel (c) where it should be [K+bath];

Thank you. We corrected the figure.

(Q16) Caption of Figure 2- the authors wrote: "In the case where the derivative of the membrane potential is zero for V > V ⋆ (e.g., if the cubic function is shifted up by adding a constant current to the membrane potential derivative), the population is described by the red distribution in the steady state, and the continuity equation is governed by the negative parabola equation." This sentence is unclear, the authors mean in the case where the derivative of the membrane potential crosses zero at V > V*? Please clarify.

We thank the reviewer for pointing this out. Yes, we refer to the case where the membrane potential derivative crosses zero at a point V>V∗. We have clarified this in the revised figure caption.

(Q17) Lines 558-562 -- Eqs (6) and (7) are examples of unnecessary complications of which this manuscript is full of. Since the authors do not consider any synaptic dynamics and homogenous (equal) couplings, these equations are not needed, I strongly recommend removing Eqs (6) and (7) and limiting to the expression reported in Eq (8), which indeed should also be corrected see next remark.

We appreciate the reviewer’s concern regarding clarity. As mentioned in our response to Reviewer 1, the inclusion of Eqs. (6) and (7) was intentional and serves a pedagogical purpose — to present the general structure of the network interactions before introducing simplifying assumptions. While we agree that Eq. (8) suffices for the simulations considered in this manuscript, we believe that showing the more general form helps clarify the model’s extensibility, for instance to cases with heterogeneous coupling or synaptic dynamics.

(Q18) Eq (8) - line 562 - Since the authors assume no synaptic evolution, i.e. instantaneous post-synaptic potentials, they can clarify that Eq (8) represents the population firing rate that later will be one of the fundamental variables of the neural mass model and call it r, as in the following. Furthermore, $s_i$ does not depend on the neuron index $i$ in a fully coupled network with homogenous coupling, as in the present case, this quantity is the same for all neurons. Please drop the index and call it r since it is the population firing rate.

We thank the reviewer for this useful suggestion. We now clarify in the text that under the assumptions of all-to-all homogeneous coupling and no synaptic dynamics, s_i is identical for all neurons and can be interpreted as the population firing rate r. This connection is made explicit in the revised manuscript.

“Under the assumption of instantaneous synaptic transmission and homogeneous all-to-all coupling, the synaptic activation variable (s_i) is the same for all neurons and corresponds to the population firing rate, which we denote by (r)”

(Q19) Line 564-567 - Here the network model is incomplete, it is not sufficient that the authors report the evolution equation for the membrane potential Eq (9). They should report the evolution equation for the gate variable n and for the potassium concentration as done in Eq (1). This request is fundamental because it is unclear from the present formulation which are the variables that are microscopic (associated with the single neuron evolution) and which are global (common to all the neurons). This is a fundamental aspect and it should be clarified. I guess that n will depend on the neuron index $i$, while the potassium concentration it is unclear how the authors will consider them, global or local. I guess that the internal density should depend on the neuron index $i$ or not ? Anyway, I would like to know exactly which network model has been simulated e.g. to obtain the results reported in Figure 3.

We thank the reviewer for this essential clarification request. In the revised manuscript, we now explicitly state the full network model, including the evolution equations for the gating variable n_i and potassium variables. While in some simulations we consider the full microscopic model involving 4N variables (where each neuron has its own V_i ,n_i ,Δ[K+]int_i ,[K+]g_i), for the mean-field reduction and mesoscopic comparisons we assume that the gating and potassium variables are shared across neurons. This assumption is consistent with prior work (e.g., Chen & Campbell) and is biophysically justified in the case of potassium due to its fast spatial equilibration in extracellular space. We also now mention this explicitly in the Limitations.

(Q20) Continuity equation - Lines 568 - 597 - This part can be largely simplified and rewritten, as a matter of fact, the authors consider the gate variable n, the potassium concentrations as global (collective variables) depending on mean field values of <V> they can directly start from eq 20, by stating that they assume that the other variables (n, $\Delta[K^+]_{int}$, $[K^+]_g$) are collective variables, common to all the neurons, and that depends only on mean field variables as <V> or r. This has been done in many previous cases since the Ott-Antonsen Ansatz can be applied whenever the potential evolution is driven by quadratic terms and in the presence of mean field variables, the first indication of this was reported in 1993 by Watanabe and Strogatz for phase oscillators :

[R12] Watanabe, Shinya, and Steven H. Strogatz. "Integrability of a globally coupled oscillator array." Physical review letters 70.16 (1993): 2391.

Anyway, this approach has been previously employed to derive a neural mass model for networks of QIF neurons in the presence of various further neuronal variables (ranging from slow currents to plastic evolution of the couplings) describing more biologically realistic situations, see references [R1-R7] above. I strongly encourage the authors to reformulate their approach in a simpler and clearer manner, particularly interesting is for them the article [R6] by Guerriero et al, the authors examine exactly the same model as in Ref [95] [Chen, L. & Campbell, S. A. Exact mean-field models for spiking neural networks with adaptation. Journal of Computational Neuroscience 50 (4), 445-469 (2022)]. However, they solve the problem in a much more simple way, I encourage the authors to follow this approach.

We thank the reviewer for the constructive suggestion. We acknowledge that, under the assumption that n, Δ[K+]int , and [K+]g are collective variables shared across the neuronal population, one could directly begin from Eq. (20) and proceed using the simpler approaches found in Guerriero et al. [R6] or related works [R1–R7]. However, we chose to retain the Chen & Campbell formalism, with additional clarification regarding the mesoscopic nature of the gatin variable, as it explicitly highlights the key approximations used in the derivation, which may be beneficial for readers seeking to extend the method. See also general response to reviewer 2 at the beginning.

(Q21) Eq (26) -- I do not think the authors can estimate explicitly <n(t)> from the equation (26), as they do for the mean membrane potential and the firing rate. This is just a formal expression representing a collective variable, I do not think that <n> will coincide with the average of the values of n_i for each neuron. Please discuss this point, and in this case show that <n> indeed coincides with the average of all of the values of the single neuron gate variable n_i.

We thank the reviewer for raising this important point. We agree that Eq. (26) is more formal than operational, as ⟨n(t)⟩ is not directly derived from the continuity equation in the same way as ⟨V⟩ or the firing rate r. Rather, it reflects our mean-field assumption that the gating variable evolves as a collective population-averaged quantity, governed by the dynamics of the average membrane potential. In our formulation, n is treated as a global variable shared across neurons, and thus ⟨n(t)⟩ effectively is the gating variable in the neural mass model — rather than the result of averaging heterogeneous n_i. We have clarified this distinction in the text to avoid suggesting that Eq. (26) provides an explicit estimate of microscopic gating dynamics.

“Unlike the mean membrane potential ⟨V⟩ and the firing rate (r)>, which can be explicitly derived from the continuity equation under the Lorentzian assumption, the expression for ⟨n(t)⟩ in Eq. (26) is formal. In our mean-field model, the gating variable (n) is treated as a global population variable, evolving deterministically as a function of the average membrane potential. Therefore ⟨n(t)⟩ corresponds to the collective gating variable assumed to be shared by all neurons, and is not computed by averaging distinct microscopic (n_i) values.”

(Q22) Mean-field dynamics for the gating variable - All this sub-section is in my opinion not useful, if the authors assume from the beginning that <n(t)> is a global variable. Indeed in the end they write for <n(t)> the evolution equation Eq (30) which is the same equation as for the single neuron gate variable (1) but for the mean values of n and <V>. I suggest removing this sub-section.

We thank the reviewer for this suggestion. We agree that, under the assumption that n is a global collective variable, the resulting equation for ⟨n(t)⟩\langle n(t) \rangle⟨n(t)⟩ is equivalent in form to the single-neuron gating equation, driven by the average membrane potential. However, we chose to retain this subsection to explicitly demonstrate how the gating dynamics enter into the mean-field formulation, especially for readers less familiar with this type of reduction. This step also mirrors the structure of the derivation used for other state variables in the model and maintains clarity for potential extensions where n may not be strictly global.

(Q23) Line 696 - here an equation reference is lost.

Thank you for pointing this out. We have corrected the text and restored the missing equation reference in the revised manuscript.

(Q24) Eqs (36) -(37) -- Since the variables r and x entered in Eq (36) are essentially the same as Eq (25), apart from a constant R/pi, the use of two different names complicated in a useless manner an already complicated expression, Please decide to use everywhere r or x and then proceed consequently this applies also to Eq (37). This will also allow us to rewrite the equation in x or r in a more compact form.

As noted in our response to Reviewer 1, point 14, we have revised Eq. (37) to ensure consistency in notation by replacing x with r throughout.

(Q25) Eq (37) - This equation is written in a manner that is not careful enough, apart from that the authors are passed now from (x,y) to (pi*r/R,V) , therefore they should substitute everywhere x with r. Furthermore, the equation for the derivative of V is confusing, the authors should use the same approximate expression employed in eq (36) that makes explicit the quadratic dependence on V itself, otherwise, I believe that the equation is incorrect.

In the same response to Reviewer 1, point 14, we also clarified the expression for \dot{V} in Eq. (37), we reintroduced the full current-based formulation (as in Eq. 16), reversing the quadratic approximation used earlier. This is now explicitly stated in the text, and we have improved the equation presentation to avoid confusion.

(Q26) Eq (37) below line 708 - From this expression, it is clear that the gate variable n and the potassium variables are ruled exactly by the same equations as for the single neuron Eq (1) and that the Lorentzian Ansatz enter only in the rewriting of the evolution of the membrane potentials of the neurons in the network. In the end, the authors are doing exactly the same approximation made by many other authors [R1-R7], that these variables are collective, i.e. they are the same for all neurons, and in particular n=n(V) is a function of the mean membrane potential V. The mean field model that the authors derive corresponds to a microscopic model where the single neurons are heterogenous only in the intrinsic currents $\eta_i$, but they are all driven by collective variables, like n(V) and the potassium variables that are identical for all neurons. This should be clarified.

We agree with the conclusion by the reviewer, and as seen through the previous responses, we now explicitly acknowledge the fact that n and the two slow variables are considered as a mesoscopic variables for the mean-field derivation, while for the spiking network, n remains microscopic.

Author response:

We are writing to provide our provisional response to the public reviews. We note that the reviewers’ comments focus primarily on strengthening technical rigor and quantitative interpretation. We have designed the planned revisions to directly address the reviewers’ major concerns and to strengthen the study’s evidentiary basis. We plan to submit a revised manuscript for the final Version of Record.

For clarity, we summarize below the major new experiments and analyses that address the reviewers’ primary concerns:

(1)Validation of Tracking Parameters (Reviewers 1 & 3): We will re-analyze our single molecule tracking data with tighter gap-time allowances (0 seconds) to demonstrate the robustness of our interpretations of short- and long-lived kinetics. We will also generate a supplementary movie with binding trajectories superimposed directly on detected molecules to visually confirm tracking robustness.

(2) Photobleaching & Two-State Controls (Reviewers 1 & 3): We will report per-cell photobleaching lifetimes derived from our global fluorescence decay. To strengthen this analysis, we will include supplementary measurements using a H2B-HaloTag control under matched imaging conditions and perform single-molecule tracking of GATA2 zinc-finger deletion mutants (N-terminal, C-terminal, and double) as a binding-deficient functional control.

(3) Protein Expression & Labeling Efficiency (Reviewers 1 & 2): To address concerns about transgene expression and competition with endogenous proteins, we will quantify Halo-GATA2 levels in G1E-ER4 and HPC7 cells and SNAP-GATA2 levels in primary cells using standardized titration methods with established Halo-CTCF and SNAP-RPB1 reference systems.

(4) Integration of SMT and CUT&Tag (Reviewer 3): We have conducted a quantitative foldchange analysis of our existing CUT&Tag dataset to complement our single-molecule kinetics.

However, as detailed in our specific response below (R3 point 5), we emphasize that directly integrating population-level genomic occupancy measurements with single-cell kinetic measurements is not straightforward. We will therefore frame the relationship between these datasets as a conceptual consistency check rather than a strict quantitative integration. This quantitative analysis supports and refines the Early-restricted peak set, identifying a high confidence strict subset consistent with the broader presence/absence-defined set described in Figure 5 of the manuscript (see Author response images 1–3 and our response to R3 point 7).

(5) Characterization of the GATA2-SNAP Mouse (Reviewer 3): We have characterized hematopoietic populations in the homozygous knock-in mouse, including lymphoid (CD3⁺/CD4⁺/CD8⁺/B220⁺/CD19⁺), myeloid (CD11b⁺/Gr1⁺), and erythroid (Ter119⁺) compartments. These data, presented in Author response image 4, indicate that normal mature hematopoietic output is preserved across genotypes. Statistical caveats are described in the corresponding figure legend and in our response to R3 point 8.

Public Reviews:

Reviewer 1 (Public review):

(1) Two binding states: justification and controls

The authors propose two states of GATA2 binding. Are there only two states? Some longbinding duration distributions here are very long-tailed (e.g., Figure 2D middle), suggesting a possible third state. The authors must explain how they determined that two states provide the best fit and how they classified short versus long binding. Controls should be included for long-lived and short-lived binding (e.g., histone proteins, HaloTag-NLS, or a binding-deficient GATA2 mutant).

Agreed in part; we will attempt the requested binding-deficient control using existing GATA2 deletion constructs, complemented by GRID and H2B-HaloTag controls.

We will clarify that the two-state framework is an operational model rather than a claim that GATA2 can occupy only two physical states. This approach is widely used in SMT studies of chromatin-associated transcription factors and transcription machinery (Gebhardt et al., 2013; Liu et al., 2014; Hansen et al., 2017; Kenworthy et al., 2022). In particular, Ling et al. (Science, 2026) recently used two-exponential survival-probability fitting across 58 Halotagged transcription-associated proteins to distinguish transient and stable chromatin-binding populations, while explicitly noting that the simplified two-state model provides a tractable framework even when the underlying physical behavior may be more heterogeneous.

We agree that our current two-state model may under-represent the diversity of GATA2 chromatin-binding populations in single cells. However, even within this simplified framework, the existing analysis already indicates increased upper-tail dispersion of kinetic measurements (e.g., residence time and/or percentage of stable events) at the single-cell level in early erythroid cells. To support the goodness-of-fit metrics from our two-state fitting, as Reviewer 3 recommends, we will provide a supplementary table containing confidence intervals for the rate parameters and an F-test metric describing the differences between one- and two-state fits.

To determine whether additional binding states exist, we will perform GRID (Genuine Rate Identification from Distributions), which does not bias the model toward a particular number of states and, in our experience across multiple proteins, yields fits with 3-5 binding populations. However, we have found that in many cases, GRID requires aggregating binding events from multiple cells to achieve consistently robust fits for the populations of relatively rare, long-lived (>~30 sec) binding events. Therefore, GRID will assess whether additional populations exist, but we will lose the ability to analyze changes in the cell populations at the single-cell level.

We will include the multi-state analysis as a new supplementary figure. We will additionally clarify in the Results and Methods exactly how short- and long-lived binding events are classified (1-second threshold consistent with prior single-molecule frameworks for transcription-factor chromatin interactions; Gebhardt et al., 2013; Liu et al., 2014; Kenworthy et al., 2022) and direct the reviewer to these passages.

For the requested controls, we will include H2B-HaloTag imaging under matched conditions as a long-lived reference for both photobleaching correction and as a positive control for stable chromatin association, addressing R1 point 2 and R3 point 1 simultaneously.

We will also attempt to address the reviewer’s request for a binding-deficient control. We have lentiviral constructs in hand that encode GATA2 with a C-terminal zinc-finger deletion (which removes the primary DNA-binding domain), an N-terminal zinc-finger deletion, and a double deletion. We will perform single-molecule tracking of these mutants in the engineered cell systems and test whether removing GATA2’s specific DNA-binding capacity produces the predicted reduction in long-lived chromatin engagement, providing a functional perturbation control. The interpretation of these experiments will depend on the mutants expressing and localizing appropriately, which we will validate before drawing kinetic conclusions. We note that an analogous binding-deficient mutant cannot be examined in the physiological context of the Gata2SNAP knock-in mouse, and we will frame the cell-line mutant analyses accordingly. Together with GRID and the H2B-HaloTag control, these mutants provide complementary lines of validation for the two-state kinetic framework.

(2) Photophysical and focal-plane artifacts

The authors should exclude contributions from (i) photobleaching, (ii) blinking, and (iii) Z-axis motion. Describe and quantify the photobleaching correction. Provide analyses or controls that distinguish true dissociation events from photophysical blinking/bleaching or axial motion.

Agreed.

We will substantially expand the methodological description and provide three new pieces of supplementary analysis:

- Photobleaching: A per-cell photobleaching-rate distribution will be plotted for each cell type and differentiation stage, and photobleach-corrected residence-time values will be reported alongside apparent values in the relevant figures. We will also perform H2B-HaloTag imaging under matched illumination, exposure, and dye conditions in each cell line as a longlived chromatin-bound reference, establishing per-cell-type bleach lifetimes to which the GATA2 measurements can be referenced. This approach follows recent SMT precedent in which H2B decay was used to correct residence-time measurements for photobleaching, chromatin and nuclear motion, microscope drift, defocalization, and dye photophysics (Ling et al., Science 2026). The right-censoring photobleach-correction model used in our analysis will be described in detail in the revised Methods, including parameter values and per-cell handling.

- Blinking: The STRAP single-particle tracking pipeline already accommodates fluorophore blinking when linking trajectories across successive frames, following the multiple-targettracing framework of Sergé et al. (Nature Methods, 2008). This use of short gap-frame allowances to avoid artificially splitting trajectories due to fluorophore blinking or transient defocalization is consistent with recent live-cell SMT studies of chromatin-associated factors (Ling et al., Science 2026). We will add an explicit statement to the Methods describing how blinking-tolerant linkage parameters are set, and we will reanalyze representative datasets

with stricter maximum off-frame settings to ensure this parameter does not drive our conclusions (also addressing R3 point 6).

- Z-axis motion: Given our 500-ms exposure and the ~500-nm axial detection range of the HiLo configuration, axial loss is expected to be a minor contributor. We will quantify this indirectly by plotting, as a supplementary analysis, the maximum in-plane 2D spatial exploration of each binding trajectory, defined as the long-axis diameter of the 2D trajectory envelope. Although this does not directly measure z-position, it serves as a control for large apparent displacements that could reflect molecules moving out of the HiLo detection volume and demonstrates that observed dissociation events are not dominated by axial drift.

Representative photobleaching traces from individual cells (lowest, highest, and median bleach rates) will be included to support the single-molecule interpretation (also addresses R1 point 5).

(3) HILO illumination and nuclear region sampled

HiLo is sensitive to illumination angle: slight changes sample different nuclear regions. Explain how the HiLo angle was controlled and confirmed comparable across cells and conditions.

Agreed.

We will add a Methods subsection describing our HiLo illumination procedure. In brief, we started at a TIRF-supercritical angle and reduced it toward epifluorescence just enough to achieve high imaging depth while minimizing out-of-focus background signal. Within each biological system (cell line or primary cells), the TIRF angle was held constant across Basal, Early, and Late conditions to ensure direct comparability of kinetic measurements across stages.

(4) Quantification of event counts and long-binding durations

The number of binding events and the duration of long-binding events are influenced by imaging conditions. Provide a more detailed analysis of how these variables were controlled and assess the sensitivity of the results to detection and tracking parameters.

Agreed.

We will (i) normalize per-cell binding-event counts to nuclear cross-sectional area (extracted from the segmented nuclear masks already in the STRAP pipeline) to control for differences in nuclear size; (ii) report the tracking-parameter sensitivity sweep described above; and (iii) confirm in the revised Methods that all imaging conditions (laser power, exposure, dye concentration, sample preparation) were held constant across stages and cell types, consistent with the existing manuscript text. Per the Reviewing Editor’s guidance, the planned labeling-efficiency and absolute-molecule-quantification experiments will further constrain the interpretation of binding-event counts across conditions.

(5) Evidence that spots are single molecules

Provide evidence that spots represent single molecules.

Agreed.

We will include a small number of per-event intensity traces from our STRAP tracking output, selected to illustrate the single-step photobleaching behavior characteristic of single-molecule emission (intensity remains approximately constant during the binding event and then drops to background in a single step). The nuclear-fluorescence measurements from the planned labeling-titration experiment will also allow us to confirm that bound-spot densities are consistent with single-molecule occupancy at the labeled fraction used for tracking.

(6) Description of the spot-analysis pipeline

The Methods should include a detailed STRAP pipeline description.

Partially agreed; the existing STRAP reference is appropriate, but the Methods will be expanded.

STRAP (Haque & Coleman, 2025) is a consolidated, automated implementation of two well-established, previously published frameworks: SLIMfast / multipletarget tracing (Sergé et al., 2008) and evalSPT (Normanno et al., 2015), both of which are cited in the original manuscript. We will expand the Methods to describe the parameter set used in our analysis (detection thresholds, linking radii, gap-frame allowance, photobleaching correction model) so that readers can assess the analysis without referring exclusively to the STRAP manuscript and code repository, while preserving the cited STRAP reference for the full algorithmic description. We respectfully suggest that a complete pipeline description duplicating Haque & Coleman (2025) would not be appropriate in a primary research article.

(7) Differences among cell systems

The three cell systems yield notably different results. Provide a more detailed explanation for these differences.

Agreed.

We will also explicitly describe the caveats of the engineered systems versus the native GATA2-SNAP primary-cell system, in which endogenous GATA2-SNAP remains under physiological regulation. Specifically, we will discuss how variables such as the GATA1null background, ectopic forced nuclear import of GATA1-ERT, and ectopic GATA2-Halo in G1E-ER4 cells, as well as ectopic GATA2-Halo, endogenous GATA1, and cytokine signaling in HPC7 cells, likely contribute to the observed differences in signatures.

Reviewer 2 (Public review):

(1) Expression levels of the GATA2-HaloTag transgene

Determine the expression levels of the GATA2-HaloTag transgene over the course of differentiation under the conditions used for single-molecule imaging.

Agreed.

This is the central concern flagged by the Reviewing Editor. For each cell line (G1E-ER4 and HPC7), we will (i) measure total nuclear GATA2-Halo fluorescence per cell under matched acquisition conditions and (ii) convert this fluorescence intensity to absolute molecules per cell using a Halo-CTCF/U2OS reference standard (Cattoglio et al., 2019; absolute CTCF abundance quantification applied previously by our group). This will provide per-cell GATA2Halo molecule counts at each differentiation stage (Basal, Early, Late). For the primary GATA2SNAP cells, we will perform the analogous comparison against a SNAP-RPB1/U2OS standard.

(2) Fraction of molecules labeled

Carry out a titration of the HaloTag ligand and compare the amount of labeled protein under single-molecule imaging conditions to that of saturating labeling.

Agreed.

We will perform HaloTag-ligand and SNAP-tag-ligand titrations in each cell type, comparing nuclear fluorescence under the limiting-label conditions used for single-molecule tracking with that under saturating labeling. This will yield a per-cell-type labeled fraction and allow us to confirm that comparisons of binding-event counts across conditions are not confounded by differences in labeling efficiency. The labeled-fraction values will be reported in a new supplementary figure and incorporated into our quantification of binding-event rates.

(3) Robust single-particle tracking

Show images of particle trajectories or movies superimposing trajectories on imaging data.

Agreed.

We will generate visualizations of selected long-lived binding events with single-particle trajectories overlaid on the imaging data — using a multi-frame color overlay (e.g., five sequential frames in distinct colors superimposed) so that linkage of the spot across frames is visually unambiguous — and include them as a new supplementary figure or movie. Examples will be drawn from each cell system to demonstrate consistent tracking quality.

Reviewer 3 (Public review):

(1) Photobleaching correction; per-cell bleach lifetimes

Report the per-stage (or per-cell) photobleaching lifetimes and the photobleachcorrected residence time values alongside apparent values, ideally with an H2B-Halo control.

Agreed.

Addressed by the photobleach-rate distribution and H2B-HaloTag control analyses described under R1 point 2. The supplementary figure will explicitly compare per-cell bleach lifetimes across stages, report photobleach-corrected residence-time values alongside apparent values and include H2B-HaloTag controls under matched conditions in each cell line.

(2) Mechanistic differences across systems

The three systems show qualitatively different signatures: residence time change in G1EER4, bound fraction expansion in HPC7 and primary cells. Reporting an on-rate proxy alongside k_off would help.

Agreed.

Addressed by the cross-system kinetic framing described under R1 point 7 and by the GRID state-spectrum analysis described under R1 point 1. We will explicitly frame the three systems in terms of underlying kinetic mechanism in both Results and Discussion, following the conceptual distinction emphasized by Ling et al. (Science 2026) in which residence time reports binding stability once engaged, whereas changes in bound fraction or event frequency can indicate altered association/recruitment efficiency. In this framework, the G1E-ER4 residencetime signature is consistent with reduced dissociation (a longer-lived bound state), while the longlived-fraction expansion in HPC7 and primary cells is consistent with an increased target-search efficiency or specific-binding-competent pool. Alongside the GRID-derived state-spectrum analysis, we will report an apparent engagement-rate proxy calculated as binding events per unit imaging time normalized to detectable molecule number; this proxy is an approximation, not a direct k_on measurement, as accurate determination of k_on from single-molecule tracking requires concentration-dependent on-rate experiments that are outside the scope of the present study. We thank the reviewer for this suggestion, which we agree sharpens rather than alters the central message.

(3) Per-cell GATA2 concentration and the uncoupling claim

Quantify total nuclear GATA2-Halo signal per cell across stages; for primary cells, a western blot or quantitative immunofluorescence on flow-sorted populations would make the uncoupling argument more defensible.

Agreed.

For the cell lines, the per-cell nuclear GATA2-Halo quantification described in our response to R2 point 1 addresses this point.

For primary cells, where the biological claim is strongest, we will exploit the endogenous Gata2SNAP knock-in itself as a quantitative reporter of total GATA2 protein. Specifically, we will label flow-sorted CD71/Ter119 populations from Gata2-SNAP mouse bone marrow with SNAP-Cell 647-SiR at saturating concentration in a parallel acquisition to the limiting-label single-molecule tracking experiment. Total nuclear SNAP-GATA2 fluorescence at saturating labeling provides a measure of endogenous GATA2 abundance per cell at each erythroid stage, in the same chemistry used for our single-molecule measurements, and will be benchmarked against a SNAPRPB1/U2OS reference standard for absolute molecule counting. This approach (i) measures the protein of interest in the labeling chemistry already established in this study; (ii) avoids reliance on quantitative immunofluorescence, which we have not been able to validate under our flowsorted-cell conditions; and (iii) extends the same analytical framework — saturating versus limiting labeling, with U2OS reference standards — across cell lines and primary cells. Quantitative western blotting on flow-sorted populations remains an alternative we will consider if specifically requested by the reviewers.

(4) Single-cell distribution analysis

Distribution-based statistics (K-S test, mixture model) rather than (or alongside) meanbased ANOVA, particularly for the Early populations, which look potentially bimodal.

Agreed.

We will perform Kolmogorov–Smirnov and Gaussian mixture model analyses of the single-cell long-lived fraction and residence-time distributions across stages, reporting these alongside the existing Welch ANOVA results in a new supplementary figure. This analysis is consistent with the conceptual framework cited in the manuscript (Wheat et al., 2020; Palii et al., 2019) for probabilistic hematopoietic transitions and may reveal subpopulation structure underlying the Early-stage signal. The GRID analysis further complements this by formally testing whether multi-state mixture models are statistically preferred at each stage. However, GRID analysis requires aggregating binding events across cells, which limits our ability to monitor changes in population dispersion at the single-cell level.

(5) Quantitative integration of CUT&Tag with SMT

Attempt a back-of-the-envelope calculation of whether the residence-time or fraction changes are quantitatively consistent with the acquisition of the 1,167 Early-restricted sites.

Partially agreed; will attempt an order-of-magnitude framing.

We thank the reviewer for this thoughtful suggestion. We agree that more explicit framing of the quantitative relationship between the two datasets will strengthen the integration. We will add a paragraph to the Discussion presenting an order-of-magnitude calculation linking the observed residence-time and long-lived-fraction changes to the steady-state occupancy increase predicted at competent regulatory sites, with explicit caveats regarding (i) the inherently semi-quantitative nature of CUT&Tag signal and (ii) the assumptions required to translate population-averaged occupancy into the genome-wide site count observed. For the G1EER4 cells, we observe relatively minor shifts in population-mean behavior as single-cell dispersion increases. Therefore, it may be difficult to directly link population-based measurements (e.g. CUT&Tag) with single-cell kinetic measurements (SPT). This distinction between occupancy and dynamics is consistent with recent systematic SMT analysis of the eukaryotic transcription machinery, in which factors appearing persistently associated in ensemble genomic assays were shown to exchange on second-scale timescales in living cells (Ling et al., Science 2026), emphasizing that population genomic occupancy and single-molecule residence time are complementary but not directly interchangeable measurements. Closing this gap rigorously is a major hurdle for the field and will require substantial technology development on quantitative single-cell CUT&Tag occupancy measurements. We will therefore frame our analysis as a consistency check rather than a strict quantitative integration. The reviewer notes that this analysis “does not change the central message; it sharpens it,” and we agree.

(6) Short-lived kinetic interpretation and tracking parameters

The 1.5 s gap allowance is long relative to the short-lived residence times in primary cells. A sensitivity analysis with tighter gap parameters would help. Also clarify how slowing of search reconciles with increased binding events at Early.

Agreed.

Addressed by the tracking-parameter sensitivity analysis described under R1 point 2. We apologize for the lack of clarity in our original description of the gap allowance. Our current maximum off-frame parameter is set to 2 frames, corresponding to a 0.5-s gap allowance. We will rerun the tracking analysis on representative datasets using a maximum off-frame parameter of 1, corresponding to no missed frames, and will report the resulting residence-time distributions alongside the original analysis to demonstrate robustness. We will also clarify in the Results and Discussion how changes in short-lived binding kinetics are reconciled with the increase in detectable binding events at the Early stage, drawing on the apparent engagement-rate proxy interpreted alongside the GRID-derived state-spectrum analysis.

(7) CUT&Tag peak definition and quantitative analysis

Report (a) signal intensity distribution at the 1,167 sites across stages (scatter or density plot beyond the heatmap) or (b) differential binding analysis (e.g., DESeq2). State replicate count and overlap of Early-restricted sets across replicates.

Agreed; normalized fold-change analysis completed, with replicate-aware differential binding analysis planned if additional replicates are generated.

We have performed a normalized count-based fold-change analysis of the union peak set from the existing GATA2 CUT&Tag dataset (14,468 peaks) using the goodpeaks framework previously used in our group, yielding per-peak log2 fold-change values and discrete dynamicstatus calls (Gained / Lost / Unchanged at |log2FC| ≥ 2) for each of the two transitions (Basal → Early at 0 vs 2 h, and Early → Late at 2 vs 24 h). This provides a conservative quantitative complement to the presence/absence peak-calling analysis presented in Figure 5; if additional replicate data are generated, we will perform replicate-aware differential binding analysis (DiffBind/DESeq2; Love et al., 2014; Stark & Brown, 2011) and report replicate overlap. This analysis addresses option (b) of the reviewer’s request and also enables the visualization requested in option (a) as a cross-stage scatter (Author response image 1). We present the quantitative analysis as a supplement to the presence/absence-defined Early-restricted set in Figure 5 of the manuscript, providing two orthogonal lines of evidence for the same biology. We note that the CUT&Tag experiments were initially performed as a validation step to confirm that the tagged GATA2-Halo constructs recapitulate endogenous chromatin-binding behavior, including appropriate genomic localization and expected GATA switch dynamics. This validation supports the conclusion that the observed single-molecule kinetics reflect physiologically relevant GATA2 engagement. Having established this, we subsequently extended the dataset to perform the quantitative analyses presented here.

Quantitative findings.

- 384 peaks were Gained (|log2FC| ≥ 2) at the Basal → Early transition.

- 1,006 peaks were Lost over the same transition.

- 178 peaks were Gained at Basal → Early and subsequently Lost at Early → Late, defining the strict differentially-restricted Early set (Author response image 1, red points). This set represents the higher-confidence subset of the manuscript’s broader presence/absence-defined Earlyrestricted set (n = 1,167; defined as MACS2 peaks at q < 0.01 present at Early but absent at Basal and Late).

- 200 peaks were Gained at Early and retained at Late, indicating stable acquisition.

- 49 peaks were acquired only at the Late stage.

The discrepancy between the broader presence/absence set (1,167) and the strict differential set (178) reflects the analytical choice the reviewer raised: presence/absence calls based on a peaksignificance threshold are sensitive to near-threshold peaks, whereas differential analysis with a fold-change cutoff captures only sites with quantitatively pronounced stage-restricted enrichment. We interpret these as two complementary definitions: the broader set captures all peaks meeting a stage-specific peak-calling criterion, and the strict subset isolates the most quantitatively dynamic core of that population.

Importantly, the three named example loci shown in Figure 5D of the manuscript — Nono (promoter-proximal), Nr3c1 (intron 2), and Gata3 (distal intergenic) — all survive the strict differential criterion (each shows |log<sup>2</sub>FC| ≥ 2 in both transitions, consistent with a clean Gainedthen-Lost signature). The published example panel therefore represents the high-confidence intersection of both definitions, supporting the robustness of the manuscript’s selected illustrative cases.

We will explicitly state the number of CUT&Tag replicates per stage in the revised Methods and figure legends. Where the differential analysis is currently based on a single replicate per stage, we will explicitly note this and treat the strict subset as a conservative confirmatory analysis. An additional replicate is under consideration for the full revision, and if performed, overlap of Earlyrestricted calls across replicates will be reported.

Motif cross-validation against a matched-GC background using HOMER and/or MEME-ChIP is planned for the strict differential subset and will be reported alongside the original SeqPos analysis in the revised Figure 5F or its supplement.

Author response image 1.

Cross-stage log₂ fold-change scatter for GATA2 CUT&Tag peaks. Each point represents a single peak in the union peak set (n = 14,468). The x-axis shows the log2 fold change from Basal (0 h) to Early (2 h); the y-axis shows the log2 fold change from Early (2 h) to Late (24 h). The sign convention follows the field-standard direction (positive log2FC = increased signal at the later time point). Peaks are colored by dynamic-status classification: unchanged/other (gray; n = 9,794); Lost at Early (blue; n = 109); Gained at Early and retained at Late (orange; n = 200); acquired only at Late (teal; n = 49); and Early-restricted, defined as Gained at Early and Lost at Late with |log2FC| ≥ 2 in both transitions (red; n = 178). The Early-restricted population occupies the lower-right quadrant, consistent with a transient kinetic peak of GATA2 binding.

Author response image 2.

Density representation of GATA2 CUT&Tag peak dynamics with Early-restricted peaks highlighted.

Author response image 2 is shown for illustrative reference and is not annotated with a separate legend; it presents the same data as Author response image 1 in a hexbin density format to emphasize the bulk of unchanged peaks at the origin and the spatial separation of the Early-restricted set.

Author response image 3.

Genomic-annotation comparison of newly acquired GATA2 binding at Early. Stacked-bar comparison of genomic annotations (ChIPseeker classification) for two definitions of the newly acquired GATA2 peaks at the Early erythroid stage: all peaks Gained at Basal → Early (orange; n = 384) and the strict Early-restricted subset (Gained then Lost; red; n = 178). Annotation categories shown: Promoter (≤1 kb of TSS), Intron, Distal Intergenic, and Other (Exon, 5′/3′ UTR, Downstream). Both peak sets contain substantial promoter-proximal and distal/intronic components, consistent with the two-subclass model described in Figure 5E–G of the manuscript (GATA2-only promoter-proximal peaks with GATA/RUNX motifs, and GATA2/GATA1 cobound distal peaks with composite GATA/E-box motifs). The strict subset shows a higher proportion of intronic and distal-intergenic sites and a lower proportion of promoter-proximal sites than the full Gained set; this difference will be discussed transparently in the revised Results. Motif analysis (HOMER/MEME-ChIP, planned for the full revision) will be performed on both peak sets to confirm that the GATA/RUNX and GATA/E-box subclass signatures are preserved.

(8) Knock-in mouse hematopoietic validation

A brief characterization of basic hematopoietic parameters in homozygotes (CBC, LSK/HSPC frequencies, or colony assays) would confirm the tagged allele is physiological.

Agreed; data acquired and analyzed.

We have characterized mature trilineage hematopoietic populations in whole bone marrow from wild-type, heterozygous (Gata2Het), and homozygous (Gata2Homo) Gata2-SNAP knock-in mice (n = 5 per genotype). Bone marrow cells were stained for myeloid (CD11b⁺ Gr1⁺), lymphoid (CD3⁺/CD4⁺/CD8⁺/B220⁺/CD19⁺), and erythroid (Ter119⁺) markers and analyzed by flow cytometry. Lineage frequencies are shown as percentages of live bone marrow cells in a new Figure Supplement in the revised manuscript.

For myeloid and erythroid populations, omnibus one-way ANOVA detected no significant differences across genotypes (Myeloid: F(2,12) = 2.616, P = 0.1140; Erythroid: F(2,12) = 0.4943, P = 0.6219). Dunnett’s multiple-comparisons test against the WT control did not detect significant pairwise differences for either knock-in genotype (Myeloid: WT vs Het P = 0.1351, WT vs Homo P = 0.9926; Erythroid: WT vs Het P = 0.7017, WT vs Homo P = 0.9602).

For the lymphoid compartment, although the omnibus ANOVA reached significance (F(2,12) = 6.690, P = 0.0112), no pairwise comparison against WT remained significant after multiplecomparisons correction (Dunnett’s adjusted P values: WT vs Het = 0.1217; WT vs Homo = 0.2078). We therefore interpret this result conservatively. Brown-Forsythe and Bartlett’s tests showed no significant differences in variance across genotypes (P = 0.1423 and P = 0.0908), so the result is not attributable to unequal variances. We do not interpret these data as indicating an unambiguous lymphoid phenotype in either heterozygous or homozygous Gata2-SNAP mice; this interpretation is consistent with the broader pattern across all three lineages, in which no pairwise comparison against WT survives multiple-comparisons correction. We will note in the figure legend and in the Results text that more granular HSPC-compartment analysis (LSK, MPP, lineage-restricted progenitor frequencies) and a complete blood count (CBC) remain valuable directions for future characterization of this resource and will be considered for the full revision if specifically requested.

Author response image 4.

Bone marrow trilineage frequencies in Gata2-SNAP knock-in mice. Bone marrow was harvested from the femurs and tibias of wild-type (WT), heterozygous (Gata2Het), and homozygous (Gata2Homo) Gata2-SNAP knock-in mice (n = 5 per genotype; mixed sex; 12–14 weeks). After ACK lysis, cells were stained for myeloid (CD11b⁺ Gr1⁺), lymphoid (CD3⁺/CD4⁺/CD8⁺/B220⁺/CD19⁺), and erythroid (Ter119⁺) markers and analyzed by flow cytometry. Each dot represents one mouse, and horizontal bars indicate genotype means. Statistical results: Myeloid: ANOVA F(2,12) = 2.616, P = 0.1140; Dunnett’s adjusted P values WT vs Het = 0.1351, WT vs Homo = 0.9926. Lymphoid: ANOVA F(2,12) = 6.690, P = 0.0112 (omnibus); Dunnett’s adjusted P values WT vs Het = 0.1217, WT vs Homo = 0.2078. Erythroid: ANOVA F(2,12) = 0.4943, P = 0.6219; Dunnett’s adjusted P values WT vs Het = 0.7017, WT vs Homo = 0.9602. Brown-Forsythe and Bartlett’s tests for unequal variance were non-significant in all three lineages. Although the lymphoid omnibus ANOVA reached nominal significance, no pairwise comparison with WT remained significant after multiple-comparison correction; we therefore interpret this result conservatively (see response to R3 point 8).

Summary

We thank the editors and the three reviewers for the constructive and detailed assessment. The planned revisions consist of:

- Four new experiments [planned] (HaloTag/SNAP labeling efficiency and absolute molecule counts via U2OS reference standards; H2B-HaloTag photobleaching reference; percell quantification of total endogenous GATA2 in flow-sorted primary Gata2-SNAP populations via saturating SNAP-tag labeling, benchmarked against a SNAP-RPB1/U2OS reference standard; single-molecule tracking of GATA2 N-terminal, C-terminal, and double zinc-finger deletion mutants in the engineered cell systems as a binding-deficient functional control).

- Six analyses of existing data (GRID multi-state fitting [planned]; per-cell bleach-rate distributions and photobleach-corrected residence times [planned]; tracking-parameter sensitivity [planned]; nuclear-area normalization and total-displacement controls [planned]; normalized fold-change CUT&Tag analysis [completed; motif cross-validation planned], presented in Author response images 1–3; distribution-based single-cell statistics [planned]).

- One previously-acquired dataset [completed] (trilineage hematopoietic flow cytometry of homozygous Gata2-SNAP knock-in mice; presented in Author response image 4 with full statistical detail).

- Substantial revisions to text and figures [planned] to address statistical reporting, methodological description, mechanistic framing of cross-system differences, and refinement of the Figure 6 schematic.

With respect to the requested binding-deficient single-molecule control, we will attempt to address this directly using sequence-validated lentiviral constructs in hand encoding GATA2 mutants lacking the C-terminal zinc finger, the N-terminal zinc finger, or both. These mutant analyses will be complemented by GRID multi-state analysis and H2B-HaloTag controls, providing converging lines of validation for the two-state kinetic framework. We note that an analogous mutant cannot be examined in the physiological context of the Gata2-SNAP knock-in mouse, and we will frame the cell-line mutant analyses accordingly.

We believe these revisions directly address the editors’ specific guidance regarding labeling efficiency and methodological clarification. We thank the editors and reviewers for their time and look forward to submitting the revised manuscript.

References cited in this response:

References listed below are cited in this provisional response in support of the planned analyses and methodology.

Cattoglio, C., Pustova, I., Walther, N., Ho, J. J., Hantsche-Grininger, M., Inouye, C. J., Hossain, M. J., Dailey, G. M., Ellenberg, J., Darzacq, X., Tjian, R., & Hansen, A. S. (2019). Determining cellular CTCF and cohesin abundances to constrain 3D genome models. eLife, 8, e40164. https://doi.org/10.7554/eLife.40164

Gebhardt, J. C. M., Suter, D. M., Roy, R., Zhao, Z. W., Chapman, A. R., Basu, S., Maniatis, T., & Xie, X. S. (2013). Single-molecule imaging of transcription factor binding to DNA in live mammalian cells. Nature Methods, 10(5), 421–426. https://doi.org/10.1038/nmeth.2411

Hansen, A. S., Pustova, I., Cattoglio, C., Tjian, R., & Darzacq, X. (2017). CTCF and cohesin regulate chromatin loop stability with distinct dynamics. eLife, 6, e25776. https://doi.org/10.7554/eLife.25776

Haque, N., & Coleman, R. A. (2025). Dynamic transcription pre-initiation complex assembly governs initiation efficiency. bioRxiv. https://doi.org/10.1101/2025.05.07.652662

Heinz, S., Benner, C., Spann, N., Bertolino, E., Lin, Y. C., Laslo, P., Cheng, J. X., Murre, C., Singh, H., & Glass, C. K. (2010). Simple combinations of lineage-determining transcription factors prime cis-regulatory elements required for macrophage and B cell identities. Molecular Cell, 38(4), 576–589. https://doi.org/10.1016/j.molcel.2010.05.004

Kaya-Okur, H. S., Wu, S. J., Codomo, C. A., Pledger, E. S., Bryson, T. D., Henikoff, J. G., Ahmad, K., & Henikoff, S. (2019). CUT&Tag for efficient epigenomic profiling of small samples and single cells. Nature Communications, 10(1), 1930. https://doi.org/10.1038/s41467-019-09982-5

Kenworthy, C. A., Haque, N., Liou, S.-H., Chandris, P., Wong, V., Dziuba, P., Lavis, L. D., Liu, W.-L., Singer, R. H., & Coleman, R. A. (2022). Bromodomains regulate dynamic targeting of the PBAF chromatin-remodeling complex to chromatin hubs. Biophysical Journal, 121(9), 1738–1752. https://doi.org/10.1016/j.bpj.2022.03.027

Ling, Y. H., Liang, C., Wang, S., & Wu, C. (2026). Live-cell single-molecule dynamics of eukaryotic RNA polymerase machineries. Science, 391, eads0960. https://doi.org/10.1126/science.ads0960

Liu, Z., Legant, W. R., Chen, B.-C., Li, L., Grimm, J. B., Lavis, L. D., Betzig, E., & Tjian, R. (2014). 3D imaging of Sox2 enhancer clusters in embryonic stem cells. eLife, 3, e04236. https://doi.org/10.7554/eLife.04236

Loeffler, D., Wang, W., Hopf, A., Hilsenbeck, O., Bourgine, P. E., Rudolf, F., Martin, I., & Schroeder, T. (2018). Mouse and human HSPC immobilization in liquid culture by CD43- or CD44-antibody coating. Blood, 131(13), 1425–1429. https://doi.org/10.1182/blood-2017-07-794131

Love, M. I., Huber, W., & Anders, S. (2014). Moderated estimation of fold change and dispersion for RNAseq data with DESeq2. Genome Biology, 15(12), 550. https://doi.org/10.1186/s13059-014-0550-8

Machanick, P., & Bailey, T. L. (2011). MEME-ChIP: motif analysis of large DNA datasets. Bioinformatics, 27(12), 1696–1697. https://doi.org/10.1093/bioinformatics/btr189

Normanno, D., Boudarène, L., Dugast-Darzacq, C., Chen, J., Richter, C., Proux, F., Bénichou, O., Voituriez, R., Darzacq, X., & Dahan, M. (2015). Probing the target search of DNA-binding proteins in mammalian cells using TetR as model searcher. Nature Communications, 6, 7357. https://doi.org/10.1038/ncomms8357

Palii, C. G., Cheng, Q., Gillespie, M. A., Shannon, P., Mazurczyk, M., Napolitani, G., Price, N. D., Ranish, J. A., Morrissey, E., Higgs, D. R., & Brand, M. (2019). Single-cell proteomics reveal that quantitative changes in co-expressed lineage-specific transcription factors determine cell fate. Cell Stem Cell, 24(5), 812–825.e5. https://doi.org/10.1016/j.stem.2019.02.016

Sergé, A., Bertaux, N., Rigneault, H., & Marguet, D. (2008). Dynamic multiple-target tracing to probe spatiotemporal cartography of cell membranes. Nature Methods, 5(8), 687–694. https://doi.org/10.1038/nmeth.1233

Stark, R., & Brown, G. D. (2011). DiffBind: Differential binding analysis of ChIP-Seq peak data. Bioconductor. http://bioconductor.org/packages/release/bioc/html/DiffBind.html

Taylor, S. J., Stauber, J., Bohorquez, O., Tatsumi, G., Kumari, R., Chakraborty, J., Bartholdy, B. A., Schwenger, E., Sundaravel, S., Farahat, A. A., Dutta, A., Koche, R. P., Steidl, U., & Wheat, J. C. (2024). Pharmacological restriction of genomic binding sites redirects PU.1 pioneer transcription factor activity. Nature Genetics, 56(10), 2213–2227. https://doi.org/10.1038/s41588-024-01911-7

Wheat, J. C., Salsman, J., Reekie, I., Mathhwala, A., Black, K. L., Tiedt, R., Shroff, H., & Steidl, U. (2020). Single-molecule imaging of transcription dynamics in somatic stem cells. Nature, 583(7816), 431– 436. https://doi.org/10.1038/s41586-020-2432-4

Author response:

Public Reviews:

Reviewer #1 (Public review):

This manuscript is very interesting and timely. By introducing the critical effects of desolvation barriers and solvent (water)-separated minima into the implicit-solvent potentials (of mean force, PMFs) for coarse-grained molecular dynamics simulations of biomolecular liquid-liquid phase separation (LLPS), this work fills a gap that should be apparent to researchers of protein folding in the past couple of decades but has so far escaped deserved attention such that these basic features of aqueous solvation have seldom, though not never, been invoked in recent studies of biomolecular condensates. Although the present paper deals almost exclusively with homopolymers, this work can be a foundation for the future development of a new, more physical coarse-grained interaction scheme for simulating amino acid sequence-dependent effects, which I presume is the authors' ongoing or next endeavor. The results presented in this manuscript are highly valuable.

We thank the reviewer for all the insightful comments.

However, there is room for improvement in the authors' description of (i) the broader impact of effects of desolvation barrier and solvent-separated minimum in the thermodynamics of biomolecular condensates, especially with regard to the ramifications on hydrostatic pressure-dependent effects; (ii) the physical implication of using a 20-parameter hydropathy scale rather than a 210-parameter pairwise amino acid interaction scheme; and (iii) temperature-dependent effects, including the authors' discussion of "enthalpic" and "entropic" contributions. In all these aspects, the authors' discussion should be put in a more comprehensive context of the existing literature. At a few other places, the description of the methods and results should be clarified as well. Accordingly, the authors should revise the manuscript to address the following items thoroughly within the revised manuscript (not merely in the response letter) with the additional references mentioned below included in the revised discussion:

(1) In several places, e.g., on line 77 (p.2), the authors appear to suggest that "implicit-solvent representation" is the origin of the deficiency in commonly utilized coarse-grained potentials that this study is aiming to rectify. But desolvation barriers and solvent-separated minima are also features of implicit-solvent representations; they are just features that should be incorporated in more accurate implicit-solvent potentials. This point is stated quite clearly and accurately in the Abstract (p.1) but not consistently in the rest of the text. The authors should check the entire text carefully to ensure that a coherent, accurate perspective is presented.

We thank the reviewer for the insightful comment and suggestion. In this work, rather than departing from the implicit‑solvent modeling framework, our intention is to incorporate the desolvation effect within the implicit solvent model framework. In the revised manuscript, we will revise the text to ensure this point is presented clearly and consistently throughout the paper.

(2) In the discussion of the importance of desolvation barriers and solvent-separated minima in the Introduction (pp.1-3), connections should be drawn to recent works that utilize these PMF features to rationalize hydrostatic pressure (P)-modulated effects on biomolecular LLPS, including the P-dependent reentrant phase separation of alpha elastin; see Cinar et al. (2019) Chem Eur J 25:13049 (https://chemistry-europe.onlinelibrary.wiley.com/doi/full/10.1002/chem.201902210) and references therein, especially discussions around Figures 10, 11 & 13 in this reference.

We thank the reviewer for bringing these references to our attention. The hydrostatic pressure modulated effects on LLPS provide important context for understanding the physical significance of desolvation barriers and solvent‑separated minima. In the revised manuscript, we will expand the literature discussion by incorporating previous studies on pressure‑modulated phase separation.

(3) In the lower panels of Figures 2D, E (p.5), what do the differently colored small circles in the double-minimum free energy profiles represent? Does the color shading have the same meaning as that in the upper panels? If so, what do the positions of the circles on the free energy profile represent? The authors should clarify this.

We thank the reviewer for the suggestion to improve the clarity of the figure. In the lower panels of Figures 2D and 2E, the colored dots were intended solely as a qualitative illustration of the populations of residue‑pair configurations along the effective energy surface. Their colors are not related to the color scale used in the phase diagrams shown in the upper panels. We will modify the color scheme to improve clarity.

(4) The discussion regarding entropy and enthalpy around Figure 2 is quite confusing as it stands. What do the authors mean exactly by the association of entropy or enthalpy with the desolvation barrier of the solvent-separated minimum? Are they referring to conformational entropy?

We apologize for the confusion. When the desolvation barrier is high, configurations with inter‑residue distances corresponding to the barrier region become difficult to access, thereby reducing the conformational entropy of the condensed phase. This interpretation is supported by Figure 2—figure supplement 1C, where increasing the desolvation barrier decreases the population in the barrier region of the radial distribution function, indicating that fewer residue‑pair configurations are sampled there. In contrast, increasing the depth of the solvent‑separated minimum makes the condensed phase more energetically favorable. In the revised manuscript, we will incorporate this discussion to improve clarity.

(5) Do the authors assume that the PMF (effective implicit-solvent potential) is a purely enthalpic term? It appears to be the authors' assumption. If so, the assumption has to be stated clearly in their discussion of "entropy" vs "enthalpy" around Figure 2.

We thank the reviewer for highlighting this important point. In this work, the PMF profile is constructed from atomistic simulation results, and thus both entropic and enthalpic contributions shape the overall PMF. In the revised manuscript, we will clarify that the PMF represents a free‑energy profile along the intermolecular distance and therefore incorporates enthalpic and entropic contributions from the solute, solvent, and configurational degrees of freedom.

(6) Closely related to points 3-5 above, it should be stated clearly that the "temperature" used in the authors' simulations does not represent experimental temperature if the authors are using purely enthalpic effective potentials because PMFs are in fact temperature-dependent. This clarification is necessary to avoid misunderstanding. In this regard, it should be noted that temperature-dependent effective interactions have been used for modeling biomolecular condensates in analytical theory (Lin, Song, Forman-Kay & Chan, J Mol Liq 2017, already in the citation list) as well as in coarse-grained molecular dynamics simulations [Dignon et al. (2019) ACS Cent Sci 5:821-830 (https://pubs.acs.org/doi/10.1021/acscentsci.9b00102); Chakravarti & Joseph (2025) Protein Sci 34:e70284 (https://onlinelibrary.wiley.com/doi/10.1002/pro.70284)]. The latter two studies, not cited currently, are particularly relevant and thus should be cited because the authors may wish to incorporate temperature-dependent features in their ongoing or future effort in constructing a more comprehensive coarse-grained interaction scheme for biomolecular LLPS simulation.

We thank the reviewer for raising this important point. We agree that PMFs and the corresponding effective interactions should be temperature dependent, and therefore the simulation temperature in our current temperature-independent CG potential cannot be interpreted as a fully quantitative experimental temperature. In the revised manuscript, we will clarify the above point. We will also expand the discussion to include previous studies that introduced temperature-dependent effective interactions in analytical theories and coarse-grained simulations of biomolecular condensates.

(7) In tackling "entropy" vs "enthalpy", it should be noted that the temperature dependence of the effective interactions entails an entropic contribution (which is itself temperature dependent) in addition to conformational entropy. As for the effective potential with desolvation barrier and solvent-separated minimum, it should be noted that the decomposition into entropic and enthalpic contributions at the direct contact, desolvation barrier, and solvent-separated minimum can be dramatically different, see, e.g., MaCallum et al. (2007) PNAS 104:6206-6210 (https://www.pnas.org/doi/full/10.1073/pnas.0605859104) and references therein.

We agree that a temperature‑dependent PMF includes entropic contributions beyond the configurational entropy discussed around Figure 2. In the present manuscript, our discussion of entropy in that context refers specifically to the reduced accessible configurational space of residue‑pair states in the coarse‑grained ensemble, rather than to a full thermodynamic decomposition of the PMF. In the revised manuscript, we will make this distinction explicit. We will also note that the direct‑contact minimum, desolvation barrier, and solvent‑separated minimum may each have distinct enthalpic and entropic components, and that resolving these components would require additional temperature‑dependent PMF calculations. We will discuss this as a limitation of the current model and as a direction for future parameterization.

(8) P.7, line 340: The proportionality relation follows directly from the standard Flory-Huggins result T_c = T chi(T)/chi_c, thus the proportionality constant is exactly 1/chi_c. Is this the standard relation that the authors are invoking here? The authors should clarify this.

We thank the reviewer for pointing this out. Yes, our argument uses the condition that chi_c is fixed at the critical point for a given chain length. We will revise the text to explicitly state this relation and add the missing intermediate step, so that the proportionality used in the manuscript is clearer.

(9) The study on dynamic consequences on pp.8-11 is interesting, but clarifications are necessary:

(i) The vertical schematic in Figure 4A should be explained in detail in its entirety. As it stands, no explanation is provided either in the figure caption or in the text. In particular, what does "elasticity driven" refer to?

(ii) The top snapshot in Figure 4A is labeled t_sim = 0 ns. Does it mean that the snapshot shown is the only chain configuration that the authors used to start the simulation, and that the snapshot does NOT represent the result of any time evolution, no matter how short the duration is? However, if that is the case, why is this snapshot identified with spinodal decomposition if it is not the product of a time evolution from a more homogeneous configuration?

(iii) Related to (ii) - do the rectangular boxes shown represent the entire simulation box or just part of the box containing the polymer chains? One would imagine that if the top snapshot represents spinodal decomposition, the simulation would have been started at a more uniform distribution a short time prior? Why is this not the case?

(iv) What precisely do the small yellow beads and black-colored springs in the zoom-in image of Figure 4E represent?

We thank the reviewer for pointing out these unclear issues in Figure 4. In the revised manuscript, we will better explain the vertical schematic in Figure 4A, including the progression from the early growth of density fluctuations, to intermediate kinetic arrest, and finally to late-stage coarsening. We will also clarify that “elasticity driven” refers to the resistance to domain deformation caused by transient inter-chain network connectivity. We will clarify that t_sim = 0 denotes the time immediately after the temperature quench from the high-temperature homogeneous state to the low-temperature two-phase region. This snapshot is the post-quench initial configuration, while spinodal decomposition refers to the subsequent amplification of density fluctuations after the quench. The displayed snapshot is one representative trajectory, not the only initial configuration used in the simulations. The quantitative kinetic analysis was averaged over multiple independent trajectories. The rectangular box represents the entire simulation box. Although the system was equilibrated at high temperature before the quench, instantaneous density fluctuations remain, so the initial configuration is not perfectly uniform. In Figure 4E, the yellow beads represent interacting residue pairs. The black springs schematically represent the transient elastic network formed by these interactions, rather than a precise structural model.

(10) In discussing dynamic effects, it is useful to draw connections to related works on the effect of chain flexibility on "aging" of condensate [Biswas & Potoyan (2024) PRX 45:9222-9245 (https://journals.aps.org/prxlife/abstract/10.1103/PRXLife.2.023011)] and characterization of viscoelasticity in simulations of biomolecular condensates [Tejedor et al. (2023) J Phys Chem B 127:4441-4459 (https://pubs.acs.org/doi/10.1021/acs.jpcb.3c01292)], as the effects of desolvation can be explored further based on these prior works.

We thank the reviewer for this helpful suggestion. In the revised Discussion, we will cite and discuss the related studies on condensate aging and viscoelasticity, including the effects of chain flexibility, sticker lifetime, desolvation, and transient network formation on condensate material properties. These works provide an important context for interpreting our dynamic results. We will clarify that desolvation may influence condensate dynamics not only by slowing local rearrangements, but also by modulating transient network connectivity, kinetic arrest, and viscoelastic relaxation.

(11) Much of the present study is based on the original HPS formulation of Dignon et al. (2018). In this regard and also in anticipation of future development of improved interaction schemes, several issues should be stated and discussed, even if briefly:

(i) The original HPS model has a basic shortcoming in accounting for the relative interaction strengths of, among others, arginine vs lysine residues [Das et al. (2020) PNAS 117:28795-28805 (https://www.pnas.org/doi/10.1073/pnas.2008122117)].

(ii) Compared to 210-parameter pairwise interaction schemes, such as KH in Dignon et al. (2018) and Joseph et al. (2021), the 20-parameter interaction scheme is likely too restrictive to account for pairwise amino acid residue interactions [Wessén et al. (2022) J Phys Chem B 45:9222-9245 (https://pubs.acs.org/doi/10.1021/acs.jpcb.2c06181)].

(iii) The height of the desolvation barrier may vary significantly for different amino acid residue pairs, see, e.g., Figure 11 of Cinar et al. (2019) mentioned above (and references therein). The authors should discuss these nuances in the revised version. They may also wish to take them into consideration in future investigations.

We thank the reviewer for highlighting these important limitations of the original HPS-based framework. We agree that a 20‑parameter hydropathy‑scale model has limitation in fully capturing residue‑pair‑specific interactions, including well‑established differences such as those between arginine and lysine. In the revised manuscript, we will explicitly discuss this limitation and cite the suggested studies on residue‑specific and pairwise interaction schemes. We also agree that desolvation barriers and solvent‑separated minima are likely to depend on amino‑acid pair identity. In the present work, we employ a simplified, residue‑independent desolvation parameterization to isolate the general thermodynamic and kinetic consequences of desolvation in coarse‑grained LLPS simulations. In the revised Discussion, we will clarify this scope and emphasize that developing residue‑pair‑specific desolvation parameters, potentially within a 210‑parameter interaction framework, is an important direction for future work.

Reviewer #2 (Public review):

Summary:

This manuscript addresses an important and timely question in the molecular simulation of biomolecular condensates. Most residue-level coarse-grained models used for IDP phase separation employ implicit solvent and represent effective interactions through relatively simple pairwise potentials. While these models have been very useful, they usually do not explicitly distinguish direct contacts from solvent-separated interactions, nor do they include an energetic barrier associated with water removal. This manuscript attempts to address that limitation by introducing desolvation-inspired terms into coarse-grained models and examining their consequences for phase behavior, chain conformations, dense-phase packing, and dynamics.

Strengths:

The central idea is physically well motivated. Using a simple homopolymer model, the authors show that increasing the desolvation barrier suppresses phase separation, whereas stabilizing solvent-separated contacts enhances phase separation. They further show that solvent-separated interactions can reduce dense-phase over-compaction, which is a meaningful result given the known challenges in obtaining both accurate single-chain dimensions and realistic dense-phase properties from the same coarse-grained model. The finding that desolvation-like terms can reshape dense-phase packing without simply rescaling the overall interaction strength is interesting and could be useful for future model development. I also found the attempt to connect conformational changes across dilute and dense phases with thermal distance from the critical point to be intriguing. The dynamic analysis, including the FRAP-like simulations and the discussion of kinetic arrest during coarsening, adds another useful dimension to the work.

We thank the reviewer for all these positive and constructive assessment and comments. We are encouraged that the reviewer found the central idea physically well motivated and recognized the value of introducing desolvation-inspired terms to distinguish direct contacts, solvent-separated interactions, and the energetic barrier associated with water removal in coarse-grained models of biomolecular condensates.

Weaknesses:

At the same time, there are several places where the manuscript would benefit from more careful framing. First, the desolvation terms are still effective coarse-grained parameters rather than a direct representation of water molecules. The language sometimes gives the impression that desolvation is being treated explicitly, whereas the model introduces desolvation-inspired effective interactions into an implicit-solvent framework.

We agree that the current wording should more clearly reflect the nature of our model. The desolvation terms introduced in this work are effective coarse-grained interaction terms rather than an explicit molecular representation of water. In the revised manuscript, we will carefully revise the language throughout the article to describe the model as incorporating desolvation-inspired effective interactions within an implicit-solvent coarse-grained framework.

Second, the conformational analysis is interesting, but the broader context of prior work on dilute-to-dense phase conformational reorganization of IDPs could be more clearly discussed. This would help clarify what is new in the present work, whether it is the conformational change itself, its dependence on desolvation terms, or the proposed scaling with distance from the critical point.

We appreciate this suggestion. In the revised manuscript, we will place the conformational analysis in the context of prior work and discuss the observed conformational changes more explicitly from the perspective of desolvation-inspired interactions. We will also clarify the assumptions behind the scaling relation between conformational change and thermal distance from the critical point.

Third, the dynamic results are potentially useful, but the manuscript should more clearly articulate what is nontrivial beyond the expected slowing of local rearrangements by an added barrier in the potential.

We thank the reviewer for the suggestion. In the revised manuscript, we will clarify which aspects of the observed dynamics can be directly expected from the added desolvation barrier and which trends arise from the combined effects of desolvation on packing density, chain mobility, kinetic arrest, and coarsening.

We again thank the editors and reviewers for their constructive comments and suggestions. We believe that the planned revisions will improve the precision of the model description, clarify the physical interpretation of the desolvation-inspired terms, expand the relevant literature context, and better define the scope and limitations of the current framework.

Author response:

We thank the Reviewers for their time and effort reviewing our manuscript, we are particularly thankful for the literature recommendations of Reviewer 1, and the analysis ideas of Reviewer 2.

We are glad that both Reviewers agree that the method we developed provides value to the field. We furthermore agree that our theoretical claims and conclusions could be supported by further analyses. Thus, we primarily plan to focus on this.

We plan to strengthen our statements by:

- Comparing our metrics to those of alternative learning processes and hypotheses

- Additional analyses, including ones using standardized learning scores, collapsed saccade likelihoods for learning-dependent and not-learning-dependent saccades, angular deviations instead of the binary update variable, and a breakdown of high-probability triplets into ones that end with a pattern element or a random one.

- Adding further information regarding saccades, trials without saccades, and saccade starting points.

Furthermore, we plan to strengthen our Methods section: some of the Reviewers’ points potentially stem from our unclear description of the ASRT task, thus, the Task & Procedure section needs deeper and clearer explanations. Lastly, we will extend the Introduction, citing the literature recommended in the reviews, which indeed could provide further depth.

Author response:

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

eLife Assessment

This study presents valuable findings on the relationship between nutrient availability and NAD/NADH levels, which in turn regulate biomass production in cancer cells. The authors provide solid evidence to support their claims, offering insight into why it is difficult to predict which nutrients limit cancer cell growth: both cell type and nutrient availability together determine the oxidative capacity that constrains the synthesis of various metabolic intermediates. The manuscript will be of interest to researchers working in cancer and cell metabolism.

We thank the eLife Editor for evaluating our manuscript and for the positive comments.

Reviewer #1 (Public review):

Summary:

This manuscript investigates how cellular NAD/NADH ratios are controlled in cancer cell lines in vitro. The authors build on previous work, which shows that serine synthesis is sensitive to NAD/NADH ratios and PHGDH expression. Here, the authors demonstrate that serine synthesis is variable across a panel of cell lines, even when controlling for expression of serine synthesis enzymes such as PHGDH. The authors show that cellular NAD/NADH ratios correlate with the ability to synthesize serine and grow in serine-deprived environments when PHGDH levels remain constant. Investigating this variability in NAD/NADH ratios, the authors find that the cells that can positively respond to serine deprivation are able to increase oxygen consumption and cellular NAD/NADH ratios. Cells that do not increase oxygen consumption in response to serine deprivation do not increase NAD/NADH ratios and cannot grow well without serine. The authors go on to show that in cells with the ability to increase oxygen consumption upon serine deprivation, PHGDH expression alone is sufficient to fully restore growth-serine; in cells that cannot increase oxygen consumption, both PHGDH expression and interventions to increase NAD/NADH ratios are required to increase growth. Thus, cells need both PHGDH and NAD/NADH increases to maximize serine synthesis in response to serine deprivation. The authors previously showed that lipid synthesis likewise requires NAD regeneration. Interestingly, one cell line that does not increase oxygen consumption in response to serine limitation tends to increase oxygen consumption in response to lipid deprivation; accordingly, depriving this cell line of lipids increases the synthesis of serine. Together, these findings show that how cells respond to nutrient deprivation is highly variable and that the response to nutrient deprivation (for example, whether or not oxygen consumption is increased) will determine how well cells tolerate depletion of nutrients with related biosynthetic constraints. This work sheds light on the complexity of cancer cell metabolism and helps to explain why it is difficult to predict which nutrients will be limiting to any cancer cell type or environment.

Strengths:

(1) The authors use multiple interventions to manipulate NAD/NADH ratios in cells.

(2) Experiments are well controlled and appropriately interpreted.

Weaknesses:

Overall the data support the conclusions of the manuscript. I have only two minor comments and suggestions:

We thank Reviewer 1 for their insightful comments, which have helped us improve the manuscript.

(1) Figure 2B/C: data are presented as relative to +serine, which shows how some cells respond to -serine, but may also be of interest to see how absolute (not relative) NAD/NADH levels correlate with serine synthesis and serine-independent proliferation. In other words, is it the dynamic increase in the ratio that is most important, or the absolute level of the ratio?

We thank Reviewer 1 for raising this point about whether it is the absolute NAD+/NADH ratio, or the change in NAD+/NADH ratio, that is important for increasing serine synthesis and allowing proliferation under serine depleted conditions. We reported relative ratios for accessibility to a general audience, but agree that this information is informative and should be presented. We assessed the NAD+/NADH ratio using an enzymatic assay, which does not directly measure absolute concentrations of NAD+ or NADH (PMID: 26232225). However, we previously confirmed the assay is in the same linear range for both NAD+ and NADH, and thus is valid for assessing the NAD+/NADH ratio. We now provide the unnormalized NAD+/NADH ratio data in Supplementary Figure 2G of the revised manuscript. This shows that the considered cells exhibit a range of NAD+/NADH ratios, and redox responsive cells do not cluster in having a higher or lower NAD+/NADH ratio.

To more formally answer Reviewer 1’s question about whether the absolute ratio or change in ratio is important for increasing serine synthesis, we measured the correlation coefficient between the unnormalized NAD+/NADH ratios and the proliferation rate of all examined cancer cells cultured with or without serine. These data are presented in Author response image 1. Of note, we find that there is a significant positive correlation between the raw values of the measured NAD+/NADH ratio and proliferation rate in both serine-replete (r = .371) and serine depleted (r = .562) conditions. However, this correlation is not strong, and when examining the cancer cells whose proliferation in serine depleted conditions cannot be fully explained by serine synthesis enzyme expression (Calu6, 8988T, A549, MIA PaCa-2, H1299, and HCT116), there is no significant correlation between the raw NAD+/NADH ratio and proliferation rate in serine depleted conditions. The association between the relative change in the NAD+/NADH ratio and proliferation rate is much stronger upon serine deprivation (r = .571), as presented in Figure 2C of the revised manuscript. This suggests that the dynamic increase in the ratio is more tightly linked to the change in serine synthesis rate and proliferation in serine depleted environments, and we discuss this point in the revised manuscript with the following text:

“Of note, whether the NAD+/NADH ratio of a cell was more or less oxidized in serine-replete conditions was not predictive of response to serine withdrawal (Supplementary Figure 2G).” (Lines 163-165)

Author response image 1.

Correlations between unnormalized NAD+/NADH ratios and cell proliferation rates between (A) all cancer cells examined (Calu6, MCF7, MDA-MB-231, A549, 8988T, MIA PaCa-2, A375, H1299, HCT116, MDA-MB-231 with PHGDH overexpression) in serine-replete conditions, (B) all cancer cells examined in serine depleted conditions, and (C) select cancer cells (labeled in gray) where serine synthesis enzyme protein expression does not fully explain proliferation in serine depleted conditions. Pearson correlation coefficient and P values were calculated by simple linear regression, *p<0.05, **p<0.01. Data shown are means of three biological replicates ± SD.

(2) Line 177-178: the authors write, "We hypothesized that the elevated NAD+/NADH ratio represented a cellular response to make the NAD+/NADH ratio more oxidized to enable serine synthesis". I recommend modest edits to avoid anthropomorphizing. It is possible that the ratio responds for reasons yet to be determined and not necessarily because the cell is deliberately trying to enable serine synthesis.

We thank Reviewer 1 for raising this point. We agree that our data do not show whether the ratio is elevated for the deliberate purpose of enabling serine synthesis and have edited the text accordingly with the following edit to that line of the revised manuscript:

“We hypothesized that a more oxidized NAD+/NADH ratio could support greater serine synthesis and thus sought to identify the processes that increase the NAD+/NADH ratio in some but not all cancer cells.” (Lines 190-192)

Reviewer #2 (Public review):

In the manuscript "Cancer cells differentially modulate mitochondrial respiration to alter redox state and enable biomass synthesis in nutrient-limited environments", Chang et al investigate how cancer cells respond to the limitation of certain environmental nutrients by regulating the cellular NAD+/NADH ratio. They focus on serine and lipid metabolism, pathways known to be controlled by the NAD+/NADH ratio, and propose that changes in mitochondrial respiration in response to deprivation of these nutrients can influence the NAD+/NADH ratio, thereby impacting biomass synthesis.

While the study is descriptive in nature and does not investigate specific molecular mechanisms that explain the crosstalk between nutrient availability and mitochondrial redox changes, the experimental component is robust, and the conclusions are well supported by the results. Some suggestions could further refine the conclusions and enhance the quality of the manuscript.

We thank Reviewer 2 for their time and for their suggestions to improve the manuscript.

Main critiques:

(1) Throughout the manuscript, the authors utilise the number of cell doublings per day as an endpoint readout of cell proliferation. It would be advisable to include a quantification of the cell number and to display the proliferation rate over time. This would provide valuable insights into the timeline of cellular responses and avoid potential confounding effects associated with the use of Sulforhodamine B dye, an indirect measure of cell proliferation based on protein content, which may be influenced by some of the interventions. Furthermore, it will help determine whether specific treatments reduce cellular doublings resulting from cell death. This concern is particularly evident in treatments with rotenone, e.g., Fig. 1G, where the increase in doublings could be attributed to cell death.

We thank the reviewer for this suggestion and agree that assessment of cell count provides additional information beyond Sulforhodamine B dye as an indirect measure of proliferation. To address this, we directly measured cell number over time using Incucyte Live-Cell imaging analysis applied to A549 and H1299 cells cultured with or without serine for 72 hours. Consistent with results using sulforhodamine B, A549 cells doubled at a rate of 0.874 per day and H1299 cells doubled at a rate of 1.034 per day in serine-replete conditions. In serine depleted conditions, A549 cells doubled at a rate of 0.205 per day while H1299 cells doubled at a rate of 0.544 per day. We have added the cell number measurements over time as well as the corresponding calculated doublings per day in Supplementary Figure 2D and Supplementary Figure 2E of the revised manuscript.

We also agree with Reviewer 2 that serine deprivation and rotenone treatment could potentially impact cell viability, which might confound phenotypes, including NAD+/NADH ratio measurements. To assess whether serine deprivation and rotenone treatment cause cell death, we measured cell viability using Sytox Green after exposing cells to these conditions for 72 hours. We find that there is indeed more cell death in cells cultured without serine at most concentrations of rotenone. However, cell death did not exceed 4% in any of the conditions tested, suggesting this is not a major contributor to the cell doubling phenotypes. These data are now presented in Supplementary Figure 1C of the revised manuscript. However, in light of Reviewer 2’s comments, along with a comment from Reviewer 3 about whether rotenone induces ROS and cellular stress responses, we have decided to remove the proliferation data involving rotenone that were in Figure 1F and 1G of the original manuscript. The rationale is that the potential confounding impacts of rotenone on viability make interpreting the proliferation data difficult. Instead, we have focused Figure 1 of the revised manuscript on the observation that there is specifically a correlation between the cell NAD+/NADH ratio and serine synthesis.

(2) The authors propose a model in which the deprivation of extracellular nutrients impacts mitochondrial respiration, which in turn increases the NAD+/NADH ratio and ultimately affects metabolic biosynthetic pathways that occur in the cytosol, such as serine biosynthesis. The mechanism by which nutrient availability is sensed and transmitted across different cellular compartments to regulate mitochondrial redox status remains unclear. This concern is particularly relevant for serine metabolism, as its synthesis occurs in the cytosol, but the authors connect it to mitochondrial respiration. Compartment-specific measurements of NAD+/NADH ratio would help to understand to what extent the redox state is affected by nutrients in the mitochondria and in the cytoplasm (see also minor critiques point 2). Moreover, the use of the genetic tool LbNox could be employed to manipulate the NAD+/NADH ratio in a compartmentspecific manner, while also avoiding the toxicity of certain compounds, such as rotenone. This set of experiments would add depth to the investigation, which might otherwise appear too descriptive.

(A) Compartment-specific measurements of NAD+/NADH ratio would help to understand to what extent the redox state is affected by nutrients in the mitochondria and in the cytoplasm

The question of how nutrient availability is sensed and transmitted across cellular compartments to impact mitochondrial respiration is important. However, rigorous assessment of compartment-specific metabolism is quite challenging, as we are not aware of tools to accurately measure redox ratios in a compartment-specific manner. Direct assessment of cofactor levels in subcellular compartments requires long isolation times and are unlikely to be accurate (PMID: 27565352). Rapid immunopurification of mitochondria has been used to estimate metabolite levels and ratios, but accurate measurements are hindered by rapid oxidation of NADH to NAD+. The use of fluorescence lifetime imaging (FLIM) to monitor NADH levels does not allow for accurate monitoring of the NAD+/NADH ratio as NAD+ cannot be visualized and NADH cannot be distinguished from NADPH. Additionally, the resolution of FLIM to interrogate compartment-specific signals is limited (PMID: 38594590). Fluorescent sensors, such as SoNar, have been used to image the NAD+/NADH ratio in compartments, though SoNar is sensitive to pH changes, which vary across compartments, and it has been argued that these sensors are more suitable for qualitative, not quantitative, changes in the NAD+/NADH ratio (PMIDs: 25955212, 29181426). It has also been argued that sensors are not amenable to measurement of mitochondrial ratios, as the predicted ratios are too reduced for the range of the sensors. Given these technical limitations, we opted to attempt a rapid subcellular fractionation (~25 second process to separate cytoplasm and mitochondria) followed by enzyme-based measurements of the NAD+/NADH ratio (PMID: 36883551), acknowledging the limitations of this approach. We find that across both A549 and H1299 cells, the mitochondrial NAD+/NADH ratio is lower than the cytosolic NAD+/NADH ratio, as expected. Using this approach, we find that in A549 cells, serine depletion leads to a decreased cytosolic NAD+/NADH ratio compared to serine-replete conditions while having no impact on the mitochondrial NAD+/NADH ratio. On the other hand, serine depletion leads to an elevated cytosolic NAD+/NADH ratio in H1299 cells while also having no impact on the mitochondrial NAD+/NADH ratio. In parallel, we used extracellular pyruvate exposure as a positive control, which should support cytosolic NAD+ regeneration, and rotenone as a negative control, which should suppress mitochondrial NAD+ regeneration. We show that pyruvate led to an elevated cytosolic NAD+/NADH ratio whereas rotenone treatment led to a decreased cytosolic NAD+/NADH ratio. Despite rotenone inhibiting complex I of the electron transport chain, we did not observe a change in the mitochondrial NAD+/NADH ratio (Author response image 2). This likely indicates that this assay is not sensitive enough to detect changes in mitochondrial NAD+/NADH, and we opted not to include these data in the revised manuscript given the limitations of the approach.

Author response image 2.

Rapid subcellular fractionation to examine compartment-specific NAD+/NADH ratios. (A) Cytosolic and mitochondrial NAD+/NADH ratios of A549 cells grown with or without serine for 24 hours, n=3. (B) Cytosolic and mitochondrial NAD+/NADH ratios of H1299 cells grown with or without serine for 24 hours, n=3. (C) Cytosolic and mitochondrial NAD+/NADH ratios of H1299 cells treated with either 1 mM pyruvate or 50 nM rotenone for 24 hours, n=3. P-values were calculated using a Student’s t-test, *p<0.05, **p<0.01. Data shown are means ± SD.

We nevertheless draw the following conclusions from these data:

(1) Changes to mitochondrial NAD+/NADH either do not occur or are not captured with this approach. Even rotenone treatment, which inhibits complex I and might be expected to change mitochondrial redox state, does not change the measured mitochondrial NAD+/NADH ratio.

(2) The whole cell NAD+/NADH ratio most likely reflects changes in the cytosolic NAD+/NADH ratio. While observing no impact on the mitochondrial NAD+/NADH ratio after rotenone treatment, we still find the cytosolic NAD+/NADH ratio is decreased. Moreover, both pyruvate and serine depletion led to an elevated cytosolic NAD+/NADH ratio in H1299 cells, which we observe at the whole cell level.

(3) H1299 cells depleted of serine elevate the cytosolic NAD+/NADH ratio, while rotenone treatment decreased the cytosolic NAD+/NADH ratio despite changes in mitochondrial respiration. This suggests that redox shuttles, such as the malate aspartate shuttle, play a role in communicating changes in mitochondrial redox dynamics to the cytoplasm. We test this hypothesis as described in response to Reviewer 2, point B, below.

(B) The mechanism by which nutrient availability is sensed and transmitted across different cellular compartments to regulate mitochondrial redox status remains unclear

Multiple known shuttles are involved in exchanging redox equivalents between the mitochondria and the cytosol. It is likely that multiple shuttles are involved, or could be involved in the right context, but one major shuttle is the malate aspartate shuttle (MAS), and the MAS has been shown previously to support de novo serine synthesis (PMID: 37647199). Thus, we hypothesized that the MAS is involved in the response involving elevated mitochondrial respiration in H1299 cells to increase the whole cell NAD+/NADH ratio upon serine deprivation. To test this, we used CRISPR/Cas9 to generate H1299 cells lacking MAS components GOT1, MDH1, or GOT2 and measured the cell NAD+/NADH ratio. We did not knock out MDH2 given its integral role in the TCA cycle. We find that when MDH1 and GOT2 are knocked-out, H1299 cells no longer exhibit elevated whole cell NAD+/NADH ratios upon serine deprivation. Consistently, removing MDH1 and GOT2 also blunted the increase in oxygen consumption as well as the increase in serine synthesis upon serine deprivation. This suggests that MDH1 and GOT2 activity though the MAS support the process by which mitochondrial NAD+ regeneration is transmitted to the cytoplasm to support serine synthesis. We have added these data as Supplementary Figure 7 in the revised manuscript.

(C) Moreover, the use of the genetic tool LbNox could be employed to manipulate the NAD+/NADH ratio in a compartment-specific manner

We thank Reviewer 2 for the suggestion to consider whether LbNOX might be used to manipulate the NAD+/NADH ratio in a compartment-specific manner. We expressed LbNOX in both the cytoplasm and the mitochondria of A549 (serine non-responsive) cells. We predicted that if LbNOX expression, either in the cytoplasm or the mitochondria, affected the NAD+/NADH ratio, proliferation in serine depleted conditions might be improved. However, we found that expressing LbNOX in the cytoplasm or the mitochondria of A549 cells had no effect on the NAD+/NADH ratio. Thus, LbNOX expression in either compartment also did not change proliferation in serine depleted conditions. These data are consistent with the known limitations of this genetic tool. While LbNOX can increase NADH oxidation in response to some interventions like rotenone, it does not necessarily change the NAD+/NADH ratio of unperturbed cells. This was reported in the original description of LbNOX (PMID: 27124460). We confirmed that LbNOX was successfully expressed via immunoblotting, and also confirmed that LbNOX functioned by showing either cytoplasmic or mitochondrial LbNOX expression improves cell proliferation following complex I inhibition. Thus, expressing LbNOX in A549 cells is not informative for understanding compartment specific metabolism following serine deprivation. Nevertheless, as this question is likely to come up for other readers, we have included these data as Supplementary Figure 6 in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

Minor critiques:

(1) It seems clear from the authors' data that the response to serine depletion in terms of cell proliferation is not determined exclusively by PHGDH levels. It would be useful to measure the levels of the other two enzymes in the serine synthesis pathway and also to measure serine uptake under normal conditions in the different groups of cells. This information could provide some insight into the different responses of cancer cell lines to serine deprivation.

(A) It would be useful to measure the levels of the other two enzymes in the serine synthesis pathway

Reviewer 2 raises a fair point, and we agree that measuring levels of other enzymes in the serine synthesis pathway is informative. Thus, we measured the expression of phosphoserine aminotransferase 1 (PSAT1) and phosphoserine phosphatase (PSPH) across all cancer cells examined and find that, similar to PHGDH protein expression, PSAT1 and PSPH protein expression is lower in many cancer cells that are more sensitive to serine withdrawal (e.g. MCF7). However, among the cancer cells where PHGDH protein expression did not explain the response to serine withdrawal, the protein expression of PSAT1 and PSPH also did not explain how well the cells proliferate without environmental serine. These data have been included in Supplementary Figure 2B of the revised manuscript.

Of note, we measured serine synthesis enzyme expression for the six cancer cell lines whose proliferation in serine depleted conditions better correlated with a change in the NAD+/NADH ratio than it did with PHGDH expression: Calu6, 8988T, A549, MIA PaCa2, H1299, and HCT116. For these cells, we correlated proliferation upon serine depletion with PHGDH, PSAT1, and PSPH protein expression and found that interestingly, there was a significant negative correlation between PHGDH protein expression and proliferation upon serine deprivation. This was not observed for PSAT1 expression, and a statistically significant positive correlation between proliferation and PSPH protein expression was noted, though the variation in PSPH protein expression was large. We have added these correlation data to the revised manuscript as Supplementary Figure 2F.

(B) It would be useful to measure…serine uptake under normal conditions in the different groups of cells

Per the Reviewer’s request, we performed absolute quantification of serine uptake rates in serine-replete conditions for three serine “non-responder” cancer cells (Calu6, 8988T, A549) and three serine “responder” cancer cells (MIA PaCa-2, H1299, HCT116). We did not observe a notable difference in serine uptake rate and whether cells responded to serine deprivation. Additionally, with the exception of 8988T cells having a higher serine uptake rate than the other cells, there was no statistical difference in serine uptake across the cancer cells tested (Author response image 3).

Author response image 3.

Basal serine uptake rate of exponentially growing cells in serine replete conditions. Serine levels were measured using GC MS before and after 24 hours of serine depletion and normalized by area under the growth curve (PMID: 26954548). P-values were calculated using one-way ANOVA followed by a post-hoc Tukey HSD test, *p<0.05, **p<0.01

(2) The authors experimentally demonstrated that some cancer cells respond to serine depletion with an increase in mitochondrial respiration, but the molecular mechanism behind this is not addressed. There is some evidence in the literature showing that serine acts as an activator of the glycolytic enzyme PKM, which is coherent with an increased mitochondrial respiration in the absence of serine (PMID: 23064226). The authors could discuss their findings in the context of this paper. Additionally, they could provide some insights about baseline mitochondrial activity in the different cell lines. Indeed, it seems that "redox responsive cells" might have an overall increased basal OCR.

We appreciate the suggestion that pyruvate kinase M (PKM) may mediate the elevation in mitochondrial respiration in response to serine depletion. Given that serine is an allosteric activator of PKM, and PKM suppression can increase mitochondrial OCR, we discuss this possibility in the Discussion section of the revised manuscript using the following text:

“Interestingly, serine is an allosteric activator of the glycolytic enzyme pyruvate kinase, which converts phosphoenolpyruvate to pyruvate and generates ATP (Chaneton, 2012). Thus, decreased environment serine availability in addition to differences in pyruvate kinase activity may yield lower glycolytic ATP, resulting in greater mitochondrial respiration in serine redox responder cancer cells.” (Lines 443-447)

Additionally, we appreciate the reviewer’s observation that redox responsive cells may have an overall increased basal respiration rate. We directly measured mitochondrial dependent oxygen consumption in the same assay to test whether redox responsive cells exhibit higher mitochondrial respiration. We find that while the redox responsive H1299 and MIA-PaCa2 cells have higher mitochondrial respiration than non-responsive cells, HCT116 cells that are also redox responsive to serine deprivation, did not exhibit higher mitochondrial respiration compared to redox non-responsive Calu6, 8988T, and A549 cells (Author response image 4). However, when comparing redox non-responders versus responders as a whole, there was a statistically significant difference in basal OCR. Together, this suggests that basal mitochondrial respiration rate in serine-replete conditions may be related in some cases to whether cancer cells elevate mitochondrial respiration and the NAD+/NADH ratio upon serine deprivation, but this cannot be the full explanation given the HCT116 cell data. We also acknowledge the reviewer’s statement that we do not understand the molecular mechanism by which respiration responds to serine deprivation and explicitly state this in the revised manuscript.

Author response image 4.

Basal Oxygen consumption rate (OCR) of cancer cells in serine-replete conditions. (A) Kinetic OCR measurements of cancer cells before and after rotenone and anti-mycin injection, n=8. Data shown are means ± SD. (B) Quantified mitochondrial OCR (removing residual OCR), n=8. Values are averages obtained over three measurements. P-values were calculated via nested ANOVA, ****p<0.001

(3) There is a discrepancy between the basal values of the OCR from the same cell lines in different experiments, i.e., Figure 3A and Supp. Figure 3C, or in different experiments, Figure 3A, Figure 5E, and Figure 6A. The authors need to comment on/clarify that. Moreover, authors are encouraged to show ECAR values to support the conclusion that lactate production is not differentially affected by serine depletion, and thus, does not contribute to the increase in the NAD+/NADH ratio.

We recognize the differences in basal OCR values across different experiments. Given experiment-to-experiment variation and the need for different cartridges for each Seahorse experiment, we have found that measured OCR values using Seahorse assays vary across experiments despite the same conditions. Additionally, while we aim to seed the same number of cells per assay, cell seeding and cell quantification after each Seahorse assay can contribute to variation. Given this variability on a per-assay basis, we performed a singular experiment across all examined cancer cell lines considered to minimize variation in oxygen sensor calibration and address the reviewer question about whether absolute differences might contribute to response. These data are shown in Author response image 4.

Regarding the reviewer’s request to present ECAR data, we note that measuring ECAR is dependent on using unbuffered media and for this reason do not routinely measure ECAR. Our concern is that removing serum from the culture conditions can impact OCR measurements, and we instead prioritized maintaining the same media composition across all sets of experiments (i.e., cell proliferation assays, NAD+/NADH assays, kinetic tracing assays, and OCR measurements). Additionally, we point out that ECAR does not directly measure lactate. We refer the Reviewer to data included in the manuscript where GC-MS was used to directly measure lactate secretion over time for cells cultured with or without serine. These data are presented as Supplementary Figure 3B in the revised manuscript.

(4) There seems to be also a discrepancy between the levels of M+2 citrate and the fraction labelled (Figure 5C versus Supplementary Figure 6C) in the H1299 cell line upon serine depletion, whereby the M+2 fraction seems unexpectedly lower in serinedeprived cells. In those conditions, H1299 cells showed an increased mitochondrial respiration, which is consistent with increased total citrate levels. This could be explained by a faster TCA cycle activity and the presence of higher-order isotopologues of citrate upon serine starvation. Is this the case? Showing the abundance of the different citrate isotopologues and their contribution to the total pool would help to interpret the results.

We thank Reviewer 2 for this thoughtful comment regarding the discrepancy between M+2 citrate produced (normalized ion counts per cell) versus fraction of the total intracellular citrate pool that is M+2 labeled in serine depleted H1299 cells. In our kinetic U-¹³C-glucose tracing experiments, where we performed isotope labeling for up to 15 minutes, we only see a greater presence of M+3 citrate from fully labeled glucose without robust changes in M+4, M+5, or M+6 citrate (Author response image 5). An elevated M+3 citrate could represent pyruvate carboxylase activity, where M+3 labeled pyruvate is converted to M+3 oxaloacetate that then reacts with unlabeled acetyl-CoA to generate M+3 citrate.

We also find that the total citrate pool in H1299 cells is elevated upon serine depletion (see Supplementary Figure 6C in the original manuscript). Thus, the fractional contribution of an isotope to the citrate pool may decrease despite an increase in the amount of the particular isotope. In the original manuscript, we included data from kinetic U-¹³C-glutamine tracing in H1299 cells cultured with or without serine (Supplementary Figure 6I,J of the original manuscript). We find that H1299 cells depleted of serine exhibit greater M+4 citrate (via oxidative decarboxylation) and greater M+5 citrate (via reductive carboxylation) compared to serine-replete H1299 cells. Thus, one other potential explanation for why M+2 citrate from kinetic U-¹³C-glucose tracing represents a lower fraction of the total citrate pool in serine depleted H1299 cells is because there is a larger contribution from glutamine to the citrate pool. While there was no difference in the fraction of the citrate pool that consists of M+4 citrate, there was a greater fraction of the citrate pool labeled by M+5 citrate upon kinetic U-¹³C-glutamine tracing in serine depleted H1299 cells (see Author response image 6A, B). There was also a greater fraction of the citrate pool from M+6 citrate upon kinetic U-³C-glutamine tracing in serine depleted H1299 cells (Author response image 6C). This would require M+3 pyruvate labeling from glutamine, which may be due to malic enzyme, which converts M+4 malate to M+3 pyruvate. M+3 pyruvate may also be formed by PEPCK, which could convert M+4 oxaloacetate to M+3 phosphoenolpyruvate, leading to M+3 pyruvate. While understanding the source of M+6 citrate from glutamine is out of the scope of this study, it may highlight an interesting metabolic shift in H1299 cells depleted of serine that could elevate the total intracellular citrate pool.

Author response image 5.

Citrate isotopologues (A. M+3; B. M+4; C. M+5; D. M+6) from kinetic U-¹³C-glucose tracing in H1299 cells depleted of serine for 24 hours. For all measurements, citrate values were normalized to internal norvaline standard and cell number for each condition, n=3. Data shown are means ± SD.

Author response image 6.

Fraction of the citrate pool labeled by U-¹³C-glutamine in H1299 cells depleted of serine for 24 hours. (A) Fraction of the total citrate pool that is M+4 citrate (formed via oxidative decarboxylation), n=3. (B) Fraction of the total citrate pool that is M+5 citrate (formed via reductive carboxylation), n=3. (C) Fraction of the total citrate pool that is M+6 citrate, n=3. Data shown are means ± SD.

(5) The lipid depletion part of the paper seems to be somewhat tangential. The effect of lipid depletion on the NAD+/NADH ratio in A549 cells is modest, and the effects of dual serine and lipid depletion on OCR and NAD+/NADH ratio are not consistent. Moreover, if the authors want to show that these different nutritional environments affect lipid synthesis, apart from glucose incorporation into citrate, they would need to show actual carbon incorporation into palmitate, probably at longer time points.

We apologize for the lack of clarity for how mitochondrial respiration and the NAD+/NADH ratio play a role in governing glucose oxidation to citrate. To better highlight our logic and rationale for investigating alterations in NAD+/NADH homeostasis and citrate synthesis under lipid depletion, we have added the following text to the revised manuscript:

“Oxidative biosynthetic reactions other than serine synthesis can also be constrained by the NAD+/NADH ratio. For example, cancer cells deprived of environmental lipids increase oxidative citrate production, and we have previously found that citrate synthesis, either through glucose oxidation or glutamine oxidation, is limited by NAD+ availability (Li, 2022) (Figure 5A, Supplementary Figure 8A). Thus, we sought to uncover whether the increase in the cell NAD+/NADH ratio by mitochondrial respiration in response to serine withdrawal specifically supports greater serine synthesis or also leads to greater oxidative citrate production.” (Lines 307-313)

While we have previously shown that alterations to the NAD+/NADH ratio can modify both citrate production and palmitate synthesis under lipid depleted conditions (PMID: 35739397), we agree with Reviewer 2 that no conclusion can be made about lipid synthesis without direct measurements and have revised the manuscript accordingly.

(6) In Figure 6C-6F, showing the results of the controls (+serine +lipids) will help to clarify the extent to which serine and citrate synthesis rates are affected by the different interventions.

We thank the reviewer for the comment. Because we specifically asked how dual serine and lipid starvation impacted either serine or citrate synthesis compared to singular nutrient deprivation alone, we performed the experiments focusing on these conditions. We felt that conducting an experiment that specifically targeted our question would be make the findings more accessible as we had compared the +serine +lipid conditions to either serine or lipid depletion alone earlier in our manuscript (Figure 2D and Figure 5G,H of the revised manuscript).

Reviewer #3 (Public review):

Summary:

The manuscript by Chang and colleagues provides new insights into how cancer cells adapt their metabolism under nutrient-deprived conditions. They find cells respond differentially to serine and lipid deprivation via oxidising the cell redox state, which enables biomass synthesis and cell proliferation. They identified mitochondrial respiration as the major mechanism that dictates the endogenous NAD+/NADH ratio. By incorporating a dual stress paradigm, serine and lipid deprivation, the study further suggests that the NAD+/NADH ratio can serve as a link to orchestrate the complex interplay between multiple nutrient changes in the tumour microenvironment.

Strengths:

A novel aspect of this study is the idea that cancer cells are not uniformly passive victims of nutrient limitation; some can actively invoke endogenous NAD+ regeneration to combat nutrient stress. The conclusion is well-supported by comparing multiple cell lines from different tissues and genetic backgrounds, which improves generalizability. While most of the smaller conclusions align with common reasoning and expectations, the step-by-step deduction that leads to a novel 'big picture' is commendable. Another notable strength is the integration of dual stress (lipid and serine deprivation), which better mimics the complex tumor microenvironment with multiple nutrient fluctuations, raising the translational potential of these findings. The observation that lipid-deprived cells can stimulate serine synthesis and support proliferation in a subset of cancer cell lines offers a novel perspective on metabolic plasticity under starvation conditions.

We thank Reviewer 3 for their time and for their comments to help us improve the manuscript. We also thank them for highlighting the strengths and significance of our findings.

Weaknesses:

(1) Although the authors derive a novel and valuable overarching concept, the presentation of this "big picture" is not clearly articulated, making it less accessible to readers outside the immediate field. It would greatly enhance the manuscript to include a clearer summary of the overarching model and its implications. Additionally, discussing the potential clinical significance and applications of the findings would increase the relevance and broader impact of the work. Finally, the manuscript's clarity and credibility are undermined by inconsistent figure labeling and the lack of statistical analysis, particularly for the Western blot data.

(A) It would greatly enhance the manuscript to include a clearer summary of the overarching model and its implications. Additionally, discussing the potential clinical significance and applications of the findings would increase the relevance and broader impact of the work.

We appreciate Reviewer 3’s suggestion to help clarify the findings of this study. To better articulate our overarching model, we have added the following text to the end of the Results section of the revised manuscript

“Taken together, we propose a model where environmental nutrient availability can impact mitochondrial respiration based on the specific cancer. Because mitochondrial respiration is a major pathway that regenerates NAD⁺, changes to mitochondrial respiration can alter the cell NAD+/NADH ratio, influencing the activity of major NAD⁺-requiring metabolic reactions such as serine synthesis and citrate synthesis that can be important for proliferation. We further propose that changes to the cell NAD+/NADH ratio can impact all oxidative biosynthetic reactions if the enzyme machinery is present, but that specificity for how the cell NAD+/NADH ratio changes is dependent on both cell-intrinsic factors and cellextrinsic factors (Figure 7)." (Lines 396-404)

Additionally, a new model figure was added as Figure 7 in the revised manuscript, which may help with understanding for a general audience.

To better highlight the potential clinical significance of these findings, we have added the following at the end of the Discussion section of the revised manuscript:

“Better understanding the mechanisms cells use to alter respiration and adjust the NAD+/NADH ratio in response to available nutrients could inform the complex interplay between cell-intrinsic and cell-extrinsic factors that determine cancer metabolic dependencies. This is particularly important to consider when targeting metabolism for cancer treatment. Many newer therapies targeting metabolism have not been successful in part because of metabolic plasticity to nutrient shifts (Amoedo, 2017; Fendt, 2020; Xiao, 2023). Co-targeting mitochondrial function limits metabolic adaptations and may also help predict the tissue nutrient conditions that result in pathway dependencies for specific cancers. Thus, better understanding how the cell NAD+/NADH ratio responds to nutrient levels in different cancers could improve selection of patients for cancer therapies that impact metabolism.” (Lines 483-492)

(B) “…the manuscript's clarity and credibility are undermined by inconsistent figure labeling and the lack of statistical analysis, particularly for the Western blot data.”

We apologize to the reviewer for any inconsistency in data presentation. To address the comment related to inconsistent figure labeling, we ensured all figures in the revised manuscript are labeled to allow readers to recognize what cell lines are used, what conditions are tested, what parameters are measured, and how the data may or may not be normalized. To address the reviewer’s comments about lack of statistical analysis, in the revised manuscript we ensured that statistical analyses are included for data presented in each figure, when appropriate. We also include a section titled “Statistics and Reproducibility” in the Methods section. In our revised manuscript, we have ensured that the p-value threshold is consistent throughout all figures, and have removed “ns” across the manuscript for consistency as suggested by Reviewer 3 in their minor comments. We also removed any explicit p-values included in figures where the p-values were close to reaching the threshold for significance (a=0.05). We have also performed additional statistical analyses where needed, including adding the pvalues for linear regression analyses, and ensured new data added to the revised manuscript also included appropriate statistical analyses.

For western blot data, we show representative immunoblots. However, we measured PHGDH, PSAT1, and PSPH protein expression in three biological replicates across examined cancer cells and quantified the average serine synthesis protein expression from each replicate performed with error bars that denote standard deviation (see Author response image 7). We performed a nested ANOVA to examine whether there was a statistically significant difference in PHGDH, PSAT1, and PSPH protein expression between non-responder and responder cancer cells. Interestingly, as noted in our response to Reviewer 2, we find a significant negative association between PHGDH protein expression and response to serine deprivation among the six cancer cells where PHGDH protein expression did not explain proliferation upon serine depletion.

Author response image 7.

Serine synthesis enzyme protein expression in serine-replete and serine depleted cancer cells. (A) Immunoblots examining the expression of PHGDH, PSAT1, and PSPH in cancer cells as shown. HSP90 was used as a loading control. Data are from two separate biological replicates. (B) Mean levels of PHGDH, PSAT1, and PSPH normalized to loading control HSP90 across cancer cells from three separate biological replicates. Yellow denotes cancer cells that do not elevate mitochondrial respiration in response to serine depletion (non-responders). Blue denotes cancer cells that do elevate mitochondrial respiration in response to serine depletion (responders). P-values were calculated with nested ANOVA comparing non-responders and responders, **p<0.01

(2) While this study identifies changes in serine synthesis, mitochondrial respiration, PHGDH protein levels, and NAD+/NADH ratio in different cell lines, some of these relationships appear correlative rather than causally established (Figure 2; Figure 5; Figure 6). Some claims are thus overinterpreted. For example, the co-occurrence of increased NAD+/NADH ratio and citrate levels under lipid deprivation in A549 cells does not establish causality (Figure 5). Direct perturbation experiments that manipulate NAD+/NADH and assess downstream effects on citrate synthesis would substantially strengthen the conclusions.

We agree with Reviewer 3 that corresponding changes in proliferation, mitochondrial respiration, and serine synthesis are correlated to the NAD+/NADH ratio. As shown in Figure 4, we perturbed the NAD+/NADH ratio with FCCP and rotenone to measure downstream effects on serine synthesis. We also agree with the reviewer that doing similar experiments in the lipid depletion condition would highlight the relationship between the NAD+/NADH ratio and citrate synthesis. However, we point out that these experiments were already published in a manuscript from our group specifically showing that the NAD+/NADH ratio is limiting for citrate synthesis (PMID: 35739397). In that manuscript, the NAD+/NADH ratio was perturbed using electron transport chain inhibitors, including complex I inhibitors, which decreases the cell NAD+/NADH ratio. Exogenous electron acceptors were used to rescue the NAD+/NADH ratio, and under those conditions, cell proliferation, the NAD+/NADH ratio, and glucose and glutamine oxidation to citrate were measured with and without lipid depletion. We showed that decreasing the NAD+/NADH ratio decreases citrate synthesis through both glucose and glutamine oxidation and also affects palmitate synthesis. We could rescue citrate and palmitate synthesis by supplementing cells with exogenous electron acceptors. We also show that expressing cytosolic or mitochondrial NADH oxidase (LbNOX; PMID: 27124460) in mitochondrial complex I-inhibited cells rescues proliferation in lipid depleted conditions and that LbNOX expression raises oxidative citrate production at baseline. Given the extensive prior work showing the relationship between the NAD+/NADH ratio, oxidative citrate synthesis, and palmitate synthesis, efforts to repeat these same experiments for this manuscript were not warranted. We do show in the current manuscript that treating cells with AKB or FCCP, which raises the NAD+/NADH ratio, also increases glucose oxidation to citrate (Figure 5D of the original and revised manuscripts). We did this to confirm that the elevated M+2 citrate production from glucose in serine starved H1299 cells was related to an increase in the NAD+/NADH ratio as opposed to a specific response to serine depletion.

The study focuses predominantly on mitochondrial respiration as a source of NAD+ regeneration. However, it will also be interesting to check other significant pathways, such as NAD+ salvage, which have been implicated in supporting serine biosynthesis. In addition, the subcellular distribution of NAD+ may distinguish whether some cells are truly redox-unresponsive. Mitochondrial NAD+ regeneration might counteract the cytosolic NAD+ consumption, rendering a relatively stable intracellular NAD+/NADH ratio. The malate-aspartate shuttle can be an interesting aspect.

(A) The role of NAD+ salvage and serine biosynthesis

Per the reviewer’s request, we investigated whether NAD+ salvage might be involved in supporting serine synthesis. Specifically, the reviewer comments highlight an interesting question about whether NAD+ salvage may differentially contribute to serine synthesis between cancer cells that elevate mitochondrial respiration in response to serine depletion and cancer cells that do not change mitochondrial respiration in response to serine depletion. Specifically, we wondered whether cancer cells that do not elevate mitochondrial respiration in response to serine depletion depend more on NAD+ salvage to support proliferation in serine depleted conditions. To test this, we treated A549 and H1299 cells in serine depleted conditions with increasing doses of the nicotinamide phosphoribosyltransferase (NAMPT) inhibitor FK866. However, we found no statistically significant difference in sensitivity to FK866 upon serine depletion in these cells based on ANCOVA analysis (p=0.9332). Interestingly, we observe that A549 cells are more sensitive to FK866 treatment than H1299 cells in serine-replete media conditions (ANCOVA analysis, p=0.0004). This suggests that A549 cells at baseline may have greater dependence on NAD+ salvage compared to H1299 cells, though this is not specific to the response to serine depletion. We then asked whether nicotinamide mononucleotide (NMN), the product of NAMPT and the immediate precursor to NAD+ in the salvage pathway, would rescue the proliferation of A549 cells cultured without serine. We find that adding 100 µM NMN, a concentration that can impact PHGDHdriven serine synthesis (PMID: 30157431), does not change proliferation of A549 cells cultured without serine, unlike supplementing cells with AKB or FCCP, which increase NADH oxidation to NAD+. Together, these data suggest that NAD+ salvage does not play a major role in differentiating the redox response to serine deprivation between responder and non-responder cells. We have added these data as Supplementary Figure 3C,D of the revised manuscript.

(B) The role of the malate-aspartate shuttle and serine biosynthesis

The MAS has been shown to play an important role in serine synthesis (PMID: 37647199) and may facilitate elevation in mitochondrial respiration in response to serine depletion. As stated in response to Reviewer 2, measuring subcellular compartmentspecific NAD+/NADH ratios accurately is not feasible, so we utilized a functional approach to interrogate the role of compartmentalization. Specifically, we tested a role for the malate-aspartate shuttle (MAS). Using CRISPR/Cas9, we generated GOT1, MDH1, and GOT2 deleted H1299 cells. We did not knock out MDH2 given its integral role in the TCA cycle. Using the knockout lines, we measured the whole cell NAD+/NADH ratio and found that MDH1 and GOT2 KO cells no longer exhibited an elevated cell NAD+/NADH ratio upon serine depletion compared to non-targeting controls (NTC). Consistently, MDH1 and GOT2 KO cells did not elevate OCR upon serine deprivation, nor did they exhibit greater serine synthesis rates compared to NTC cells. This suggests that MDH1 and GOT2 activity support the process by which mitochondrial NAD+ regeneration provides cytosolic NAD+ to support serine synthesis. We next asked whether MAS protein expression differed between cells that elevate respiration in response to serine depletion and cells that do not. While enzyme expression is not equivalent to activity, we wondered whether MAS protein expression would be lower in cells that do not increase their mitochondrial respiration upon serine depletion. However, we observed no major difference in GOT1, GOT2, MDH1, or MDH2 protein expression across the cancer cells examined (Author response image 8). Further experimentation is needed to measure MAS activity across lines and may reveal a mechanism by which mitochondrial respiration is governed by nutrient availability, such as levels of environmental serine.

Author response image 8.

Protein expression of the malate aspartate shuttle enzymes GOT1, MDH1, GOT2, and MDH2 in cancer cells cultured without serine for 24 hours. Membranes were first probed for GOT1 or GOT2 then stripped and re-probed for MDH1 or MDH2.

(3) The authors should acknowledge the limitations of short-term isotope tracing in their experimental design. Differences in metabolic rates across cell lines can affect the kinetics of metabolite labeling, limiting the direct comparability of metabolic fluxes between them. As a result, observed changes may reflect transient adaptations rather than stable metabolic reprogramming. It is important to clarify that the study primarily captures short-term responses, and the conclusions may not extrapolate to longer-term adaptations or protein-level changes under sustained nutrient stress.

We thank the reviewer for this comment. We apologize for any confusion around experimental approaches. We agree that in the case of acute changes in nutrient availability at the start of kinetic isotope tracing, the observed changes may reflect transient adaptations. However, cells are exposed to conditions for 24 hours prior to performing kinetic tracing. This approach allows us to examine changes that occurred in response to the nutrient condition, not acute changes. Additionally, we add fresh, prewarmed treatment media at least two hours prior to commencing kinetic isotope tracing. Upon analysis of kinetic isotope tracing, we examine whether cells were at metabolic steady state by monitoring metabolite levels over the course of tracing. For example, in the kinetic glucose tracing experiments in serine depleted cells, total serine levels are relatively stable throughout the experiment, and we find that total serine levels are greater in H1299 cells after 24 hours of serine starvation. Data showing total metabolite pools over the course of tracing are shown in the Supplementary Figures (for example, see Supplementary Figure 8C-H in the revised manuscript). The period of treatment prior to the start of kinetic isotope tracing is described in the figure legends and further detailed in the “Kinetic U-¹³C-Glucose Isotope Tracing Experiments” section of the Methods in the revised manuscript. To improve clarity, we added a kinetic graph showing total serine levels over time in Supplementary Figure 2I of the revised manuscript as this can address whether synthesis rates are captured while cells are at metabolic steady state. We also discuss these considerations better in the revised manuscript with the following text:

“Importantly, we confirmed kinetic U-¹³C-glucose tracing was performed at metabolic steady state by ensuring metabolite levels were stable at each collected time point (Supplementary Figure 2I)” (Lines 178-180).

Reviewer #3 (Recommendations for the authors):

It is important to note that, in many cases, the data show only trends rather than statistically significant differences, or, if significance testing was performed, the results are not clearly labeled. For example, in Figure 1B, no p value was denoted in the figure, and the scale bar is quite high, precluding the conclusion that "AKB and rotenone dosedependently increased and decreased the cell NAD+/NADH ratio". In Figure 2E, no pvalue was shown to support the result that "H1299 cells had higher serine level than A549 cells". Inconsistencies in how significance is denoted across figures (e.g., asterisks vs. numerical values; "ns" vs. no label) make interpretation difficult. Marginal significance (e.g., p = 0.06 in Figure B) can be reported explicitly, but all figures should clearly denote whether comparisons are significant or not. Conclusions drawn from nonsignificant trends should be appropriately stated.

We thank Reviewer 3 for this important comment and for highlighting specific instances where the manuscript could be improved. Please see response to Reviewer 3, Major Comment 1B. We also agree with Reviewer 3 that it is integral to ensure that conclusions made from non-significant trends are appropriately stated. For example, we explicitly mention that there was no statistically significant difference between the serine synthesis rate of A549 cells depleted of serine versus A549 cells depleted of both serine and lipids (Line 375). As another example, we changed the phrase “Moreover lipid depletion led to a greater fraction of total serine derived from glucose in serine depleted A549 cells” to “Moreover, lipid depletion appeared to lead to a greater fraction…” (Line 376).

Western blot data supporting PHGDH expression variability across cell lines (e.g., Supplementary Figure 2B, 3E) appear to rely on single experiments. At least three biological replicates are required to substantiate claims about discordance between PHGDH levels and serine sensitivity. Supplementary Figure 4G presents overexpression validation based on a single Western blot without quantification. Including statistical validation from biological replicates would strengthen this point.

We thank Reviewer 3 for this suggestion. Western blots were repeated 3 times, although data from a representative blot is shown. Please see response to Reviewer 3, Major Comment 1B.

Certain data visualizations (e.g., Figure 2C) lack annotation indicating which data points correspond to which cell lines, limiting interpretability. All figures should include clear labels, consistent statistical notation, and complete legends. The author uses different color labels (redox-responsive (blue) and unresponsive (yellow) cell lines), which provides mechanistic clarity; however, this classification was not consistently used across the manuscript (e.g., Figures 2d and 2e). To further improve reader comprehension, consider adding conceptual schematic diagrams before each main result section to illustrate experimental logic, and a final diagram summarizing the proposed mechanism.

We apologize for any unclear data presentation. In the revised manuscript we have added greater clarity around what cell lines are used in each experiment and have added explicit labeling to specify cancer cell lines in Figure 2C of the revised manuscript. Throughout, we have ensured that any serine redox non-responder cell lines are labeled in yellow while serine redox non-responder cell lines are labeled in blue. We have also ensured that any lipid redox responder cells are labeled in green while lipid redox non-responder cells are labeled in dark purple, a change from the original manuscript. Finally, we have also added a schematic to summarize the proposed model in Figure 7 of the revised manuscript.

Although the authors provide justification for using H1299 and A549 as representative cell lines to study serine depletion, it remains unclear whether these two lines are equally suitable for investigating lipid depletion. Additional rationale or supporting data would help clarify their appropriateness for the lipid-related experiments.

We thank Reviewer 3 for this suggestion. We opted to study H1299 and A549 cells under lipid deprivation to assess their responses in relation to the response to serine deprivation. We specifically wanted to know whether these findings related to serine deprivation applied to other nutrient depleted conditions. We clarify this logic in the revised manuscript by adding the following text:

“Oxidative biosynthetic reactions other than serine synthesis can also be constrained by the NAD+/NADH ratio. For example, cancer cells deprived of environmental lipids increase oxidative citrate production, and we have previously found that citrate synthesis, either through glucose oxidation or glutamine oxidation, is limited by NAD+ availability (Li, 2022) (Figure 5A, Supplementary Figure 8A). Thus, we sought to uncover whether the increase in the cell NAD+/NADH ratio by mitochondrial respiration in response to serine withdrawal specifically supports greater serine synthesis or also leads to greater oxidative citrate production.” (Lines 307-313)

We have also included more detailed justification for focusing our studies on A549 and H1299 to study serine depletion by adding the following statements to the manuscript:

“We performed focused comparisons between A549 and H1299 cells because they exhibit differences in proliferation upon serine deprivation that are not explained by PHGDH protein expression, demonstrate differing responses of the cell NAD+/NADH ratio upon serine deprivation, and have similar basal proliferation rates.” (Lines 171-175)

The concentration of serine in replete media should be explicitly stated and justified. If the intention is to mimic physiological conditions, alignment with human plasma levels would increase translational relevance.

We agree that explicitly stating the concentration of serine in replete media is important. In the revised manuscript, we explicitly state that DMEM contains 400 uM of serine and that we use this concentration for serine-replete conditions (Line 102). While an important application of our manuscript is to better explain metabolic changes that can occur in physiologic conditions, we acknowledge that we did not test levels found in different tissues. Rather, by examining extreme conditions of high and low serine, we hoped to dissect how cells adapt to nutrient conditions, and testing the more subtle responses based on tissue serine levels will require a dedicated study.

Rotenone may elevate ROS levels and trigger cellular stress responses, potentially confounding proliferation assays. The authors should validate that concentrations used do not induce cytotoxicity or excessive oxidative stress, and ideally measure ROS levels to support interpretation.

We thank Reviewer 3 for raising this important point. We explicitly measured cell viability with the doses of rotenone used in this manuscript in cells cultured with or without serine. We find that rotenone dose-dependently increases cytotoxicity in A549 cells grown in serine-replete conditions in a statistically significant manner as calculated by simple linear regression. However, the cytotoxicity from rotenone is low (at most 4% in serine depleted conditions) and does not explain differences to rotenone sensitivity with respect to serine synthesis. These data have been added to Supplementary Figure 1C of the revised manuscript.

Evidence for lipid depletion can enhance serine synthesis in A549 cells is inadequate, for the marginal difference in NAD+/NADH ratio and slight increase of M+3 serine levels. The statement "any perturbation that increases the NAD+/NADH ratio led to both elevated serine and citrate production, regardless of what nutrient was depleted from the environment" (introduction section) should be reworded.

We thank Reviewer 3 for this suggestion. We have changed the above statement to the following:

“Lastly, we find that any perturbation that increases the NAD+/NADH ratio, including lipid deprivation, could paradoxically improve the proliferation of cells in serine depleted conditions.” (Lines 90-92).

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The authors conducted a comprehensive benchmarking and evaluation of co-folding platforms, including AlphaFold3, Boltz-2, Chai-1, and the docking algorithm Dock3.7, which employs a physics-based scoring function that incorporates van der Waals interactions, electrostatics, and ligand desolvation energies. The system of interest was the SARS-CoV-2 NSP3 macrodomain (Mac1), an increasingly popular antiviral target, and the ligand sets comprised 557 unseen ligand poses (keeping the training for these co-folding platforms in mind). Additionally, the authors investigated whether the co-folding models could distinguish true ligands from non-binding small molecules. The study is thorough, with extensive statistical support and consensus across multiple metrics (chemoinformatics for quantifying ligand similarity and efficacy). The questions that the authors aim to address are whether the co-folding models struggle with memorization, whether they can distinguish between a true and a false binder, whether they replicate experimental binding affinities and efficacy, and how they compare to the physics-based docking algorithm (Dock3.7).

We thank Reviewer 1 for this thoughtful summary of our work.

Strengths:

Overall, this is a scientifically solid paper. The work is highly detailed and well executed, featuring thorough data analysis and statistical assessment.

Weaknesses:

My main concern is that the study's aim is a bit unclear. Modern benchmarking studies comparing physics-based docking with deep learning-based co-folding approaches (e.g., AF3, Boltz-2, Chai-1, and others) are increasingly expected to go beyond aggregate performance metrics.

Indeed, we have gone into several examples of failures and successes for each of these methods. As we are not developing these methods ourselves, we also think this dataset will be a valuable contribution for improving them further.

In addition to rigorous dataset construction, transparent methodology, and appropriate statistical evaluation, high-impact benchmarks typically provide actionable guidance on when each method class is most appropriate, reflecting their distinct inductive biases and practical constraints. Failure-mode analyses that link performance differences to protein flexibility, ligand chemistry, or binding-site characteristics are particularly valuable, as they move comparisons beyond "scoreboard" assessments toward mechanistic understanding.

Right now, we do not observe meaningful trends that separate the failure modes for any individual method. This is covered in Supplementary Figures 6 and 7.

While full biological validation is not expected, qualitative interpretation grounded in physical and biological principles strengthens conclusions. Providing reproducible workflows or reference pipelines is not mandatory, but it is increasingly viewed as a best practice because it facilitates adoption and helps contextualize results for practitioners.

We note that our code is available (https://github.com/jongbin99/Cofolding/) and all structural data will be publicly accessible in the PDB alongside publication (we only held it back only for “blinding” during peer review to avoid contamination with any new deep learning methods).

Reviewer #2 (Public review):

Summary:

The manuscript by Kim et al. evaluates the performance of three modern AI-based methods in predicting complex structures and binding affinities between proteins and chemical compounds. An honest 'prospective' evaluation is achieved by studying benchmark structures and chemical compounds that did not exist in the PDB at the time the AI structure prediction models (AlphaFold3, Chai-1, Boltz-2) were trained.

Strengths:

(1) The study addresses an important question in modern computational biology and drug discovery, and establishes the strengths and limitations of the three tools in solving various computational chemistry tasks, including compound pose prediction, active-inactive discrimination, and potency ranking.

(2) The conclusions are based on examination of four separate targets and respective compound datasets, where for one of the targets, the authors also obtained numerous X-ray structures to serve as experimental answers for the binding pose prediction task.

(3) The study reports relationships between structure prediction confidence, predicted energies (DOCK3.7), and affinity predictions (Boltz-2) with the geometric accuracy of compound pose prediction as well as the experimentally measured potency.

(4) One of the key findings is the limited ability of co-folding methods to predict conformational rearrangements, which does not correlate with their ability to predict binding poses of the compounds inducing these rearrangements.

(5) The findings could serve as useful guidelines for computational chemists in selecting appropriate software and scoring schemes for each task.

We appreciate Reviewer 2’s summary of the novelty of the dataset and analysis.

Weaknesses:

While I consider this a solid study, several aspects would need to be addressed to make it really strong:

(1) DOCK3.7 docking and scoring experiments were performed using one experimental structure of Mac1, selected from dozens of structures based on a criterion that is not sufficiently well justified. For sigma2 receptor, dopamine D4 receptor, and AmpC β-lactamase, it is not clear which structures or models were selected for docking at all. It is well known that geometry predictions, scoring, and active-inactive ROC AUCs are all strongly influenced by the selected structure. It would be important to attempt Mac1 docking using all available experimental Mac1 structures, or at least against representative structures in various conformations; it would also be quite insightful to compare results to docking of the same compound sets to AF3, Boltz-2 and Chai-1 predicted structures of Mac1. Same goes for the docking studies of sigma2, D4, and AmpC β-lactamase.

In any program, a decision has to be made as to which template will be used for docking, we justified the choice in the methods:

“We used this structure because the inhibitor (Z5014193706) was the most potent molecule with a structure determined around the same time as the ligands in this dataset were tested.”

We stand by this as a reasonable assumption. Similarly, for sigma2, D4, and AmpC β-lactamase, the template was chosen in the respective papers:

a) The σ2 receptor bound to cholesterol (PDB ID: 7MFI) was used in the docking calculations.

- This structure was determined in the paper, the first structure of sigma2 and therefore a worthy template

b) The D4 receptor campaign used PDB 5WIU

- This was one of two D4 structures available and chosen because it was not bound to sodium

c) For AmpC, the campaign used the structure in the Protein Data Bank (PDB) 1L2S

- This maximizes comparisons to other docking studies that used the same receptor template.

The major goal of this study is to compare different methods under reasonable (but perhaps as the reviewer points out, not optimal) conditions, not to optimize docking score.

(2) For binding affinity predictions, as a control, authors should consider compound co-folding with an unrelated protein, or even with a pseudo-peptide that consists of a few random single amino acids - this would provide an honest baseline for such predictions.

This suggestion would be valuable for understanding the performance for these methods from the perspective of ligand specificity (a valuable, but separate, goal). Surely this will generate some number or some prediction - but what would this baseline mean and how would it be relevant for drug discovery? Therefore, we do not think this suggestion is relevant for the issues being investigated in this manuscript.

(3) ROC curves Figure 3 and elsewhere should be shown, and AUCs quantified/reported on a log or square-root scaled x-axis, to emphasize early enrichment, which is the area of practical significance for these predictions. For example, Figure 3A currently suggests that the pose prediction performance of AF3 exceeds that of Boltz-2 whereas the early enrichment is clearly better for Boltz-2.

We agree with this, and added a semi-logAUC plot for Figure 3A. For Figure 5, we also generated a semi-logAUC plot to see early ligand enrichment clearly, added as Supplementary Figure 11. We added the text:

“Considering its early enrichment performance, Boltz-2 Ligand ipTM was the strongest predictor of pose accuracy based on normalized logAUC (20.5% above random, Fig. 3a). In contrast, although Boltz-2 pIC50 showed poor overall discrimination, it overestimated its ability to enrich true positive poses at low false positive rates, despite having a weak early enrichment behavior”

(4) 'Trained set' in figures and text should probably be 'training set'? Or otherwise explain this new term the first time it is introduced.

Thank you for pointing out this for clarification. ‘Training set’ is the correct word, and we made changes appropriately across all figures and texts.

(5) Figure 1 illustrates a projection onto the first two principal components of a space that apparently had only one (scalar) metric for each compound pair (% maximum common substructure or Tanimoto coefficient); the authors need to better explain the principle behind this analysis and visualization.

This suggestion is valuable, since we often use PCA to reduce dimensionality for more complex features. For clarification, we actually have a full pairwise similarity matrix for all tested Mac1 compounds based on each of Tc and MCS%. PCA for each MCS% and Tc is a representation of each pairwise similarity matrix. We also made a change in Figure 1 caption to make this point clearer:

“projection of compounds represented by their full pairwise similarity vectors (by ECFP-4 Tc and MCS%)”

Reviewer #3 (Public review):

Summary:

This study's core conclusions are well-supported by data. It is shown that co-folding outperforms docking in known ligand pose/affinity prediction (validated by RMSD and IC₅₀ correlation), struggles with false-positive discrimination in virtual screens (lower AUC values), and is complementary to docking (non-correlated errors, distinct strengths in drug discovery stages).

Strengths:

(1) Unprecedented prospective design with 557 novel Mac1-ligand complexes ensures rigorous, independent evaluation of co-folding methods.

(2) Comprehensive comparison of 3 co-folding tools (AlphaFold3, Chai-1, Boltz-2) with DOCK3.7 across diverse targets and metrics enables nuanced performance assessment.

(3) The study clearly demonstrates complementary roles of co-folding (superior pose/affinity prediction for known ligands) and docking (better hit prioritization), and addresses deep learning memorization concerns via ligand similarity analysis.

We thank Reviewer 3 for pointing out the unprecedented and comprehensive nature of our study

Weaknesses:

(1) Limited generalization to diverse protein families (e.g., no ion channels/transporters).

We agree - we have not explored the entire proteome and these are important target classes that will surely be investigated by future studies. We focused on targets here where we had large number of X-ray crystal structures (Mac1) and affinity/inhibition measurements from docking (the other three targets).

(2) Ambiguity in the mechanism underlying co-folding's failure to predict rare conformational changes.

Again, we agree. We are not the developers of these methods. We observe that these methods do not predict conformational changes with high fidelity and this weakness is an area that co-folding methods will surely prioritize in the future.

(3) Virtual screen comparison is unbalanced (docking-prioritized hit lists bias results).

We acknowledge this in the results: “An important caveat is that the hit-lists were composed of molecules prioritized by docking in the first place, giving it an advantage on these particular sets.” and discussion: “Finally, comparing co-folding to docking based on hit-lists themselves selected by docking is arguably unfair to co-folding. Counter-balancing this is the inclusion, in each of the three hit lists, of molecules that had mediocre and poor docking scores intentionally selected to test the correlation between docking score and hit-rate. Here too, the correlation between co-folding score and likelihood to bind, what we sometimes call a “dock-response-curve” was no better than docking’s, often worse (SFig.11).”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Here are suggestions for revisions:

(1) The writing is at times obtuse and hard to follow.

This happens sometimes when multiple authors are writing together. We apologize and are happy to respond to specific areas that can be streamlined to be easier to follow.

(2) In the Results section, "A set of 557 previously unreported Mac1 ligand complexes", the authors have compared the ligand poses across different metrics such as Tc - a standard, highly effective method in chemo-informatics and MCS (maximum common substructures); these are standard metrics for quantifying the structural similarity between pairs of small molecules. This part of the analysis checks whether this is memorization; it is critical to compare the two metrics, but it is not sufficient to draw a conclusion.

Thank you for pointing out about the structural similarity of molecules co-folded to those present in the training set (resolved as Mac1 complexes and deposited in PDB before training dates). We have conducted an analysis where we do a pairwise similarity comparison for all ligands present in the PDB (regardless of the target), by both Tc and MCS, and overlay the cluster of ligands we tested (Mac1, AmpC, sigma2, D4). This should show where our tested benchmark datasets lie in the chemical space covered in the entire PDB. Each cluster (around 500 to 1300 compounds per target system) is overlaid on the cluster of all ligands deposited in PDB (over 50,000 compounds), and each cluster was relatively diverse by both Tc and MCS.

(3) In the "Co folding can accurately reproduce poses of ligands dissimilar to those trained." Subsection under Results, the authors' conclusions are hard to follow; they state that the co-folding models often mispredict or miss the alternative conformation, but they also predict poses that are distinct from the training set. What does that imply?

Our interpretation is actually a somewhat unsettling one: co-folding gets the ligand pose right even when it gets the protein wrong, and even when the ligand is novel. This suggests the models may be anchoring on conserved pharmacophoric interactions (like the adenosine-mimicking purine scaffold) rather than truly modeling the physics of the full complex. We added to the results section:

This result suggests that co-folding reliably recapitulates dominant ligand-binding interactions even in the absence of accurate protein conformational modeling, providing further support to the idea that they are learning specific interaction patterns rather than a deeper physics-based representation (Masters et al. 2025).

(4) The Discussion section connects the results and conclusions, but it can be challenging to grasp the study's overall message.

We think the final paragraph hits on three major points:

- Co-folding accurately predicts ligand poses for known binders, but fails to capture conformational changes

- Co-folding does not reliably distinguish true binders from false positives in virtual screening hit lists

- Docking and co-folding are complementary rather than competing tools

(5) The work is highly detailed and well executed, featuring thorough data analysis and statistical assessment. The value of the paper would be further enhanced by explaining how it differs from seemingly similar results reported in other studies, including the one cited in this manuscript (see https://www.biorxiv.org/content/10.64898/2025.12.04.692352v1).

The Mac1 results are completely unique. However, the docking datasets are exactly the same as those analyzed in the Menon et al manuscript. We don’t think our results differs from conclusions of the Menon et al manuscript as we wrote: These observations are supported by a fascinating study on some of the same ligand sets as investigated here, using AlphaFold3, reaching similar conclusions (Menon et al. 2025).

Reviewer #3 (Recommendations for the authors):

(1) Expand target diversity to include ion channels, transporters, etc., beyond enzymes and GPCRs.

(2) Investigate the cause of co-folding's failure in predicting rare conformational changes (e.g., adjust sampling, MSA inputs, or add experimental constraints).

(3) Mitigate docking bias in virtual screens (e.g., re-analyze unbiased compound libraries).

We addressed these three points in the public review above

(4) Test Boltz-2's affinity predictions without linear calibration and compare with FEP.

The data without linear calibration are included in the manuscript. Comparing such a large number of compounds with FEP is currently beyond our capabilities.

(5) Conduct proof-of-concept to test co-folding-docking integration for better hit rates.

We think this is well beyond the scope of this manuscript - but look forward to testing this idea in the future.

We also got one community review that we respond to below:

Summary

This manuscript evaluates the performance of co-folding models when tasked with 1) the recapitulation of a large number of experimentally determined co-crystal structures of Mac1 with a series of Mac1 ligands and 2) the rescoring of hits to identify false positives originally derived from a set of large docking-based virtual screens. The evaluation leverages a dataset of crystal structures and affinity data from high-throughput crystallographic and biophysical screens, respectively. These data uniquely enable this report to focus on the ability of co-folding models to handle ligands, resulting in an analysis that is particularly timely given the wide adoption of co-folding models and the relative scarcity of such ligand-focused benchmarks among existing evaluations, which have primarily focused on protein structure prediction or binder design.

Thank you for this thoughtful summary of our work

Feedback

The experiments and analyses in the manuscript are well thought-out and do not have any significant issues. There are a few high-level points that may improve the clarity and completeness of the results. Importantly, none of the suggested additional experiments will affect the conclusions of the paper, but rather help provide additional context for the results:

The first section presents an exciting opportunity to frame the Mac1 ligands against ligands in the PDB more broadly. It would be informative to assess whether chemotypes that are easier or harder to predict accurately and confidently are over- or under-represented in the PDB as a whole. Note that this is not a recommendation that new scaffold similarity metrics be incorporated into the analysis, but rather that analyses similar to those already performed in the manuscript are performed using all ligands in the PDB. For example, PCA-based analyses similar to those in Fig. 1c could be used to examine Mac1 ligands in the context of all PDB ligands enabling questions such as whether similarity to a nearest PDB neighbor, cluster size in a Tc/MCS PCA space, or other frequency-based measures show any relationship with prediction vs. crystal structure RMSD. Such analyses could provide additional insight into how effectively models leverage ligand information present in the PDB overall, as opposed to biases arising specifically from scaffolds represented in Mac1 structures in the PDB, which are already well covered in the manuscript. The conclusion that Tc/MCS do not correlate with the ligand RMSDs for the ligands already associated with the Mac1 is well supported, and presumably suggests that a correlation would not exist against the backdrop of the PDB, but it would be interesting to see the data using analyses similar to those already done in the manuscript nonetheless.

We are adding new figures in SFig.1 that consider how different clusters of ligands tested for our co-folding analysis are distributed across the chemical space in PDB. This is done by making a similarity comparison between every ligand in PDB and those tested in our analysis by Tc and MCS%, then plotting in PCA space for each metric. We are excited to see that each dataset covers a wide scope in PCA space, but at the same time, there are unexplored areas in the chemical space of PDB by co-folding.

Similarly, even though the four proteins used in this manuscript are not themselves the primary focus of the analysis, it would be valuable to perform a high-level assessment of the precedent for each protein in the PDB (beyond the count of liganded structures in Table S6), either in protein sequence space (e.g., MSAs) or structural space (e.g., FoldSeek). An analysis like this would provide important context about whether any of the proteins in the study have close homologs with liganded structures in the PDB, or are generally overrepresented in the PDB. The fact that the AUC for L-pLDDT for AmpC is higher than σ2 and D4, for example, is notable given the relative abundance of liganded AmpC structures in the PDB (this raises potentially interesting questions related to where DOCK3.7 and AF3 actually place the ligands, given the orthosteric β-lactam binding pocket in AmpC, although this is outside of the scope of this manuscript).

High-level assessment of the precedent for each protein in the PDB will definitely help to understand if proteins we used have close homologs with liganded structures in the PDB. Our Supplementary Table 6 covers the extent to which these liganded structures were available by cutoff dates for AF3, Chai-1 and Boltz-2. AmpC had more homologs than sigma2 and D4, and this may explain a better AUC for AF3 L-pLDDT specifically for this target.

A discussion of the affinity probability results (`affinity_probability_binary`) from Boltz-2 is likely warranted in the second section in addition to the pIC50s that are already reported (`affinity_pred_value`). The former seems like it would be more applicable for section 2 of the manuscript, but both warrant inclusion—they should both be calculated by default when the affinity pipeline in Boltz-2 is turned on, so it wouldn't involve any more inference.

As boltz-2 affinity module outputs both affinity probability binary output and affinity predicted value, we kept track of both metrics. So we tried re-ranking hit lists using both metrics. Where boltz-2 performed better (Sigma2, D4), binary probability values were more representative as a metric to differentiate true actives from non-binders. This was more clear in semi-logarithmic ROC plots. However, in AmpC, both Boltz-2 scoring metrics performed similarly. Such inconsistency in trend made it difficult to draw conclusions.

Minor points

A more detailed description of the experimental methods used to generate the ground-truth data in the introduction (even though these have been explained in prior works) would help orient the reader early on, and ground the benchmarking aspect of the story. In general, the abstract and introduction would benefit from a more cohesive through-line to tie the two complementary but orthogonal sections of the paper together.

We will include a more thorough description alongside the PDB depositions. As for the two sections, we have tried to tie them together from the perspective of drug discovery workflows…

The cutoffs in the "Co-folding can accurately reproduce..." section shift between 2.5 Å (from the ligand center of mass) and 2.0 Å. Is there a reason for this? Along similar lines, mentioning cutoffs for true positives/negatives when introducing the ROC analyses later on in the Mac1 section seems unnecessary since no cutoff should be necessary here.

We used 2.5A distance to COM to just get at “broadly the correct binding site” for fast filtering and 2.0A RMSD because that is the broadly accepted standard in the field for “relatively correct binding pose”.

Author response:

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

eLife Assessment

The nematode C. elegans is an ideal model in which to achieve the ambitious goal of a genome-wide atlas of protein expression and localization. In this paper, the authors explore the utility of a new and efficient method for labeling proteins with fluorescent tags, evaluating its potential to be the basis for a larger, genome-wide effort that is likely to be very useful for the community. While the evidence for the method itself is solid, carrying out this project at a large scale will require significant additional feasibility studies.

We appreciate the editor’s recognition that the evidence for our method is solid and that a genome-wide protein atlas in C. elegans would be highly valuable to the community. However, we respectfully disagree that “significant additional feasibility studies” are required. Take the yeast proteome-wide GFP tagging project (Huh et al., Nature 2003). It achieved ~75% coverage of ~6,000 proteins directly from an established protocol without any prior significant feasibility studies, at least to our knowledge. While the C. elegans genome is 3 times in size, we would argue that our tagging protocol may even be less labor intensive as it does not involve any cloning and the screening is visual, requiring no molecular biology skills. Reviewer 3 notes: ‘They also provide convincing evidence that labelling the whole proteome is an achievable goal with relatively limited resources and time.’

Our pilot study validates all key parameters for genome-wide scaling: editing efficiency at novel loci with untested reagents, viability of tagged worms, and detectability of multiple spectrally separated fluorophores across expression ranges. These address the core technical, biological, and practical challenges of large-scale endogenous tagging in a multicellular organism, leaving no fundamental barriers in our view.

The proposed cost and timeline align quite favorably with established large-scale consortium projects: e.g., ENCODE pilot analyzed 1% of the human genome at ~$55 million over 4 years; Mouse Knockout Consortium scaled to ~20,000 genes over 20 years (ongoing) with ~$100 million; Human Protein Atlas mapped ~87% of proteins with antibodies in fixed cells (through much more labor intensive methods) over 20+ years at >$100 million. With ~8% of C. elegans genes already tagged (WormTagDB) and labs already tagging entire gene classes (PMID: 40463100), scaling our protocol to the proteome is feasible, potentially covering the genome in 5-6 years by a single lab or faster with distributed effort at a reagent cost of merely $2.2 million. The main barriers now are funding commitment and assembling collaborators, not further feasibility testing.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Eroglu and Hobert demonstrate that injecting CRISPR guides and repair constructs to target three genes at a time, tagging each with a different fluorescent protein, and selecting which gene to tag with which fluorophore based on genes' expression levels, can improve the efficiency of gene tagging.

Strengths:

This manuscript demonstrates that three genes can be targeted efficiently with three different fluorophores. It also presents some practical considerations, like using the fluorophore least complicated by agar/worm autofluorescence for genes with low expression levels, and cost calculations if the same methods were used on all genes.

Weaknesses:

Eroglu has demonstrated in a previous publication that single-stranded DNA injection can increase the efficiency of CRISPR in C. elegans while inserting two fluorescent proteins and a co-CRISPR marker into three loci. The current work is, therefore, an incremental advance. In general, I applaud the authors' willingness to think ahead to how whole proteome tagging might be accomplished, but I predict that the advance here will be one of many small advances that will get the field to that goal.

Our manuscript indeed builds on prior multiplex editing (including our own co-CRISPR work), but the manuscript's primary contribution is not a novel technical breakthrough per se. Instead, our main goal was to pilot and strategize a feasible path to whole-proteome tagging in C. elegans and, most critically, test the following key parameters: (1) success rate of triple pools with prior untested reagents at novel targets; (2) utility of fluorophores across expression levels; (3) major effects on tagged protein function. In prior multiplexing, we used two targets which we already knew could be edited quite efficiently, with the 3rd target a point mutation with nearly 100% efficiency. Thus, it was not at all clear that picking 3 random genes and replacing the 3rd highly efficient locus with another less efficient large insertion would work or be sufficiently scalable for thousands of novel genes with unvalidated reagents at first pass.

The title vastly oversells the advance in my view, and the first sentence of the Discussion seems a more apt summary of the key advance here.

Some injections target genes on the same chromosome together, which will create unnecessary issues when doing necessary backcrossing, especially if the mutation rate is increased by CRISPR.

We disagree with the reviewer’s assessment of the need for backcrossing, for two reasons: (1) Prior studies have shown that off-target mutations are not a serious concern in C. elegans (reviewed in PMID: 26336798). For instance, WGS of strains after CRISPR/Cas9 found negligible off-target effects (PMID: 25249454, PMID: 30420468 – using similar RNP/ssDNA method and multiple guides; PMID: 23979577, PMID: 27650892 using other methods). Targeted sequencing studies have reported similar findings, using various CRISPR/Cas9 methods, with essentially no mutations at sites other than the intended target (PMID: 23995389; PMID: 23817069). (2) If the goal is to tag the entire genome, the introduction of backcrossing should not reasonably be a routine part of the initial tagging.

Lastly, if one really does want to backcross, the existence of tags on the same chromosome is actually an advantage because it permits selection for recombinants with wild-type chromosomes.

Also, the need for backcrossing and perhaps sequencing made me wonder if injecting 3 together really is helpful vs targeting each gene separately, since only 5 worms need to be injected.

Apart from our disagreement regarding backcrossing, we are puzzled by the reviewer’s comment. Why would one do single tagging at a time, rather than triple tagging if the whole point is to scale up tagging? It is important to keep in mind that the rate limiting step for tagging the whole genome is the number of injections that can be done per day. Since there is no cloning to generate the repair templates/guides and all other reagents are commercially available and not sample specific, these can be prepared quite rapidly. Being able to isolate multiple lines (together or independently) from the same injection increases throughput 3-fold and in our view does not provide any disadvantages as individual tags can be isolated independently if desired.

Beyond the numerous technical advantages pooling provides (also lower cost and throughput for making injection mixes as well as imaging), our results show that it yields epistemic benefits as well: we would never have noted the subcellular pattern in Fig. 6B, C with different sets of mitochondria being marked by different mitochondrial proteins had we imaged them separately or even aligned to a pan-mitochondrial landmark. As we mentioned in the discussion, grouping proteins predicted to localize to the same compartment together can simultaneously test how uniform or differentiated such compartments are during the screen.

The limited utility of current blue fluorescent proteins makes me wonder if it's worth using at all at this stage, before there are better blue (or far red) fluorescent proteins.

We do not think that the utility of current BFPs is that limiting. At least the theoretical brightness of mTagBFP2 is comparable to that of EGFP (PMID: 30886412), which was useful for the bulk of currently tagged proteins. Due to modestly higher autofluorescence in the blue spectrum, the practical brightness is somewhat less ideal, but we have shown that many proteins are expressed high enough to be detected quite well with mTagBFP2 by eye at low magnification. We also note that many tags that are not visible by eye under a dissection scope become visible with long exposure cameras of widefield microscopes or modern confocal (GaAsP) detectors, so the list of genes detectable with mTagBFP2 is likely to be much higher. We routinely use mTagBFP2 to super-resolve subnuclear structures with endogenous tags (e.g., in the nucleolus), with some tags having lower annotated FPKMs than the genes tested here.

Some literature reviews, particularly in the Introduction and Abstract, rely too much on recent examples from the authors' laboratory instead of presenting the state of the field. I'd like to have known what exactly has been done with simultaneous injection targeting multiple loci more thoroughly, comparing what has been accomplished to date by various laboratories' advances to date.

We are not sure what the reviewer is referring to. In the Abstract, we do not refer to any literature. In the Introduction, we cite 28 papers, 6 of those from our lab (4 of which providing examples of protein tags). We do not believe that this can be fairly called an unbalanced presentation of the state of the field.

This being said, we have gladly expanded our Introduction to provide more background on co-CRISPRing. Labs have routinely used co-conversion (“coCRISPR”) markers for picking out their intended edits (e.g., point mutations or insertions), as it has been shown by multiple groups that a CRISPR/Cas9 edit at one locus correlates with efficiency at other simultaneous targets (PMID: 25161212). Generally, making point mutations with the Cas9/RNP protocol is highly efficient, especially at specific loci such as dpy-10. However, multiple FP-sized insertions have not been routinely attempted. We and only one other group have successfully attempted it using previously working targets and reagents (e.g., 28% in PMID: 26187122). Importantly, the efficiency of such multiple insertions has never been assessed at scale and using entirely untested reagents at novel sites – critical parameters to determine for a whole genome approach. So, we test here (1) the efficiency of triple insertions and (2) the chance of getting them with new and untested guides and reagents.

In our view, since we have to use some injection/coCRISPR marker anyway for those genes which are not expressed at dissecting-scope visible levels (likely most genes), using highly expressed intended targets as improvised markers in a pooled approach makes our approach much more efficient. It allows us to find the worms with the highest chance of yielding CRISPR insertions, which we can screen with higher power methods for the dimmer targets, while enabling us to co-isolate other intended targets. Insertions, being often heterozygous in F1, can be segregated independently if desired, or homozygosed together to facilitate maintenance then outcrossed individually by those interested in studying specific genes in more detail.

In the revised version of this manuscript, we now discuss some of these points in the introduction section:

“Currently, around 1554 proteins representing 8% of the proteome are estimated to have been endogenously tagged (Leyhr et al., 2025). However, at current rates, tagging the proteome is projected to take around 100 years and likely involve numerous duplicate attempts on a small number of commonly studied proteins (Leyhr et al., 2025). It will thus be crucial for the field to coordinate tagging efforts and scale up tagging protocols to enable coverage of the entire genome at a reasonable timescale and cost. Given the number of injections is a major time-limiting factor, pooling multiple injections into one would at minimum cut tagging time by a factor of 3. In C. elegans, screening for novel CRISPR/Cas9-induced genomic edits is already facilitated either by use of co-injection markers (i.e., plasmids that form extrachromosomal arrays) that yield phenotypes or fluorescence in progeny of successfully injected worms, or co-editing well characterized loci using established and highly efficient reagents which likewise yield visible phenotypes. In the latter approach, termed “co-CRISPR”, worms edited at the marker locus are most likely to also carry the intended edit (Arribere et al., 2014). Recent methods for CRISPR/Cas9 mediated genomic insertions have pushed efficiencies to sufficient levels to simultaneously insert multiple fluorophores (e.g., mNeonGreen and mScarlet) as well as a co-CRISPR marker (dpy-10) at three independent loci in a single injection (Eroglu et al., 2023; Paix et al., 2015). These attempts pooled reagents previously established to work efficiently and targeted genes that were known to yield functional fusion proteins when tagged. Thus, while in principle current methods could allow tagging of at least 3 independent loci in one injection if a co-CRISPR marker is omitted, it is not known to what extent such an approach could be generalized across the genome with previously unvalidated reagents (i.e., guides and repair template homology arms) at novel loci to yield functional tags”

Reviewer #2 (Public review):

The manuscript by Eroglu and Hobert presents a set of strains each harboring up to three fluorescently tagged endogenous proteins. While there is technically nothing wrong with the method and the images are beautiful, we struggled to appreciate the advance of this work - who is this paper for?

We consider this paper to have two purposes: (1) motivate the community to come together to consider such genome-wide tagging approach; (2) provide a reference point for funding agencies that such an aim is not unreasonable and will provide novel interesting insights.

As a technical method, the advance is minimal since the first author had already demonstrated that three mutations (fluorophore insertion and co-CRISPR marker) could be introduced simultaneously.

We agree that the basic principle is similar. However, it was not clear that triple pooling three novel large edits would work, given the numbers in our original paper or that it would be scalable.

The dpy-10 coCRISPR marker previously used is a highly efficient single site, with close to 100% hit rate. We also knew in the earlier study that the two pooled insertions already worked quite efficiently and did not disrupt the function of targeted proteins. Exchanging these plus dpy-10 for three novel tags was not guaranteed to succeed for many potential reasons, including both biological and technical. For instance, such a “marker free” approach necessitates that a significant number of targets in the genome should be expressed highly enough to be visible by fluorescence stereomicroscopy when tagged with current best fluorophores. The chance of disrupting gene function by tagging was also not explored in detail in C. elegans, nor whether one untested guide is generally sufficient. We think that establishing these parameters was meaningful and necessary for the goal of whole genome tagging. We have clarified some of these points in the text.

As a pilot for creating genome-scale resources, it is not clear whether three different fluorophores in one animal, while elegantly designed and implemented, will be desired by the broader community. 

The usage of three different fluorophores is largely driven by the ability to co-inject and therefore cut injection effort by a factor of three. Moreover, having all three fluorophores together facilitates imaging and maintenance. Lastly, co-labeling has the potential to reveal unexpected patterns of co-localization or lack thereof (example: two mitochondrial proteins that we found to not have overlapping distribution). We clarified this point in the revised text in both the results and discussion.

Finally, the interpretation of the patterns observed in the created lines is somewhat lacking. A Table with all the observations must be included. This can replace the descriptions of the observations with the different lines, which could be somewhat laborious for the reader, and are often wrong. There are numerous mistaken expectations of protein expression here, but two examples include:

We are not convinced that our expectations are mistaken. Below we respond to the reviewer’s specific examples, and we are open to hear from the reviewer about additional cases.

(1) The expectation that ACDH-10 is enriched in the intestine and epidermal tissues (hypodermis).

There are multiple paralogs of this protein (see WormPaths or WormFlux) that may share functions in different tissues. There is also no reason to assume that fatty acid metabolism does not occur in other tissues (including the germline). Finally, there are no published studies about this enzyme, so we really don't know for sure what it's doing.

The expression of acdh-10 is annotated in multiple scRNA datasets as intestine and epidermal enriched (CeNGEN/Taylor et al. 2021, highest in epidermis; Ghaddar et al 2023 highest in intestine). We did not mean to imply that fatty acid metabolism does not occur in the gonad, nor that a paralog of acdh-10 could not be performing the same function in tissues where acdh-10 is not expressed.

However, this raises an important question: why have different paralogs doing the same thing? Duplicate genes with the same function are generally not evolutionarily stable (PMID: 11073452, PMID: 24659815). That there are such striking tissue specific expression patterns of an essential or widely expressed protein class suggests that paralogs of the gene likely differ in some meaningful parameter that might align with tissue-specific functional needs or regulation. The reviewer’s statement that ‘there are no published studies about this enzyme, so we really don't know for sure what it's doing’ is in fact an excellent demonstration of our point; finding out where the duplicates are expressed can provide a starting point to uncover potential differences between the paralogs. At the very least it can delineate to what degree paralogs diverge in their expression across the proteome and identify which such cases merit further study. In a more ideal scenario, prior information of protein function could indicate that the involved pathway requires tissue specific regulation.

(2) The expectation that HXK-1 is ubiquitously expressed.

Three paralogous enzymes are all associated with the same reaction, and we have shown that these three function redundantly in vivo, perhaps in different tissues (PMID: 40011787).

The cited paper (PMID: 40011787) does not show where they are expressed. We discussed redundancy/paralogs above in point 1, and in our view the same applies here. They may perform the same reaction but are likely to differ in some meaningful way, be it regulation or rate of activity, for them to be stably maintained as functional genes over evolution.

Moreover, single-cell RNA-seq data (PMID: 38816550) also show enrichment of hxk-1 in gonadal sheath cells.

The Ghaddar et al. and CeNGEN/Taylor et al. datasets do not show this. The scRNA paper cited (PMID: 38816550) also shows enrichment in neurons, pharynx, coelomocyte and germ cells which we did not note. In our view, these in fact further support our goals: often, transcript datasets alone (frequently used to infer tissue function) do not sufficiently predict protein expression. One can post hoc find an scRNA-seq dataset that aligns somewhat with our protein observations, but how does one know which to trust a priori? Disagreements between transcript datasets will ultimately require resolution at the protein level, in our view.

To clarify these points, we added the following to the discussion section:

“We also noted unexpected cell type dependent distributions of proteins involved in broadly important metabolic processes such as ACDH-10, which was depleted from the germline compared to other tissues, and HXK-1, which was highly enriched in the gonadal sheath. Notably, for these as well as other cases, scRNA-seq datasets were not sufficient to deduce a priori the observed cell type specific differences at the protein level. Importantly, many genes encoding metabolic enzymes including acdh-10 and hxk-1 have paralogs that likely perform similar catalytic functions. Yet, duplicate genes with identical functions are generally not evolutionarily stable (Adler et al., 2014; Lynch and Conery, 2000); thus such genes are likely to differ in some meaningful parameter (e.g., regulation or activity) that might align with tissue-specific functional needs. Fully annotating the expression patterns of paralogs at the protein level could indicate which tissues require unique metabolic needs and indicate which paralogous genes have undergone sub- versus neo-functionalization. For those proteins that are less functionally understood, unexpected distributions might indicate which merit further study.”

The table should have at least the following information: gene/protein name - Wormbase ID - TPM levels of single cell data assigned to tissues for L2, L4, and adult (all published) - tissues in which expression is observed in the lines presented by the authors.

We added some of this information such as annotated expression levels in young adults from various scRNA datasets (but not larval datasets as we did not image these). We note that each of these studies use different pipelines and report different metrics (scaled TPM/Z-score versus Seurat average expression versus TPM), so comparisons between them are not informative unless they are integrated and analyzed together.

Reviewer #3 (Public review):

Summary:

The authors argue that establishing the expression pattern and subcellular localisation of an animal's proteome will highlight many hypotheses for further study. To make this point and show feasibility, they developed a pipeline to knock in DNA encoding fluorescent tags into C. elegans genes.

Strengths:

The authors effectively make the points above. For example, they provide evidence of two populations of mitochondria in the C. elegans germline that differ qualitatively in the proteins they express. They also provide convincing evidence that labelling the whole proteome is an achievable goal with relatively limited resources and time.

We appreciate the referee’s recognition that whole proteome tagging is feasible.

Weaknesses:

Cell biology in C. elegans is challenging because of the small size of many of its cells, notably neurons. This can make establishing the sub-cellular localisation of a fluorescently tagged protein, or co-localizing it with another protein, tricky. The authors point out in their introduction that advances in light microscopy, such as diSPIM, STED, and ISM (a close relative of SIM), have increased the resolution of light microscopy. They also point out that recent advances in expansion microscopy can similarly help overcome the resolution limit.

(1) Have the authors investigated if the three fluorescent tags they use are appropriate for super-resolution microscopy of C. elegans, e.g., STED or SIM? Would Elektra be better than mTAGBFP2? How does mScarlet3-S2 compare to mScarlet 3?

All three tags work for ISM (i.e., Airyscan). We previously tried Electra (not for the genes tested here) but could not isolate positive tags. Given Electra is not that much brighter on paper than mTagBFP2 we did not pursue it further, though we recognize that these may simply have been unlucky injections. mScarlet3-S2 is quite a bit dimmer than mScarlet3 on paper – the advantage is that it has higher photostability. In our view, the limiting factor will be having FPs that are bright enough to screen, image and scale to the whole genome, so brightness will likely provide an advantage over photostability at this stage.

(2) Have the authors investigated what tags could be used in expansion microscopy - that is, which retain antigenicity or even fluorescence after the protocol is applied? It may be useful to add different epitope tags to the knock-in cassettes for this purpose.

mSG and mSc3 retain fluorescence after fixing with formaldehyde. We have not tested mTagBFP2 fluorescence in fixed worms. We agree that adding different epitope tags would be useful.

The paper is fine as it stands. The experiments above could add value to it and future-proof it, but are not essential. If the experiments are not attempted, the authors could refer to the points above in the discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Merged figures appear saturated, and use colors that won't work for red-green colorblind viewers. 

For all figures, we also show individual channels separately, which is common practice for making fluorescence images accessible to colorblind readers (PMID: 33788834). Figures highlighting non-overlap like 6B and C are already in accessible colors when merged (blue/green) and include a numerical quantification. 3-color RGB images preserve the greatest information for the highest number of individuals.

(2) Targeting ubiquitously expressed genes as a proof of concept gives me some concern that this might underestimate the challenges that may be experienced with less widely expressed genes.

While the genes were predicted to be ubiquitously expressed, many were not in practice, like HXK-1 and F54C8.1, which were also among the lower expressed genes on our list and highly cell type restricted. As discussed, the more tissue restricted a gene, the likelier that bulk RNA levels underestimate expression. Such genes are therefore more likely to be detected in a specific tissue. We routinely isolate tissue restricted endogenous tags, including those expressed in only a few neurons, with bulk FPKMs lower than the ranges tested in this manuscript.

(3) Some results are not shown or referenced (autofluorescence, for example, is shown using a schematic in Figure 1C).

We now provide representative images alongside what would be expected to be observed by eye during screening.

(4) It would be useful to describe how to recover worms from what is shown in Figure 1A. 

In the revised version, we added the following in the caption for Fig. 1A:

“Selected worms expressing the brighter tag can be screened for dimmer tags by higher magnification and long exposure imaging. Worms can be recovered directly from slides if immobilized by levamisole as described (Ghanta et al., 2021). Alternatively, single hermaphrodite worms can be isolated, allowed to lay eggs, then screened.”

(5) A blue bar of data must be missing from Figure 3B injection pool 5.

As stated in the text, “All but one tag (cox-6B::mTagBFP2) was visible in the F1 generation of injected P0 animals, and these were subsequently isolated among F2 worms positive for the other tags in the pool.”

To clarify that data points are not unintentionally omitted, we added the following text to the caption of Fig. 3B:

“For group 5 including cox-6B::mTagBFP2, worms with detectable levels of mTagBFP2 fluorescence were not recovered in the F1 generation but were isolated among progeny of F1s positive for mStayGold and mScarlet3; we were thus unable to quantify efficiency for this locus at F1.”

(6) Some expression or localization patterns were unexpected, but complications like germline silencing and protein mislocalization, with a small fraction localizing normally and rescuing function, were not presented as possibilities. Viability is used to confirm function, but without presenting whether this means 100% viability, less, or just the ability to maintain a strain.

We already do discuss mislocalization and functionality issues in the Discussion, as well as tradeoffs of alternate methods. Any existing method to observe biological molecules, be it protein, RNA or DNA, has multiple drawbacks and sources of artifacts, which are unlikely to be fully eliminated in the foreseeable future.

In regard to germline silencing of endogenously tagged genes in C. elegans, there is actually very little evidence for this. Collectively, various labs have now generated over 200 reporter alleles of germline-expressed genes (WormTagDB), with robust expression throughout the germline and retention of function. Likewise, numerous of our tags across fluorophores showed robust germline expressions including EEF-1A.1::mTagBFP2, Y22D7AL.10::mStayGold, and HAT-1::mScarlet3. In fact, overall transcript levels generally tended to underestimate germline enrichment at the protein level. We note that single-copy transgenes driven by eef-1A.1/eft-3 promoter by itself are frequently not expressed in the germline (PMID: 31064766); that we could detect EEF-1A.1 robustly in the germline when tagged endogenously is evidence that silencing is unlikely to be a widespread concern, and at the least less of a concern than single copy transgenes. We appreciate that for a transgene, presence/absence of specific sequence elements and genomic loci play a role in expression, but an endogenous tag captures all such information at a given locus.

Indeed, we found only two reports of endogenous tags being silenced in the germline, the first being a novel tag (not fluorophore) which initially prevented expression at the tagged locus (PMID: 30109984), but after making changes to the sequence to avoid silencing signals the authors could rescue expression and thereafter saw robust expression in various novel contexts with this tag. The second example (PMID: 34547227) leaves open the possibility that germline repression of that particular gene might be a part of its endogenous regulation.

Nevertheless, given it is probably rare if occurs at all, it will likely take a large scale tagging effort to uncover such cases at sufficient numbers to study. In our view, this further justifies tagging at large, ideally genomic, scales. If we do discover that there are numerous annotated germline proteins which we don’t observe by tagging, that would be interesting to study on its own.

(7) Halotag is presented in the Discussion as a small tag, but it is bigger than GFP.

Thank you for catching this. We have removed the discussion of Halotag. Given the comparable size to FPs, it would be unlikely to alleviate issues of tag functionality.

(8) It would be useful to include FPKMs and viability percentages in Table 1.

FPKM is included in column 6, but the title for this column is cut off. In the revised table FPKM values are now shown more clearly across stages.

We did not quantify viability percentage. In our view it does not yield an informative metric when there is little information about the protein’s required dosage for function, which was the case for most proteins here. A haplosufficient gene might yield a full brood size even if 50% of protein function is lost; conversely, a highly dose sensitive protein could yield penetrant and severe inviability with mild perturbation of function. It also is not actionable information at this stage if there is no alternate tagging strategy as a baseline of comparison. The worms we picked to image all have viable embryos as adults, so in those individuals the genes were likely to be sufficiently expressed and functional.

(9) Because establishing that a guide works well is a limiting step for many CRISPR experiments (once a guide works well, it's easy to inject 5 worms and get lines), I wondered if testing that for many genes is what is really needed in the field at this stage. 

Guide quality is rarely an issue in C. elegans, as for all the genes here we tried only one guide, all of which were previously untested. We now clarified this in the discussion section:

“Notably, we find that previously untested guide RNAs and homology arms perform exceptionally well at novel loci, as we only tested one set of reagents for each locus which yielded satisfactory tagging rates.”

(10) For a manuscript where the injection is so central to what was done, I was surprised to read in the Acknowledgments that all of the injections were done by someone who is not included as an author.

We are likewise surprised by such a comment but gladly clarify: Chi Chen has been with us as an expert microinjection specialist for more than 25 years and her very important technical contributions have been acknowledged in many dozen papers. Multiple authorship guidelines, including COPE’s and ICMJE’s, state that technical contributions alone do not qualify for authorship.

Reviewer #2 (Recommendations for the authors):

(1) We would encourage the authors to provide systematic validation of the reported insertions. The manuscript reports that 24 of 30 tags were isolated and visible, but does not clearly state whether each isolated line was confirmed by sequence‑level validation to be correctly in‑frame and free of unintended mutations at the target locus.

We appreciate the reviewer’s concerns on fidelity. These parameters have been assessed in prior published work (e.g., PMID: 30504364, PMID: 34748534) and in our hands are in the range of 80% whenever we sequence non-fluorescent tags of similar sizes. The efficiencies we observed are high enough that one can expect to recover numerous worms with the exact intended sequence for each target, though we would argue mutations within the FP reporter are less likely to matter if it retains high fluorescence.

(2) The manuscript presents aggregated success counts (e.g., 8/10 mTagBFP2 tags, 9/10 mStayGold, 7/10 mScarlet3) and useful narrative descriptions of injection outcomes. We also suggest including per‑locus success rates.

Figure 3B shows per locus success rate and source data is provided for this figure. Each dot is an individual injection and the Y axis is per locus rate. We now worded this more clearly in the figure’s caption.

“Total insertion efficiencies per locus for the indicated targets across injection pools.”

(3) For pools that required re‑injection after initial failures, we would like to see a description of the specific changes that were made to the injection mixes or procedures (e.g., new repair template prep, different Cas9 reagent lot, guide redesign). This will be useful troubleshooting information for others.

We re-made the exact same injection mix but with nanodrop to ensure the purity of the repair templates as assessed by absorbance ratios (A260/230 and A260/280) were sufficient after each purification step. No other changes were made. This is now specified in the methods section in the following way:

“For re-runs of pools 4, 6 and 10 which failed initially, we regenerated the repair templates and ensured that after each column purification, the A260/230 ratio of the purified DNA was ≥2.2 and A260/280 was 1.8 ± 0.05 when measured with a Nanodrop spectrophotometer.”

(4) The authors state that the fluorophore sequences are codon-optimized for C. elegans. We suggest they provide the exact donor/tag sequences, specifically state whether the fluorophore sequences contain any synthetic/artificial introns, or whether other sequence modifications (e.g., silent PAM‑disrupting mutations) were included in the donor templates. 

This information is provided in Supplementary Table 1.

(5) Page 3: Include a reference for "The C. elegans genome encodes around 20,000 genes" 

We added a reference to the most recent release of the genome (WS237, May 2013). Spieth et al., 2014.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to uncover novel therapeutic vulnerabilities in APC-mutant colorectal cancer (CRC), which constitutes the majority of CRC cases. They hypothesized that modulating oxygen-sensing pathways (via PHD inhibition) could disrupt adaptive stress responses in these tumours.

Strengths:

The study employs a powerful, two-pronged approach to identify Molidustat's targets. By using both Thermal Proteome Profiling (TPP) and an orthogonal chemical proteomic competition assay, the authors provide compelling evidence that GSTP1 is a genuine, direct off-target, effectively addressing the common limitation of indirect effects in proteomic screens.

Weaknesses:

(1) In Figure 1, the current data rely on a single guide RNA (sgRNA). To make the data solid, at least two independent sgRNAs targeting different regions of PHD2 should be used.

We thank the reviewer for raising this. Clarity on the CRISPR strategy was missing from the original submission and we have now added the following to the Methods (Page 4). We did not use a single sgRNA. PHD2 was targeted with a pool of three chemically modified crRNAs:

(IDT Alt-R; target sequences: 5'-TACAACCAGCATATGCTACA, 5'GTGGCTGCCGAAGCCGAGCC, 5'-GATAAGATCACCTGGATCGA)

Delivered as in vitro assembled ribonucleoprotein complexes with high-fidelity Cas9. This format has been reported to achieve high on-target efficiency while minimising off-target cutting [1,2] such that any residual stochastic off-target events are distributed across the population and are not expected to manifest as a coherent phenotype at the population level. Working with pooled, unselected knockouts rather than single-cell clones also avoids the confounds of clonal heterogeneity that normally motivate the use of multiple independent guides and rescue experiments in single-clone workflows. We have previously validated this approach for GSTP1 knockout in a separate single-cell proteomics study [3], where loss of GSTP1 protein was observed in over 90% of single cells and GSTP1 was the most significantly altered protein between sgControl and sgGSTP1 populations.

(2) Figure 3E: Asn205 site should be mutated to prove that whether Molidustat inhibits GSTP1 activity via Asn205 or not.

This is a good suggestion, and we explored it in silico before concluding it was not tractable. We used PyMol mutagenesis to model Molidustat binding to GSTP1 variants at the predicted contact residues: Asn205 was mutated to Ala, Gly and Ser; Trp39 (predicted to hydrogen-bond Molidustat) was mutated to Ala, Phe and Thr; and a Tyr8Phe/Asn205Ser double mutant was also modelled. In every case, Molidustat reoriented within the active site and adopted an alternative hydrogen-bonding configuration (most commonly with Tyr8), yielding a docking score equal to or better than binding to native GSTP1 (Author response image 1– Author response image 4). The model therefore does not predict any single or double point mutant that would ablate Molidustat binding in a clean, interpretable way, and we could not design a rational loss-of-interaction mutant on this basis. Given this limitation, and that definitive mapping of the binding interface would require co-crystallography, which is beyond the scope of the present study, we have moved the docking model to the supplement and flagged it as predictive rather than definitive.

Author response image 1.

Molidustat in native GSTP1

Author response image 2.

Molidustat docking with mutated GSTP1, Asn205 mutated to Gln205

Author response image 3.

Molidustat docking with mutated GSTP1, Tyr39 mutated to Phe39

Author response image 4.

Molidustat docking with mutated GSTP1, Asn205 mutated to Ser205 and Tyr8 mutated to Phe8

(3) Figure 5B and 5C: The metabolic imbalance phenotype observed upon dual knockout of PHD2 and GSTP1 requires rescue experiments to confirm on-target specificity.

We thank the reviewer for this important point and agree that rescue experiments could represent the most direct demonstration of on-target specificity for the metabolic phenotype observed in Figures 5B and 5C. These rescue experiments are necessary when working with single clones, as they allow for comparing a knock-out clone with a reconstituted pool and sidestep the issue of clonal heterogeneity.

In our case, we think that there is no advantage to doing so, as we work with pooled knockouts, so any clonal heterogeneity is diluted in the pool.

One could even make the case that such a rescue experiment would introduce additional artefacts. Combined loss of PHD2 and GSTP1 leads to reduced cellular viability, with decreased proliferation and increased apoptosis, consistent with a synthetic lethal interaction. To devise a rescue experiment, we would have to isolate a single-cell clone (the pool is not a complete 100% knock out, WT cells would outgrow the knock out cells). The isolation of such a clone that has overcome the anti-proliferative insult of the double knockout is likely to have a phenotype distinct from the original, pooled population, as would the rescued have from the WT cells. For these reasons, we have not performed rescue experiments in the current study. We have added the absence of a rescue as a limitation to the study in the discussion

“While genetic rescue experiments would provide definitive confirmation of on-target specificity, the pronounced loss-of-fitness and apoptotic phenotype observed upon combined PHD2 and GSTP1 loss limited the feasibility of establishing stable rescued double-knockout populations, and therefore represents a limitation of the current study.”

Reviewer #2 (Public review):

Summary:

The authors aimed to determine Molidustat targets and the potential utility of these findings. They clearly demonstrate that Molidustat interferes with GSTP1 and some other proteins on top of PHD2. They also demonstrate that PHD2 deletion is not sufficient to recapitulate Molidustat effects in cells and proteomes. Finally, they demonstrate synthetic lethality in organoids for Molidustat and APC deletion.

Strengths:

The data on Molidustat proteomes, GSTP1 binding, inhibition and metabolic health of organoids is really clear. All biochemical, docking and omic data are really strong. The potential impact of these findings could be the use of Molidustat in APC null tumours and awareness of potential off-target effects.

Weaknesses:

A main but minor weakness is that Molidustat also inhibits other PHDs, although these are less expressed. PHD1 has been shown to control the cell cycle and be expressed in the colon, where it is needed for viability. Although this does not explain the lack of effect of other PHD inhibitors, it does warrant some discussion. The use of MTT is not very good to detect viability when it measures metabolism; this also needs to be discussed and perhaps supplemented with colony or cell number measurements.

Great point, for this reason, we have assayed apoptosis throughout. In addition, we have added a clonogenicity assay with APC organoids. Organoid cells were treated with an acute dose of Molidustat. We subsequently measured the level of Lgr5 (a stem cell marker) and of the ability of the cells to generate organoids (these data have been added as Figure 5 F-G.)

Reviewer #3 (Public review):

In this paper, the authors revealed that Molidustat can induce a dose-dependent increase in Caspase-3/7 activity in the HT29 cell line, which is an APC-mutant colorectal cancer cell line. More importantly, they found that targeting PHD2 alone cannot cause cell death. By using thermal proteome profiling (TPP) and orthogonal chemical proteomic competition assays, they determined GTSP1 as a previously undiscovered off-target of Molidustat. They also revealed that combined PHD2 and GSTP1 loss leads to an increase in intracellular ROS and apoptosis. Moreover, they evaluated the effects of Molidustat in colonic organoids and showed that

Molidustat has a high selectivity for colonic organoids with activated WNT signaling and/or KRAS pathway alterations, and this effect is not reproduced by hydroxylase inhibition alone, providing a new potential approach to targeting both PHD2 and GTSP1 for the treatment of APC-mutant CRC.

Specific comments:

(1) What is the possible molecular mechanism of dual GSTP1/PHD2 loss, inducing cell death?

This is an important question. Our data support a model in which combined loss of GSTP1 and PHD2 disrupts cellular redox homeostasis, leading to accumulation of reactive oxygen species, increased GSSG/GSH ratios, and depletion of antioxidant buffering capacity. This redox imbalance is accompanied by downregulation of pro-survival pathways. In this context, activation of apoptotic signalling, as evidenced by increased caspase-3/7 activity and proteomic enrichment of apoptosis-associated pathways, contributes to the observed cell death phenotype.

While apoptosis is supported by our data, the magnitude of oxidative stress suggests that additional oxidative stress-associated cell death mechanisms may also contribute. We have clarified this point in the Discussion (Page 11).

(2) Can the authors mutate the binding site of Molidustat on GTSP1 to verify the in silico docking results?

This is a very important question. Currently, the model is of limited value. Reviewer 1 had a similar question. Can we refer you to Reviewer 1, question 2.

(3) Evidence for Molidustat inhibiting PHD2 activity or stabilising HIF-1α should be provided.

We thank the reviewer for this suggestion. Data showing HIF-1α stabilisation and evidence of downstream signalling is now added to Supplementary Figure 1.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I only have minor suggestions:

Molidustat also inhibits other PHDs, although these are less expressed. PHD1 has been shown to control the cell cycle and be expressed in the colon, where it is needed for viability. Although this does not explain the lack of effect of other PHD inhibitors, it does warrant some discussion. The use of MTT is not very good to detect viability when it measures metabolism; this also needs to be discussed and perhaps supplemented with colony or cell number measurements.

This is correct, PHD1 is of particular interest, given the effects inhibition/knock-out has on the inflamed colon. We have added a new paragraph to the Discussion (Page 13) that addresses the isoform selectivity of Molidustat. We note that, although developed as a PHD2 inhibitor, Molidustat retains appreciable activity against PHD1 and PHD3 [4], and we discuss the non-redundant and in some contexts opposing roles of PHD1 and PHD2 in the colon, PHD1 loss is protective in DSS colitis [5] and restrains colitis-associated tumour growth, whereas PHD2 loss in the tumour and stroma is reported to inhibit metastasis and treatment response [6]. We further note that this pattern of isoform engagement is shared with other pan-PHD inhibitors that did not phenocopy Molidustat in our screens, indicating that PHD isoform profile alone is insufficient to explain Molidustat’s distinctive activity and pointing to GSTP1 off-target engagement as the key distinguishing feature. We argue that localised colonic delivery (as discussed earlier in the Discussion) would concentrate drug at the APC-mutant epithelium while limiting systemic exposure.

We fully agree with the reviewer, MTT measures metabolic activity/NADH levels rather than viability in the strict sense, and that this is particularly relevant for a compound that perturbs redox metabolism. We have added a clonogenicity assay in APC organoids (Fig. 5 F-G) to supplement the MTT and Cleaved Caspase 3 assays already present in the manuscript.

(1) Lee, J. K. et al. Directed evolution of CRISPR-Cas9 to increase its specificity. Nat. Commun. 9, (2018).

(2) Sakovina, L., Vokhtantsev, I., Vorobyeva, M., Vorobyev, P. & Novopashina, D. Improving Stability and Specificity of CRISPR/Cas9 System by Selective Modification of Guide RNAs with 2′-fluoro and Locked Nucleic Acid Nucleotides. Int. J. Mol. Sci. 23, (2022).

(3) Makar, A. N., Holkham, J., Lilla, S., Wilkinson, S. & von Kriegsheim, A. Overcoming preservation challenges to enable single-cell proteomics of fixed cell and tissue samples with retained proteome integrity. Preprint at https://doi.org/10.1101/2025.03.10.642380 (2025).

(4) Flamme, I. et al. Mimicking hypoxia to treat anemia: HIF-stabilizer BAY 85-3934 (molidustat) stimulates erythropoietin production without hypertensive effects. PLoS One 9, (2014).

(5) Tambuwala, M. M. et al. Loss of prolyl hydroxylase-1 protects against colitis through reduced epithelial cell apoptosis and increased barrier function. Gastroenterology 139, (2010).

(6) Leite de Oliveira, R. et al. Gene-Targeting of Phd2 Improves Tumor Response to Chemotherapy and Prevents Side-Toxicity. Cancer Cell 22, (2012).

Author response:

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

eLife Assessment

This study used pupillometry to provide an objective assessment of a form of synesthesia in which people see additional color when reading numbers. It provides convincing evidence that subjective color ratings are matched by changes in pupil size that recapitulate brightnessmediated changes when exposed to the real color. The work provides a valuable contribution to the literature on both synesthetic perception and the use of pupillometry to probe perception and related psychological processes.

We were pleased to learn that our manuscript was of interest to the reviewers and the editor. We thank the reviewers for their useful feedback and have addressed all their comments in the revised version. We here give the most prominent changes as quotes.

We thank all reviewers and for their very helpful input.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Knowing that small pupil-size variations accompany brightness variations (even when these are illusory), the authors asked whether pupil constrictions would accompany the synesthetic perception of a brighter color (compared with a darker one), induced by the presentation of a blackwhite character. This grapheme-colour synesthesia is only experienced by a few participants, sixteen of whom were enrolled in this study. The results reliably showed that a relative pupil constriction would "betray" the perception of a brighter color in these participants, while no such effect would be observed in control participants who were asked to report a color in association with each grapheme, even though they did not perceive any.

Strengths:

The main strength of the study lies in its combination of psychophysics (brightness ratings) and pupillometry, which allowed for showing clear-cut results.

Weaknesses:

Some relatively minor weaknesses concern the ancillary analyses, which tackle secondary questions and are not entirely convincing.

(1) The linear mixed model approach is a powerful way to identify important variables, but it does not clarify whether the key factors are between-subject or between-trial variations. Some variables are inherently defined at a subject level (e.g., PA scores), others are not. I would strongly recommend an alternative visualisation of the results to examine inter-individual variability.

Visualizing the highly idiosyncratic effects is indeed challenging. Addressing R1’s point 4 and a point brought up by R2, we updated all figures to now visualize pupil size in millimeters instead of arbitrary units. Furthermore, we added a supplementary figure (supplementary figure 4) that visualizes pupil size change without demeaning (please see reply to point 4).

To get a better grasp of the interaction between lightness and coupling strength, we further included the supplementary figure 5 that splits by lightness and coupling strength in synesthetes.

Furthermore, as this review and response will be publicly available, Author response image 1 provides participant-mean traces per lightness bin in addition to the overall means and hopefully makes the stability/variability of effects visually clearer (in addition to the strip plots that attempt this for the average response).

Author response image 1.

We hope that these additional visualizations make the effects of interest more transparent. Ultimately, however, the LME figure likely provides the information best, albeit at the cost of complexity.

(2) It is not clear why taking the first derivative of pupil size in Figure 5 would isolate the effect of arousal, eliminating those of luminance and contrast changes (in fact, one could argue for the opposite, since arousal effects are generally constant for extended periods of time while contrast effects are typically more local and transient).

First, please note that the results in 2.3.1 cannot be explained by task or context effects such as luminance and contrast: the exact same active color reporting task (same task and context) was presented to synesthetes and non-synesthetes.

Indeed, the reviewer is correct that the first derivative does not eliminate other concurrent pupil-driving effects, that was expressed wrongly in our original text. Indeed, any stimulus-locked effect, such as the luminance and contrast effects, but also the effort effect will reflect similarly in the derivative measure.

We did take the derivative because pupil responses driven by other non-trial related activity, such as increasing tiredness or excitement over the course of trials differ almost by necessity between participants, thus creating variability. However, these effects are most likely happening at a slower timescale and thus show less in the derivative measure. Accordingly in past research, we previously found clearer response-locked effects in the past when using a derivative measure (Douze et al., 2025; Ten Brink et al., 2024). This way, we also hoped to get rid of such variability that happens between participants for this between participant analysis.

Even if we were to use the same baseline corrected analysis, we would arrive at the same conclusion: we here directly compared baseline-corrected pupil sizes by taking individual differences into account (using a LME). In other words, we tested for the same question, but not relying on the derivative. We thus compared baseline-corrected pupil sizes using over-time LMEs. Group (active control vs. synesthete) gained significance between ~1.7s and 3s, aligning with the derivative-based result.

Author response image 2.

t-values of a per-time point LME predicting pupil response from group (synesthete/active control) Group reached significance.

In sum, we deem the derivative more powerful/more appropriate in this context, but the interpretation of findings does not hinge on that analysis choice (as can be seen in the Author response image 2).

We corrected the claims on the derivative as a measure cleaning out other effects that indeed was oversimplified as it stood. We now write:

“Mental effort presents in task-evoked pupil dilations, yet other factors simultaneously affect the pupil, such as luminance and contrast changes at trial onset, as well as slower trends across the session (e.g., fatigue). To reduce the influence of these slower, non-trial-locked fluctuations while retaining the trial-evoked dynamics, we calculated the first derivative of the pupil time course to assess the velocity of pupillary changes (Butterworth filter, 18 Hz, order 3, 2.5 Hz lowpass, following our previous works [60, 61]).”

Douze, B. T., Ten Brink, A. F., Dijkerman, H. C., & Strauch, C. (2025). Pupil responses objectively index pharmacologically altered tactile sensitivity. Cortex, 193, 90-104.

Ten Brink, A. F., Heiner, I., Dijkerman, H. C., & Strauch, C. (2024). Pupil dilation reveals the intensity of touch. Psychophysiology, 61(6), e14538.

(3) It is a pity that responses to physical brightness modulations were only measured in the synesthete group, not in controls, as this would have allowed for ruling out differences in pupil reactivity across the two populations.

The reviewer is correct that this would allow additional comparisons, but argue that light responses in healthy control samples are very well documented and stereotypical. For instance, Bergamin & Kardon (2003) provide very systematic latency estimations, for low-luminance change stimuli in the realm of about 320ms that can accelerate to about 250ms for very strong luminance changes. Our relatively small luminance increments should thus be expected in this range. Indeed, this also well describes the response latencies we observed in synesthetes when exposed to the colored disks. While there is no detailed information about participants in Bergamin & Kardon (2003), data from previous studies shows very similar pupil light response profiles in a healthy student control population that matches our synesthetes well demographically (Strauch, Romein et al., 2022 Figure 2a, exact same lab as for the present study; Koevoet et al., 2025 Figure 3a). See also the further responses, baseline pupil size in millimeters across groups did not differ.

Together, we can safely conclude that pupil light responses in synesthetes are not different from pupil light responses in controls. We agree with the reviewer that this is a sensible point to also make in the manuscript:

“Specifically, pupil size first responded significantly to physical luminance after 330 ms (see Supplementary Figure 7 for per-timepoint LME; in line with response latencies of similar control populations, see Bergamin & Kardon [52], Koevoet et al. [40], and Strauch et al. [53]), but only responded significantly to synesthetic lightness at about 870 ms (see also Figure 3c vs e and Figure 4 for per-timepoint LME)”.

Bergamin, O., & Kardon, R. H. (2003). Latency of the pupil light reflex: sample rate, stimulus intensity, and variation in normal subjects. Investigative Ophthalmology & Visual Science, 44(4), 1546-1554.

Koevoet, D., Naber, M., Strauch, C. & Van der Stigchel, S. Presaccadic Attention Shifts Up-and Downwards: Evidence From the Pupil Light Response. Psychophysiology 62, e70047 (2025).

Strauch, C., Romein, C., Naber, M., Van der Stigchel, S., & Ten Brink, A. F. (2022). The orienting response drives pseudoneglect—Evidence from an objective pupillometric method. Cortex, 151, 259-271.

(4) Another concern is with the visualisation of the pupil traces in Figure 3 (main results); these were heavily pre-processed (per-participant demeaned), losing any feature besides the effect of interest and generating the unrealistic expectation that perception of dark/bright colors generate a net dilation/constriction of the pupil - whereas perception-related modulations of pupil size are always relative and generally small compared to the numerous other effects registered in pupil size. It would be far better to see the actual profiles, preserving the unfolding of dilations and constrictions over time, especially since these are further analysed in Figures 4 and 5.

Indeed, the expectation that any dark synesthetic experience would lead to pupil dilation whereas any bright synesthetic experience would lead to constriction is not warranted – it would only do that relative to the counterfactual of not having that experience.

Many factors affect the pupillary signal at the same time, and often differently across individuals (think of tiredness etc.), making merely baseline corrected traces seemingly noisy. Our visualization highlights that there is a systematic part to that variation that lies in the synesthetic brightness experience.

Visualizing the effects of idiosyncratic experiences, varying within and between participants is challenging. For the theoretical insight brought about through our paper in Figure 4 (synesthesia being sensory in nature), demeaning is favorable in our opinion as it isolates the effect of interest in visualization. However, for methodological reasons and to better show effect sizes etc., there is certainly use in additional transparency. We now thus provide non-demeaned traces in the supplementary material as the reviewer suggested and also refer to these in the main manuscript. Furthermore, all figures are now provided in millimeters, with all pupil related analysis being rerun and updated to this end (without qualitative changes to the results). This should further rectify possibly inflated expectations about the absolute size of effects and allows to put effects into perspective across studies. We now added:

“Pupillary data were transformed from arbitrary eyelink units to millimeters using a conversion factor obtained with an artificial eye (see Hayes & Petrov, 2016).”

Hayes, T. R., & Petrov, A. A. (2016). Mapping and correcting the influence of gaze position on pupil size measurements. Behavior research methods, 48(2), 510-527.

Impact:

Despite these weaknesses, and especially if they are adequately addressed in the review, this work is likely to improve our understanding of synesthesia, providing a new tool to quantify the subjective sensations; an interesting potential extension would be using pupillometry for tracking changes over time of the synesthetic experiences, opening up the possibility to evaluate the importance of learning for this peculiar experience.

We were happy to read our manuscript was evaluated this positively and hope that our replies can address the remaining smaller concerns and make findings more transparent to the readers.

Reviewer #2 (Public review):

Synesthesia is a neurological condition where stimulation of one sensory channel leads to involuntary, automatic, and consistent experience of another, unrelated percept. For example, Sir Francis Galton (1880, Nature) famously described the robust tendency of some individuals (synesthetes) to associate numerals with a distinct color. Ever since, synesthesia has continued to attract a broad interest in the cognitive neurosciences in light of its implications for the study of domains such as perception, consciousness, and brain connectivity, among others.

Strauch, Leenaars, and Rouw measured pupil size in a group of 16 grapheme-color synesthetes and two matched control groups. The participants were presented with gray digits - that is, visual stimuli having identical physical properties in terms of brightness. Each participant subsequently rated the corresponding evoked color and brightness: unlike controls, synesthetes did so in a very consistent and reliable fashion. Accordingly, this was also shown in their pupils: despite the same objective luminance, digits associated with brighter percepts caused their pupils to constrict, and digits associated with darker percepts caused their pupils to dilate more than controls. These results highlight how crossmodal correspondences are deeply rooted in synesthetes, and put forward pupillometry as a particularly appealing biomarker for some phenomenological experience (at least those grounded in "brightness").

Further strengths of the technique are its temporal resolution and its responsiveness to several constructs. Across several tasks, the authors show, for example, that responses to synesthetic light are somewhat slower than responses to real light (i.e., they are likely mediated), but at the same time faster than responses to mental imagery. The role of mental imagery can also be reasonably dismissed when considering the second feature of pupil size: its responsiveness to mental effort and cognitive load. The pupils tend to dilate with demanding, challenging tasks, and this was the case when control participants were asked to report the color of a digit for which they did not consistently experience a synesthetic association. The same task was, instead, seemingly effortless for synesthetes, again speaking in favor of the automaticity of number-color correspondences in their case.

Overall, the findings by Strauch, Leenaars, and Rouw are highly significant for the field and likely to be impactful. The strength of their evidence, when accounting for the relatively small sample size and the inherent variability of both phenomenology (color perception and subjective reporting) and physiology (pupil size), is adequate and sufficiently convincing.

We were glad to read this overall very positive assessment of our work and thank the reviewer for the additional non-public suggestions for improvements.

Reviewer #3 (Public review):

Summary:

In the present study, the authors examined pupillary responses to uncolored stimuli (number graphemes) among number-color synesthetes and non-synesthetes. After seeing a digit, the synesthetes and active control participants were asked to indicate which color they perceived using three dimensions of hue, saturation, and lightness. The lightness values were the primary independent variable for follow-up analyses. To see how the pupil responded to psychologically "bright" and "dark" digits, the authors split the reported lightness values at the median and plotted them. The synesthetes showed a pupillary constriction to digits they perceived as bright and dilation to digits they perceived as dark. Active control participants did not show that effect. In a subsequent block, only the synesthetes were shown the colors they reported perceiving as colored discs. Their pupillary responses were similar. The authors also found that the differences in pupillary responses between light and dark perceptions (with digits) were only slightly delayed in their onset to the perception of a colored disc, and therefore, the color perception accompanying a digit is unlikely to be effortful or a retrieved association, but occurs rather automatically.

Strengths:

The authors employed a well-controlled and designed quasi-experiment comparing colorgrapheme synesthetes to non-synesthetes and showed convincingly that the color perceptions accompanying graphemes alter the physical perception of brightness. They also made a reasoned attempt to rule out the possibility that color associations are occurring effortfully via retrieved associations.

We appreciate the positive assessment and useful suggestions for revision.

Weaknesses:

There are some areas in which the implications of these findings could be elaborated upon. I had the following questions:

(1) Are the pupillary responses among synesthetes, which objectively do not seem to match the degree of physical stimulation entering the retina, in any way maladaptive for eye functioning? I understand the constriction/dilation of the pupil to not only benefit visual acuity but also to protect the retina from damage. Are synesthetes at any risk of retinal damage due to over-dilation of the pupil to brighter stimuli? Or are these effects of a magnitude that is too small to matter? As reported in arbitrary units, it was hard to know how large these effects were in terms of measurable changes in dilation (e.g., millimeters).

This is an interesting point. Some argue that pupil size changes in a mid-range mildly affect optics thus affecting detection performance, contrast perception, and depth of field (Eberhardt et al., 2022, Mathôt & Ivanov 2019, Ruuskanen, Boehler, & Mathôt, 2025), rather than serving a protective role for the retina (Mathôt, 2018). Indeed, any effects reported here were quite small. We agree with the reviewer that this can be made more accessible by reporting effects in millimeters. We thus now adjusted all figures accordingly and write in the methods section:

“Pupillary data were transformed from arbitrary eyelink units to millimeters using a conversion factor obtained with an artificial eye (see Hayes & Petrov, 2016).”

Note that even the largest effects here (those elicited by physical luminance change in block 2 for the synesthetes) only caused differences in pupil size of about 0.3mm. This lies below the maximal pupil dilations observable in response maximal effort (about 0.5mm), for instance, and substantially below the full range of pupil size changes elicited through strong luminance stimulation (several millimeters). We therefore deem the changes in pupil size as obtained in our study too minor to be practically maladaptive for optics/perception.

Eberhardt, L. V., Strauch, C., Hartmann, T. S., & Huckauf, A. (2022). Increasing pupil size is associated with improved detection performance in the periphery. Attention, perception, & psychophysics, 84(1), 138-149.

Hayes, T. R., & Petrov, A. A. (2016). Mapping and correcting the influence of gaze position on pupil size measurements. Behavior research methods, 48(2), 510-527.

Mathôt, S., & Ivanov, Y. (2019). The effect of pupil size and peripheral brightness on detection and discrimination performance. PeerJ, 7, e8220.

Mathôt, S. (2018). Pupillometry: Psychology, physiology, and function. Journal of cognition, 1(1), 16.

Ruuskanen, V., Boehler, C. N., & Mathôt, S. (2025). The Interplay of Spontaneous Pupil-Size Fluctuations and EEG Power in Near-Threshold Detection. Psychophysiology, 62(3), e70035.

(2) Likewise, is the automatic synesthetic merging of two percepts something that could be learned such that natural synesthetes and "artificial" synesthetes would look similar? For example, if a group of non-synesthetic participants were to learn a color-grapheme association to automaticity, would you expect their pupillary responses to the graphemes look similar to the synesthetes'? If so (or if not), what would this tell us anything about the phenomenology of synesthesia?

We find this question most interesting. Likely, different synesthesia researchers wouldn’t even fully agree on the most plausible answers to these questions. Training studies have shown that nonsynesthetes can be trained to associate particular colors to particular graphemes, as revealed in the synesthetic Stroop effect: interference effects of the learned color onto reporting the typeface color of the grapheme. The degree to which non-synesthetes can be trained to become similar to synesthetes is however still topic of debate.

We now discuss as follows:

“Future studies could examine to what degree training a non-synesthete to associate specific colors to particular inducers (e.g., digits), can provide similar patterns of results as genuine synesthesia (Bor et al., 2014, Colizoli et al., 2012, Rothen & Meier, 2014). Could learning produce similar brightness-related pupil effects in non-synesthetes? Similarly, would effort-linked responses diminish with increased training duration? The perhaps most interesting question relates to response latencies: Would a trained participant ever be able to produce brightnessrelated pupil effects as fast as a synesthete?”

Bor, D., Rothen, N., Schwartzman, D. J., Clayton, S., & Seth, A. K. (2014). Adults can be trained to acquire synesthetic experiences. Scientific reports, 4(1), 7089.

Colizoli, O., Murre, J. M., & Rouw, R. (2012). Pseudo-synesthesia through reading books with colored letters. PloS one, 7(6), e39799.

Rothen, N., & Meier, B. (2014). Acquiring synaesthesia: insights from training studies. Frontiers in human neuroscience, 8, 109.

(3) Do the synesthetic perceptions of digit graphemes merge in a sensible way? For example, if a synesthete sees a particular color with the digit 1, and a different color with the digit 9, what do they perceive when they see 19? or 1-9, or 1 9? Is there color blending, or an altogether different color perception?

This is a very interesting question indeed. While each synesthete will have their own specific expression of synesthesia, there are regularities in how a combination of digits evokes synesthetic color. First, if asked about the color of a specific digit, each digit keeps its own color, as the color of a digit is linked to the identity of the digit (Dixon et al., 2006). Context effects are however possible, in particular when context alters the interpretation of the digit (Myles et al., 2003). A particularly common context in a multi-digit number is a dominant first digit, spreading its color to the subsequent digits in the number. However, as the digit color is linked to digit identity, what does ‘not’ happen is a mixing of colors into a qualitatively new color; for example, a yellow "1" and blue "9" do not merge into a green "19".

Dixon, M. J., Smilek, D., Duffy, P. L., Zanna, M. P., & Merikle, P. M. (2006). The role of meaning in grapheme-colour synaesthesia. Cortex, 42(2), 243-252.

Myles, K. M., Dixon, M. J., Smilek, D., & Merikle, P. M. (2003). Seeing double: The role of meaning in alphanumeric-colour synaesthesia. Brain and Cognition, 53(2), 342-345.

Many thanks for the constructive assessment of our work.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I am not sure I'd use the term 'cross-modal' given that the case considered here (graphemecolor) is purely visual.

The reviewer is absolutely right: the term 'cross-modal' has a historical background rather than reflecting an exact factual accuracy. The term is still commonly used however, as it readily reflects how the induced additional experience is always of a different (sub)type than the inducing experience. There is a cross-over between experiences that might occur within the same sensory modality, or even induce awareness of a particular concept. But key to synesthesia is the crossover experience as the inducer and concurrent are different (sub)types of experiences. For example, seeing a letter can evoke a synesthetic experience of seeing a color, or evoke awareness of a particular gender or personality of that letter, but does not evoke another letter. To remain consistent with literature, we refer to 'cross-modality' when explaining the link to previous literature, but generally switched to using 'cross-over experience':

“Therefore, synesthesia might provide a unique window into how the brain’s constructive processes can generate additional, conscious content, in cross-over experiences, often across modalities, going all the way down to the level of sensory phenomenology.”

We adjusted throughout the manuscript accordingly.

(2) I would not recommend focusing the introduction on the problem of qualia; this is a much more general and complex question than the one addressed in the study; the space of the introduction may be better used to present the actual object of study, giving a better picture of the synesthetic phenomenon and of previous work aimed at characterising it (behavioural, including PA scores and consistency measures, and neuroimaging). It is important to discuss how the pupillometric approach differs from the previously adopted neuroimaging techniques and what it can add to those.

We agree that qualia is a very general and complex question. However, we respectfully disagree that this complex question is not the object of the study. What is remarkable about synesthesia is not the presence of an additional perceptual association per se, but the presence of a specific perceptual experience. As illustration, think of a test where an unconscious color association to the word 'banana' was tested. While a generic 'yellow' could semantically be linked and would likely be obtained in the (e.g. priming) experimental results, a follow-up question of picking on a color wheel the exact shade of yellow to this association, or describing the perceptual sensation of the color, would be non-sensical to the participants.

This sharply contrasts with the current study: synesthetes, but not non-synesthetes, indicate a perceptual sensation of additional colors, and subsequently indeed the sensory properties of this percept (experienced brightness) affects the objective reflection of this sensation (pupil size) in synesthetes but not in non-synesthetes. In our view, the presence of additional qualia is key in understanding what sets synesthetic apart from non-synesthete associations, including so-called cross-modal correspondences (unconscious consistent associations across modalities, common to us all). We even believe that the reported qualia is what makes synesthesia so interesting in the first place. We now more clearly explain this link to qualia better in the introduction.

"The most remarkable aspect of synesthesia is the subjective perceptual phenomenology of the induced colors, setting these sensations apart from color memory, thought, or amodal association. The contrast between synesthetes and non-synesthetes can thus offer an interesting doorway into examining qualia, the subjective perceptual phenomenology or first person (what's-it-like) perspective."

We also improved the explanation of the synesthetic phenomenon, including a more detailed characterisation of behavioural measures (including consistency scores) and added neuroimaging studies. These changes have been incorporated into the text in response to previous comments (point 1- reviewer 1).

Please note that we have chosen not to include more detailed discussion of PA scores. Our results show a trend but do not allow for a conclusive interpretation on PA scores, and we feel that placing greater emphasis on this topic might therefore be confusing or even misleading. Still, it would be a very interesting topic for follow-up research to examine how alterations in characteristics of the synesthetic experience influence pupil responses.

The different synesthesia types all share the defining characteristics of an additional conscious and consistent experience. Synesthetes can verbally report their additional experience, and synesthetic sensations can be measured in behavioral paradigms such as the ’synesthetic Stroop’ effect, or brain activation patterns in sensory cortex [15]. Furthermore, test-retest paradigms show how synesthetic, but not non-synesthetic associations are highly specific and consistent [16-18]. Thus, over the past decades, research has established synesthesia as a ’real’ condition that can reliably be identified using behavior, neurophysiology, and neuroimaging [11, 13, 15–21]. The most remarkable aspect of synesthesia is the subjective perceptual phenomenology of the induced additional sensation, i.e., color in grapheme-color synesthesia. This sets synesthetic sensations apart from (color) memory, thought, or amodal association. Synesthesia can thus offer an interesting doorway into examining qualia, the subjective perceptual phenomenology or first person (what’s-it-like) perspective.

We now discuss the pupillometric approach as it differs from the previously adopted neuroimaging techniques as follows:

“Compared to neuroimaging studies [12,15,51], pupillometry may offer a more direct window into synesthetic phenomenology, as the directionality between pupil light reflex and perceived brightness is straightforward. Finally, improved understanding of the underlying processes can be obtained by contrasting responses to perceived versus actual (physical) brightness, given that the pupil light reflex is a well-characterised reflex arc involving few inferential steps.

This adds to the explanation that was already present on how the current approach differs from previous techniques, and what it can add to those techniques:

"Instead, current paradigms capturing synesthesia employ objective measures, but fail to capture its phenomenology [16, 17, 21, 23]."

(3) There are a few typos and word repetitions.

Many thanks – we identified typos and repetitions after another set of careful reads and hope to have eradicated them completely now.

Reviewer #2 (Recommendations for the authors):

I am overall very supportive of this work, but addressing the following points may enrich it further:

(1) Paragraph 2.2.1. Here, models do not seem to compare synesthetes versus controls but rather assess the effects of interest separately in the two groups. The fact that experimental effects are significant in synesthetes, but not in controls, does not tell us much about differences between groups. Controls (e.g., Figure 3) do show a similar trend, albeit clearly smaller. There is one passage in which this issue appears to be tackled (page 10): "Critically, in an LME ran on synesthetes and controls and using only graphemes and the interaction of group and lightness as predictors, we found lightness to predict pupil size in synesthetes (t = -2.754, p = 0.006), but not controls (t = -1.134, p = 0.257)." But I am not sure that the reported statistics belong to the interaction - they seem to refer to the lightness effect within each group, not the difference.

This is an important point, power for between-group comparisons is inherently limited for n = 16 per group (while still feasible for overall responses, things become trickier when less trials remain). A simple model of pupil ~ grapheme + group * lightness_scaled + (1 | participant) shows no significant interaction (despite one group showing the effect and the other not showing the effect significantly). The additional negative effect for group is in line with the effort-related effect reported later in the manuscript. Where does this leave us? Based on the lightness responses alone, the group difference can be characterized as a quantitative distinction, but the degree in which it is also a qualitative distinction cannot clearly be determined from current data. We revised the manuscript to make sure that such an interaction is not implied/ point to the absence of the significance of that interaction.

The sensory nature of synesthetic color is supported by within-synesthete analyses, where coupling strength parametrically modulates the lightness-pupil relationship in a theoretically predicted manner. Importantly, the effort-related findings provide a complementary and statistically robust group comparison: synesthetes and controls performing the identical colorreporting task showed significantly different pupil dilation rates, directly demonstrating that the two groups differ in how they access color information. Together, these two independent pupillometric signatures, one tracking perceptual quality, one tracking effort, converge on the same conclusion and mutually reinforce the interpretation that synesthetic color constitutes genuine sensory phenomenology.

Author response image 3.

We now make this more explicit in the manuscript as follows:

“We found significant modulations of pupil size by the lightness of the grapheme's synesthetic color - sustained and in the to-be-expected time window. Specifically, the pupil constricted more for brighter reported colors, and dilated more for darker reported colors, as predicted (Average pupil size 800-4000ms, t = -3.601, p < 0.001). In an LME ran for synesthetes and controls and using only graphemes and lightness as predictors, we found lightness to predict pupil size in synesthetes (t = 2.844, p = 0.004), but not controls (t = 0.606, p = 0.544). However, when taking group as interacting factor in a joint LME, there was no interaction of lightness and group (t = -0.949 p = 0.342).”

and

“For controls a separate model was run, now without the PA score as predictor (not assessed for controls). Neither lightness (t = -0.815, p = 0.415), coupling strength (t = 0.438, p = 0.661), nor their interaction gained significance (t = -1.058, p = 0.290; all for average pupil size between 800 ms and 4000 ms). Critically, we also ran a LME with the three-way interaction of coupling strength, group, and lightness (Wilkinson notation: pupil = grapheme + group + lightness * group + coupling strength * lightness * group + (1 | participant)). This analysis revealed a significant three-way interaction between lightness, coupling strength, and group (F = 3.86, p = .021), indicating that the lightness × coupling strength effect on pupil size was not equivalent across groups. Decomposing this interaction by group, the lightness × coupling strength slope was significant in synesthetes (t = 2.59, p = .010) but not in controls (t=-1.01, p=.311), suggesting that reported lightness and its coupling strength were more consistently related to pupil size in synesthetes than in controls. Note however, that this decomposition does not directly test whether the two slopes significantly differ from each other, however. Lastly, pupil size was marginally larger in controls than in synesthetes (t = 1.94, p = .062; see later sections for more in-depth analyses)”

(2) The authors choose to analyze pupil size in arbitrary eye tracker units. This is fine, although I would recommend assessing and reporting whether the average pupil size (e.g., during the baseline) is roughly comparable between groups. The size of the effects may be difficult to compare between groups in the presence of very different baseline pupil size.

Please see Author response image 4 for Baseline pupil sizes per group in millimeters. There were no differences between groups.

Author response image 4.

F2, 45) = 0.707, p = 0.499 (One-way Anova).

We now write:

“Baseline pupil sizes did not differ between groups (F(2, 45) = 0.707, p = 0.499).”

We agree with the reviewer that millimeters are a more intuitive measure and updated all figures throughout manuscript and supplementary materials accordingly. We also briefly added to signal processing that this conversion was applied.

“Pupillary data were transformed from arbitrary eyelink units to millimeters using a conversion factor obtained with an artificial eye (see Hayes & Petrov, 2016).”

Hayes, T. R., & Petrov, A. A. (2016). Mapping and correcting the influence of gaze position on pupil size measurements. Behavior research methods, 48(2), 510-527.

(3) If I understand correctly, the main task counted 120 trials overall (12 per digit). It seems, however, that only 3 and 4 participants remained with at least 50 trials (or 25 per median split by lightness) after preprocessing. This appears to be quite a massive data loss: is there a reason behind it? Please also clarify: the overall percentage of discarded trials; whether the median split by lightness was computed on all responses or only on those of the remaining, valid trials.

This is an important point for clarification indeed. The exclusion of participants in Figure 3 applies only to that particular visualization, not to the statistical analyses. The linear mixed effects models (LMEs) used all available valid trials from all participants, with no participant-level exclusions. The figure-specific threshold (≥25 trials per median-split bin) was applied purely for display clarity, as plotting participants with very few trials per bin would produce unreliable/noisy and thus visually misleading traces (as we note in the figure caption and point readers to Supplementary Figure 1, which shows the same visualization without any exclusions).

Since the paradigm required participants to repeat discarded trials until 120 valid trials were collected, all participants thus contributed exactly 120 valid trials to the analyses. There was therefore no data loss at the analysis level for the LME that is central to the claims of the manuscript (albeit more complex to grasp than the t-tests between bins).

Why were there sometimes so little trials per brightness bin?

First, participants differed in how dark or bright (synesthetic or forced-report) colors were overall, meaning that differing proportions thereof would fall above or below the 0.5 cutoff that overall, well represented the sample (but not necessarily every single participant). Note that this median split was not performed per individual but across all color reports to allow an apples-to-apples comparison.

Second, participants often reported colors that differed in Hue and Saturation, but not Lightness. This is in line with synesthetes picking certain colors more often than others, as compared with non-synesthetes (Rouw & Root, 2019; Ward et al., 2025).

We now include a new Supplementary Figure that visualizes responses on the Hue and Saturation dimensions of HSL space for both synesthetes and controls; fully saturated reports appear on the outer edge. We refer to the supplementary figure in the caption of Figure 2 as follows:

"See Supplementary Figure 1 for color reports on the hue and saturation axes.”

Rouw, R., & Root, N. B. (2019). Distinct colours in the ‘synaesthetic colour palette’. Philosophical Transactions of the Royal Society B: Biological Sciences, 374(1787).

Ward, J., Maciel, S., Rouw, R., Simner, J., & Root, N. (2025). Synaesthesia is linked to differences in music preference and musical sophistication and a distinctive pattern of sound-color associations. Psychology of Music, 53(3), 453-473.

Minor points:

(1) "Building on this evidence, we hypothesized that the cross modal color phenomenology in synesthesia can, if truly sensory in nature, could likewise be (...)" -> may need rephrasing (can/could).

Many thanks, fixed.

(2) Caption of Figure 1: "Block 2 (synesthetes only): a colored disk and gray central patch, matching the average indicated color per digit, and the number and luminance of pixels of said digit were presented to assess externally triggered light responses." -> I find this sentence a bit hard to follow; perhaps consider rephrasing it.

Agreed, we rephrased to:

Block 2 (synesthetes only): a colored disk was presented, colored according to the synesthete's average indicated color for that digit. At its center sat a gray patch matching the luminance and pixel area of the original digit from Block 1, together allowing assessment of externally triggered light responses.

(3) Figure 2 b: Consider truncating the y-axis to 1 if that improves the visualization.

We adjusted the axis accordingly and added a bit more detail in the caption for the interpretation of the measure.

(4) Caption of Figure 3 points to "see Supplementary Figure 1", but it should probably be SF2.

Many thanks for spotting, all references to supplementary figures have been checked and are corrected now.

Elvio Blini

Reviewer #3 (Recommendations for the authors):

(1) As a minor comment, there are some terms that felt overused in the manuscript. For example, the words "extraordinary" and "exceptional" were used multiple times throughout. I believe I understand the authors to mean them in their descriptive sense (i.e., outside the realm of typical experience), but in context, those words make it seem like they are touting their own experiment as "exceptional" or "extraordinary," which I don't believe was their intention.

We agree. We removed words such as exceptional and extraordinary when they do not directly refer to the sensation throughout the manuscript (which is indeed how we intended to use it). We hope that this removes unnecessary and convoluting hyperbole.

(2) It seemed counterintuitive to me that the color consistency score would be reverse-coded. In this case, the scores actually seem to indicate inconsistency, rather than consistency. Perhaps the raw scores can be inverted for a more intuitive interpretation that aligns with the terminology. I understand that they were following a previous publication in their method (Rothen et al., 2013).

This manner of coding is counter-intuitive indeed. However, there are both logical and practical reasons to this approach. Importantly, this is indeed the standard way of reporting color consistency in synesthesia research (Carmichael et al., 2015; Eagleman et al., 2007; Root et al., 2025; Rothen et al., 2013). The calculation is based on a simple logic; a higher number reflects a larger distance in color space. An additional advantage is the clear and intuitive zero- reference: a score of zero implies choosing the exact same color. Finally, it intuitively reflects the distinction between synesthetes and non-synesthetes; there is by definition little variation across synesthetes (visualized at the bottom of the graph), then a 'cut-off line' (if consistency is used as diagnostic tool), and then the height of the range shows how large the range in consistency is, in that particular sample of non-synesthetes. In a way we therefore inherit a confusing definition/standard, but changing it would lead to new confusion instead. We now specifically clarify this in the caption as follows:

“Note that higher consistency is reflected in lower color distance, hence lower values [17].”

Carmichael, D.A., Down, M.P., Shillcock, R.C., Eagleman, D.M., Simner, J., 2015. Validating a standardised test battery for synesthesia: does the synesthesia battery reliably detect synesthesia? Conscious. Cogn. 33, 375–385

Eagleman, D.M., Kagan, A.D., Nelson, S.S., Sagaram, D., Sarma, A.K., 2007. A standardized test battery for the study of synesthesia. J. Neurosci. Methods 159 (1), 139–145.

Root, N., Chkhaidze, A., Melero, H., Sidoro -Dorso, A., Volberg, G., Zhang, Y., & Rouw, R. (2025). How “diagnostic” criteria interact to shape synesthetic behavior: The role of self-report and test–retest consistency in synesthesia research. Consciousness and Cognition, 129, 103819.

Rothen, N., Seth, A.K., Witzel, C., Ward, J., 2013. Diagnosing synaesthesia with online colour pickers: maximising sensitivity and specificity. J. Neurosci. Methods 215 (1), 156–160.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This work compiles a comprehensive atlas of ncORFs across mammalian tissues and cell types, derived from reanalysis of ~400 public ribosome profiling datasets. The authors then evaluate cross-species conservation and functional signatures, proposing that evolutionarily ancient ncORFs tend to have higher translation potential, stronger expression, and closer relationships with canonical coding sequences.

Strengths:

In general, the study provides a large-scale and timely resource of annotated ncORFs, which could be broadly useful for the community. The authors collected ~400 public ribosome profiling datasets for annotations of ncORFs, which, to my best knowledge, is the largest collection of data for such a purpose. The catalog could facilitate future investigations into ncORF biology and broaden understanding of the coding potential of the "non-coding" genome.

We thank the reviewer for the positive evaluation of our manuscript and for recognizing the significance of our contribution.

Weaknesses:

Based on the ncORF catalog, some of the analyses were not properly done. Some of the results are descriptive.

(1) Bias and representations of the data source. Public ribo-seq datasets are unevenly distributed across tissues and cell lines, raising concerns about heterogeneity and underrepresentation of certain contexts. This may limit the generalizability of the catalog.

We agree with the reviewer that the uneven distribution of public Ribo-seq datasets across tissues can inevitably introduce bias in the ncORF composition of our catalog. This bias is likely more pronounced in humans due to the narrower tissue coverage. We have addressed this point in the Discussion section of the revised manuscript.

(2) The discussion on modular domains of ncORFs is unclear, and the claim that they may originate via TErelated mechanisms is not well supported. Stronger evidence or clearer reasoning is needed.

We thank the reviewer for highlighting this point. We have revised the manuscript to more clearly explain the rationale behind our analysis of ncORF modular domains and have adopted more cautious language regarding their potential transposable element–related origins, limiting interpretations to what is directly supported by the data.

(3) The conservation comparisons are not fully convincing. Figure S7 shows only mild differences between ncORFs and CDS, and statistical significance is not clearly demonstrated.

Comparisons with other non-coding RNAs should be added, and overlapping sequences between ncORFs and CDS should be excluded to avoid bias.

We thank the reviewer for this comment and apologize for the lack of clarity in the original figure. Both CDSs and ncORFs show significant deviation from zero Gnocchi scores (two-sided Wilcoxon signed-rank tests), which is now stated explicitly in the revised legend and text. CDS-overlapping ncORFs were already excluded in the original analysis; this has been clarified to avoid confusion.

As suggested, we have added lncRNAs for comparison. ncORFs display modestly higher Gnocchi scores than lncRNAs, and this difference persists when restricting the analysis to lncRNA-derived ncORFs and their corresponding full-length lncRNAs (see revised Fig. S7). These additions strengthen the conservation comparison while controlling for transcript context.

(4) Figure 3 indicates that some ncORFs are subject to evolutionary constraints. This is not surprising. The authors should provide further analyses on more detailed features of these "conserved" ncORFs vs. the "non-conserved" ones. Some pretty informative works have been done in Drosophila, worms, mice, and humans. Figure 3 suggests some ncORFs are under evolutionary constraint, but this is not unexpected. More granular analyses contrasting "conserved" versus "non-conserved" ncORFs would be informative. In fact, small ORFs, especially uORFs, have been extensively studied for their functions and cross-species conservation. The authors should explicitly show what is new here in their analyses.

We thank the reviewer for this insightful comment. We agree that cross-species conservation of ncORFs (particularly uORFs) has been extensively investigated in prior studies, including our own.

However, most prior analyses have focused on conservation of start codons or overall ORF integrity, which does not distinguish selection acting on translational activity from selection acting on the encoded peptide sequence itself. In contrast, our analysis leverages codon-level periodic PhyloP signals across the full ORF. The observed three-nucleotide periodicity is consistent with selective constraint at the amino acid level, rather than merely preservation of initiation sites or translational potential. Furthermore, our newly developed branch-length statistic uncovers lineage-restricted conservation patterns among ncORFs, enabling resolution of evolutionary dynamics not captured by conventional conservation metrics.

Thus, while the existence of conserved ncORFs is not unexpected, the conceptual advance of our study lies in demonstrating that a subset exhibits coding-like evolutionary constraint consistent with selection on their peptide products, as well as revealing lineage-specific conservation patterns. We have clarified this distinction in the revised Discussion.

(5) Translation levels are reported using RPF counts. However, translation efficiency (normalized by RNA expression) is a more appropriate measure to account for expression heterogeneity.

We agree that translation efficiency (TE), which normalizes ribosome footprint counts by RNA abundance, is in principle an appropriate metric. We initially calculated TE and compared ncORFs with CDSs. However, we found that TE estimates for short ncORFs were substantially inflated by RPF enrichment near start and stop codons, leading to unstable and potentially misleading values.

For CDSs, this bias is commonly addressed by excluding the first and last 10 to 20 codons when quantifying RPF density. This strategy is not feasible for ncORFs because of their short length. We therefore used RPF counts in the final analysis, applying stringent positional filtering. Only RPFs whose P sites fall within the ORF body, excluding start and stop codons, were counted. RPFs overlapping the ORF but with P sites outside the annotated frame, likely derived from adjacent ORFs or initiation or termination pausing, were excluded.

TE and RPF counts both measure translation but capture different aspects. TE reflects ribosome density relative to transcript abundance, whereas RPF counts quantify overall ribosome engagement. Given the short lengths of ncORFs, count-based quantification provides a more robust and conservative estimate of their translational activity.

(6) The correlation analyses between ncORF translation levels and PhyloCSF are confusing and largely descriptive. These sections need sharper framing and clearer conclusions.

We thank the reviewer for this comment. We agree that the original presentation lacked clear framing. The relationship between PhyloCSF scores and mean ncORF translation levels across tissues is influenced by both evolutionary age and tissue specificity. Older ncORFs with higher coding potential tend to exhibit stronger tissue-restricted expression. As a result, their mean translation levels across all tissues appear lower, not because they are weakly translated, but because their translation is concentrated in specific tissues. This point is addressed in the revised manuscript.

(7) Public ribo-seq datasets, generated by different research labs, are known for their strong batch effects. Representations of tissues and cells are also very unbalanced. Therefore, the co-translation analysis between ncORFs and canonical CDS is not well controlled. This should be done by referring to a recent large-scale ribo-seq meta-analysis (Nat Biotechnol. 2025. doi: 10.1038/s41587-025-02718-5).

We thank the reviewer for highlighting this important study and for raising concerns regarding batch effects and tissue imbalance in public Ribo-seq datasets. We are aware that public Ribo-seq data generated by different laboratories are subject to substantial batch effects. During the ncORF annotation phase, we applied stringent quality-control criteria to minimize technical variability. For the co-translation analysis, inclusion criteria were relaxed to increase tissue and cell-type coverage. To partially mitigate representation bias, libraries derived from the same tissue or cell type were merged when quantifying ORF translation levels, thereby reducing overrepresentation from heavily sampled contexts.

Nevertheless, we acknowledge that these measures cannot completely eliminate batch effects or imbalance inherent to public datasets. We agree that co-translation analysis would benefit from uniformly processed, high-quality datasets generated under standardized protocols with balanced tissue representation, representing a valuable direction for future research.

Reviewer #2 (Public review):

Summary:

Chang et al. attempted to analyze a large number of ribo-seq datasets through a standardized pipeline, identifying novel non-canonical ORFs and elucidating their evolutionary and expression characteristics.

Strengths:

(1) The datasets analyzed by the authors are sufficiently comprehensive, and the use of standardized pipelines ensures excellent analytical consistency.

(2) Their analyses of ORF evolution and co-expression further deepen our understanding of these ORFs.

We thank the reviewer for the positive evaluation of our manuscript. It is encouraging to know that the analytical framework was found to be sound and appropriate.

Weaknesses:

(1) The authors primarily conducted analyses through bioinformatics, lacking sufficient wet-lab experimental evidence.

We thank the reviewer for this comment and acknowledge this limitation. We agree that functional validation through wet-lab experiments would provide important mechanistic insight into individual ncORFs. However, this study was designed as a systematic, genome-wide computational analysis to characterize translated ncORFs across species and tissues. Our objective was to define global patterns of translation, conservation, and structural features using large-scale datasets. Given the breadth and scale of these analyses, experimental validation of specific ncORFs falls beyond the scope of the current study. We have clarified this point in the dicussion and noted that our results provide a framework for future targeted experimental investigation.

(2) Regarding the evolution of non-canonical ORFs, a considerable amount of prior work already exists. The authors need to further clarify what new insights and discoveries they have made based on the analysis of such a large dataset.

We thank the reviewer for this suggestion. Similar concerns were also raised by Reviewer #1. In response, we have revised the Discussion to more clearly delineate the conceptual advances enabled by our large-scale dataset.

Recommendations for the authors:

Reviewing Editor Comments:

Several aspects of the downstream analyses would benefit from additional refinement. The heterogeneity and tissue imbalance inherent in public Ribo-seq datasets introduce potential biases in ncORF detection and inferences about co-translation. Given the breadth of the dataset, it would also be informative to quantify how consistently the newly identified ncORFs are detected across samples-distinguishing those observed broadly across tissues, those enriched in specific contexts, and those detected in only a few datasets. Such stratification would help differentiate reproducibly translated ORFs from candidates requiring further validation.

We thank the editor for the helpful comments. We agree that heterogeneity and tissue imbalance in public Ribo-seq datasets can influence ncORF detection and downstream interpretations. We have added discussion of this limitation in the revised manuscript.

Detection of ncORF translation depends not only on biological activity but also on sequencing depth and data quality. Although all ncORFs reported here were reproducibly identified by multiple methods across independent libraries, we agree that those detected in a larger number of datasets represent stronger candidates for functional validation. Accordingly, we now report the number of methods and libraries in which each ncORF was detected in the final catalog (Supplementary Table 3). Overall, 22.3–26.3% of ncORFs were detected in more than 10 libraries, whereas more than half were observed in only two to five libraries (Fig. S1B), enabling clearer stratification of broadly translated versus more context-specific candidates.

Some evolutionary and functional interpretations are largely descriptive or consistent with established findings for small ORFs, and the authors should more clearly articulate what is novel in their analyses. The criteria separating "young," "old," and "ancient" ORFs require clearer definition, and conservation analyses would be strengthened by improved statistical rigor and explicit exclusion of regions overlapping annotated coding sequences. Evidence for modular domain features or transposable element-related origins is limited and warrants either stronger support or more cautious framing. Proteomics validation is currently minimal and could be substantially reinforced using existing public MS resources.

We thank the reviewer for these constructive comments. In the revised manuscript, we more clearly delineate the novel insights derived from our evolutionary analyses of ncORFs, distinguishing them from established findings on small ORFs.

We have clarified the criteria used to classify ORFs by evolutionary age in figure 6E and refined the terminology describing “young,” “old,” and “ancient” categories to ensure precise definition. The conservation analyses have been strengthened through more rigorous statistical treatment and by explicitly excluding regions overlapping annotated coding sequences.

With respect to modular domain features and potential transposable element–related origins, we have adopted more cautious language and limited our interpretations to what is directly supported by the data. Finally, we acknowledge that current proteomic validation remains limited and have clarified this point in the manuscript while outlining the potential for future integration of large-scale public mass spectrometry datasets in Discussion.

The authors additionally report an interesting observation that many ncORFs on mRNA co-translate with the main CDS of the same gene. Because canonical models often posit that uORF translation suppresses downstream CDS translation, further analysis would be valuable. In particular, it would be useful to determine whether patterns of co-translation differ among ORF types or evolutionary categories and to discuss possible regulatory mechanisms underlying these relationships.

We thank the editor for this thoughtful comment. As noted in our response to Reviewer #2, uORF–CDS co-translation does not contradict the canonical model in which uORFs repress downstream CDS translation. Co-translation reflects concurrent ribosome occupancy, whereas repression concerns the fraction of initiating ribosomes that ultimately reach and translate the CDS. Following the editor’s suggestion, we further examined whether co-translation patterns differ across ORF types or evolutionary categories. We found that ncORFs co-translating with their corresponding main CDSs are predominantly uORFs. However, these uORFs do not show statistically significant differences in conservation metrics or evolutionary age compared with other non-overlapping uORFs. Thus, we did not detect clear subtype- or age-specific distinctions among co-translating ncORFs. We have clarified these analyses in the revised manuscript.

Addressing these points would enhance the precision, interpretability, and robustness of the study's conclusions.

Reviewer #2 (Recommendations for the authors):

(1) The authors developed and refined a standardized pipeline to analyze nearly 400 ribo-seq datasets, identifying over 10,000 novel non-canonical ORFs in both human and mouse samples. Given the scale of this analysis, it is intriguing to consider how many of the newly identified non-canonical ORFs are consistently detected across multiple sample types (conservatively expressed ORFs), how many are restricted to specific tissues/ or tissue-specific ORFs), and how many were detected in only a single or very few samples (ORFs requiring further validation). Providing these data could offer new insights into understanding ORF translation.

Thanks for this constructive suggestion. This information has been presented in the revised Supplementary Table 3 and in a newly added supplementary figure (Fig. S1B), which together provide a clearer overview of ncORF detection consistency and context specificity.

(2) The authors' validation of MS data lacks specific details in the paper. Regarding the MS-supported ORF mentioned in Lane 117, which dataset's MS data is being referenced? Or does it refer to the content in Reference 20? At present, substantial research exists in both public general proteomics studies (e.g., CPTAC) and MS investigations targeting non-canonical ORFs. We recommend the authors incorporate additional MS data or public MS-based databases to strengthen validation in this area (PMID: 34129944, 39794466, 37823596，39413795).

We thank the reviewer for this comment and for the helpful suggestions. The MS-supported ORFs mentioned in line 117 refer to the compilation reported in Reference 20, which integrates evidence from multiple independent proteomics studies. In addition, we examined MS-supported ORFs curated by GENCODE and PeptideAtlas, which are shown in Fig. 1E.

We agree that incorporating additional MS datasets would further strengthen validation of ncORFs. Studies cited by the reviewer and recent community efforts such as the GENCODE and PeptideAtlas analyses (PMID: 39314370) provide valuable examples in this direction. However, performing a comprehensive reanalysis of more than 95,000 public human MS runs is computationally demanding and currently infeasible for our group given resource and funding constraints.

To our knowledge, ongoing community-wide initiatives are working toward more comprehensive catalogs of translated human ncORFs. Large-scale, exhaustive MS searches will be particularly effective once a community consensus annotation framework for ncORFs is established. We have added discussion of these limitations and future directions in the revised manuscript.

(3) The authors classified ncORFs into three groups-"Ancient," "Young," and "Old"-based on their origin nodes. However, both the "Young" and 'Old' groups appear to be "mammalian-specific," yet the specific criteria for their division remain unclear. It is recommended to more clearly define in the figure legend or main text how "Young" and "Old" are categorized (e.g., based on specific evolutionary nodes or distance thresholds from nodes to the end) to avoid reader confusion.

In Fig. 5, “old” and “young” were intended as qualitative descriptors of relative evolutionary age based on the position of ncORF origination nodes along the phylogeny, as indicated on the x-axis. They were not meant to represent discrete categories. To avoid confusion, we have revised the manuscript to use “older” and “younger” throughout when referring to relative age differences. A binary classification is used only in Fig. 6E, where ncORFs are grouped into ancient (pre-mammalian) and younger (mammalian-specific) categories. This distinction is clearly defined in both the main text and the corresponding figure legend.

(4) The authors observed an intriguing phenomenon: ncORFs on mRNA tend to co-translate with the main CDS of the same gene. However, the conventional view holds that uORF translation often inhibits the translation of the main CDS. I suggest the authors could refine their analysis in this section further. For instance, do different types of ORFs or ORFs at different evolutionary levels exhibit distinct levels of cotranslation with the main CDS? Additionally, while observing this phenomenon, the authors should also propose hypotheses regarding the regulatory mechanisms involved in these processes.

We thank the reviewer for these constructive suggestions. After excluding CDS-overlapping ORFs, we identified 258 human and 128 mouse ncORFs that co-translate with their corresponding main CDSs. With the exception of 10 human dORFs, all remaining cases were uORFs. We compared these cotranslating ncORFs with other non-overlapping uORFs and dORFs but did not detect statistically significant differences in evolutionary age and conservation metrics. Because no clear distinguishing features emerged, we did not include these results in the manuscript.

Importantly, the observation of uORF–CDS co-translation does not contradict the established repressive role of uORFs. Co-translation reflects concurrent ribosome occupancy, whereas repression concerns the proportion of initiating ribosomes that ultimately translate the CDS. For example, if two ribosomes initiate within a given interval and one translates the uORF while one translates the CDS, CDS output is reduced by 50% relative to a uORF-free transcript. If four ribosomes initiate under the same repressive regime, two may translate the uORF and two the CDS. In this case, absolute translation of both ORFs increases, while the fractional repression remains unchanged. Thus, co-translation is compatible with a regulatory model in which uORFs reduce CDS translation efficiency without abolishing it. This has been clarified in the revised manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) All outcomes are attributed specifically to L6b neurons, but the genetic manipulation is not specific to L6b neurons. The authors acknowledge this as a limitation, but in my view, this global manipulation is more than a limitation - it affects the overall interpretations of the data. The Hoerder-Suabedissen et al., 2018 paper shows sparse, but also dense, expression of Drd1a+ neurons in brain regions outside of the L6b. Given this issue, the results are largely overstated throughout the paper.

We appreciate the reviewer’s careful reading and concern that some of our statements may have overstated the implications of our data. The Drd1a Cre mouse model used (FK164) has a relatively selective expression of Drd1a Cre in cortex, but indeed some expression is seen subcortically. This is an acknowledged limitation which is now explicitly addressed in the revised manuscript.

(2) It is not clear to me that the "silencing" of Drd1a+ neurons was verified.

In our previous publications, we showed confirmation of the loss of regulated synaptic vesicle release from the Cre-positive neuronal population (Marques-Smith et al., 2016; Hoerder-Suabedissen et al., 2018; Messore et al., 2024). This has now been described in the revised manuscript.

(3) There were various discrepancies (and potentially misattributions) between the stated significant differences in Supplementary Table T1 data and Figure 3a & S2 spectral plots. This issue makes it difficult to effectively evaluate the main text and stated outcomes.

We thank the reviewer for their careful attention to the statistical analyses and for noting the inconsistencies in how the results of the spectral analysis were presented: in the text we described two-way ANOVAs with according posthoc tests but in the figures significance markers were positioned based on multiple t tests. We have now carefully revised the spectral results and implemented a consistent approach in statistical reporting and spectral plots. We have updated Supplementary Table T1, Figure 3a and S2 to ensure that all statistics are presented consistently throughout the manuscript, i.e. with two-way ANOVAs and accompanying posthoc tests. Please note that we performed all spectral analyses in the range between 0.5 and 128 Hz (excluding the range between 49-51.5 Hz due to electrical noise from the power grid) but only plot the range between 0.5-30 Hz as the spectral bands most relevant for sleep neurophysiology are contained in this range.

Related, the authors stated that post hoc comparisons of EEG spectral frequency bins were not corrected for multiple testing. Instead, significance was only denoted if changes in at least two consecutive frequency bins were significant. However, there are multiple plots in which a single significance marker is placed over an isolated bin (i.e., 4c, 6, S5, S6). Unless each marker is equivalent to 2 consecutive frequency bins, these markers should be removed from the plots. Otherwise, please define the frequency and size of these markers in the main text.

In line with the previous comment, we have adjusted markers to reflect the results from posthoc tests after two-way ANOVAs.Please note that Figure 6 and the related supplementary figures S5 and S6 have now been removed from the manuscript, as careful re-analysis indicated that the sample size was too low to support a strong conclusion regarding the comparison of orexin effects between genotypes. We stated in the text that we would only include posthoc significance when at least two consecutive bins were significant, but this was indeed not supported in our figure, where each marker reflects one 0.25 Hz bin. We have now adjusted our code to ensure that only markers are plotted when at least two consecutive bins are significant in bin-wise posthoc comparisons.

(4) A rainbow color scale, as in Figure 3, we've now learned, can be misleading and difficult to interpret. The viridis color scale or a different diverging color scale are good alternatives.

Thank you for pointing this out, we have adjusted the colour scale.

(5) How much time elapsed between vehicle/orexin A & B infusions?

There were 2-4 non-infusions days between infusions. We have added this information to methods.

(6) For Figure 6, there are statistical discrepancies between the main text and the plots (pg. 10):

(a) The text claims post hoc differences for relative ORXA frontal EEG, but there are no significance markers on the plot.

(b) The text states that there were no post hoc differences for the relative ORXA occipital EEG, but significance markers are on the plot.

(c) The main test for the relative ORXB frontal EEG was not significant, but there are post hoc significance markers on the plot.

(d) For relative ORXB occipital EEG, there are significant markers on the plot outside of the stated range in the text.

We agree with the reviewer, and we decided to exclude this figure from the manuscript as the sample size for some key comparisons was too low to support any strong conclusions and therefore presenting this analysis is potentially misleading. We explain the rationale for excluding this analyses in the revised manuscript.

(7) Some important details are only available in figure captions, making it difficult to understand the main text. For example, when describing Figure 3c in the main text on page 7, it is not clear what type of transitions are being discussed without reading the figure caption. Likewise, a "decrease," "shift," and "change" are mentioned, but relative to what? Similar comment for the EEG theta activity description on pages 7 - 8. Please add relevant details to the main text.

We have adjusted the wording in the main text to reflect more precisely which comparisons are shown in the figures.

(8) Statistical comparisons for data in Figure 3e, post hoc analyses for data in Figure S7a-b REM data, and post hoc analyses for Figure S7c (not b) occipital EEG should be included to support differences claims. Please denote these differences on the respective plots.

Please note that the previously named Supplementary Figures S5 and S6 have been removed from the manuscript, and that the Supplementary Figure S7 in this comment refers to the figure currently named Supplementary Figure S5.

We have added the statistical comparisons for Figure 3e, Supplementary Figure S5A and Figure S5b to the results section. In Figure S5c, there was an overall genotype difference, but there was no significant time x genotype interaction, so we have not performed posthoc tests and did not plot posthoc significance markers for this figure. We have adjusted the wording in the results section to make this clearer. We have adjusted the reference to the figure S5c which was incorrect, thank you for your careful attention.

(9) In the subsection titled "Layer 6b mediates effects of orexin on vigilance states (pg. 8)," there does not seem to be any stated differences between control and L6b silenced mice. A more accurate subtitle is needed.

We agree with the reviewer and the title of this sub-section has now been changed accordingly.

Reviewer #2 (Public review):

Weaknesses:

(1) Although the authors used a highly selective approach to silence layer 6b neurons, the observed changes in EEG oscillations cannot be solely attributed to layer 6b neurons because of the ICV route for orexin administration.

We thank the reviewer for this important comment. The ICV route of orexin administration cannot guarantee that only cortical Drd1a-Cre–expressing neurons are reached by orexin, and the Drd1a-Cre driver line is highly selective but not entirely specific for layer 6b neurons (see also response to reviewer #1, comment 1). We have therefore changed the wording of the stated effects and addressed this consideration in the Limitations section of the manuscript. Please note that, as mentioned above, Figure 6 has now been excluded from the manuscript.

(2) The rationale for using only male rats is not provided.

We thank the reviewer for highlighting this omission. We now provide the rationale for using only male mice in the methods section as follows: “In the current study, only male mice were used, because our experimental protocol precluded the possibility of accurately monitoring the oestrous cycle, which has marked effects on brain activity, arousal and vigilance states. We therefore decided to use male mice only for the current study but are planning to use both sexes in future work.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Better descriptions of L6b connectivity will improve clarity in the second paragraph of the Introduction (pg. 3). For example, it is not explicitly stated that L6b projects to L5 before the authors describe L5. Therefore, the L5 description seems irrelevant.

We thank the reviewer for this request for clarification. We mention the connectivity between L6b and L5 because L5 pyramidal neurons have recently been found to play a key role in sleep-wake regulation (Krone et al., Nat. Neurosci. 2021; Honjo et al., 2025; Wasilczuk et al, 2025; Krone et al., 2025). We have now amended the corresponding section of the introduction to emphasise the potential functional relevance of this connection as follows:

“L5, the major output layer of the cortex, is also bidirectionally communicative with higher order thalamic nuclei (Hoerder-Suabedissen et al., 2018) as well as layer 5 pyramidal neurons (Zolnik et al., 2024). Since several subtypes of L5 pyramidal neurons have recently been shown to play important roles in distinct aspects of sleep-wake regulation (Krone et al., 2021, 2025; Hong et al. 2023; Wasilczuk et al. 2025; Honjo et al., 2025; Chouafeev et al., 2025); depth of anaesthesia (Wasilczuk et al. 2025), and the influence of stress on sleep (Chouafeev et al. 2025) the projections of orexin-sensitive L6b to L5 pyramidal neurons may be a key circuitry in the top-down regulation of brain states.”

(2) There are plots where the y-axis tick label appears to be offset from the tick mark (4a, S5b, S6a).

Thank you for spotting this graphical issue. We have removed the y-axis tick labels from Figure 4a to avoid confusion. Please note that we decided to remove Figure S5 and Figure S6, because after careful re-analysis we concluded that the group size was too small to draw conclusions on orexin spectra and that any results could be potentially misleading.

(3) The 2-h time constant, I believe, is depicted in Figure 4H (not 4G).

Thank you for spotting this. We have corrected the figure legends accordingly and double-checked that Figure 4G depicts the 2-h time constant and Figure 4H the 6-h time constant.

(4) "...although there was an indication of a higher absolute theta-peak power in layer 6b silenced mice (Figure S6)," pg. 10. It is not clear to me how the data lead to this conclusion.

Thank you for identifying this inconsistency, which resulted from a preliminary statistical analysis subsequently corrected. We have now improved the statistical analysis of spectral data (for more details see comments to both reviewers in public response) and removed this statement, which in fact is no longer supported by the data.

(5) Exclusion of female mice is not listed as a limitation.

We now discuss this limitation as follows:

“In the current study, only male mice were used, because our experimental protocol precluded the possibility of accurately monitoring the oestrous cycle, which has marked effects on brain activity, arousal and vigilance states. We therefore decided to use male mice only for the current study but are planning to use both sexes in future work.”

(6) A brief description of why Cplx3 and Tbr1 antibodies are being used will be helpful to include in the Methods (pg. 21) in addition to what is in the figure caption.

We have added the following information to the methods section to clarify why we used these two antibodies: “rabbit α-Cplx3 to distinguish between L6a and L6b” “mouse α-Tbr1 to identify the L5-6 boundary”

(7) Including a label/title for the Figure 2c spectral plots will be helpful. It is not immediately clear if these are light period & dark period data or frontal & occipital data.

Thank you for pointing this out, we have updated the figure legend to clarify what is shown on this Figure

Similar comments for S2 and S3a plots. Including a state label on the plots will be helpful in addition to the caption description.

We have now added the state labels for Figure panels S2 and S3a for improved clarity.

Reviewer #2 (Recommendations for the authors):

This is a soundly conducted and well-written study that enhances our understanding of the cortical control of states of consciousness. I do not have any major concerns, but would like the authors to consider some alternate possibilities as suggested in my comments below:

We thank the reviewer for this positive assessment of our manuscript and the helpful suggestions.

(1) Given that the inactivation of layer6b neurons did not affect the time spent in sleep-wake states, to me it appears that these neurons likely have a role in creating the background neural conditions/oscillations supportive of an activated state rather than a direct role in behavioral state control.

We completely agree with the reviewer and have made the wording more consistent throughout the manuscript, now using “brain state control” rather than “behavioural state control” to clarify that the main effect observed in the L6b-silenced mouse model is a change in spectral characteristics reflecting brain oscillations, rather than effects on vigilance states, which were modest.

(2) Does the observed shift in REM sleep-related theta-peak frequency in the occipital derivation suggest changes in local neural processes, or could it be just a matter of better signal detection because theta is most prominent at or around the hippocampal region, which is approximately the location of occipital electrodes in this study.

The source of the shift in REM sleep–related theta peak frequency in the occipital derivation cannot be established with EEG recordings alone. Additional intracortical or intrahippocampal recordings would be necessary to distinguish between the two possible explanations proposed by the reviewer. We have discussed this further in the revised manuscript.

(3) Orexinergic system innervates multiple subcortical sites and widely covers the cortex too, because of which the effect of ICV orexins cannot be attributed to just layer6b neurons as described in the manuscript ("Layer 6b mediates effects of orexin on brain activity.").

We agree with the reviewer that this is a limitation. We have now adjusted the subtitle of the paragraph describing the results from the ICV administration of orexin and further mention this important consideration in the ‘limitations’ section of the discussion.

(4) While the current study is focused on sleep-wake mechanisms, the findings reported here have much broader implications for behavioral and/or brain state arousal and provide a mechanistic bridge between different states of consciousness, including general anesthesia. Therefore, the authors may consider tying these findings with the recent work on the role of the prefrontal cortex in arousal from general anesthesia and slow-wave sleep (PMID: 35436248, PMID: 29937348, PMID: 33328847).

We thank the reviewer for this excellent recommendation. We are now citing these papers in the revised manuscript.

(5) It's up to the authors, but I do not see the need for the section on Clinical Implications. It's very speculative, and it makes the entire discussion section heavy.<br />

We have considerably shortened the discussion of potential clinical implications to make the manuscript more concise.

(6) Figure 1: It's difficult to compare the EEG power the way figures are set up right now. I think it would enhance clarity if the authors separate the plots based on state and show power from the control and silenced neuronal group in the same plot. Also, the colors are too similar (essentially a shade of green/blue) to provide effective visual resolution. This is especially true in panel d. Please consider changing the color scheme.

This comment seems to refer to Figure 2 and subsequent figures with analysis of vigilance states and EEG spectra (Figure 1 contains histological images). We have selected the colour scheme for colour-blind individuals. Therefore, the main difference is in the saturation, not the colour of the plots. We have tested the visibility of the colour scheme on a high-resolution screen with the original image files and can reassure the reviewer that the genotype differences, which are slightly blurred in the reduced-resolution figures provided within the combined text file for the review process, are easily distinguishable in the final figure quality.

(7) I don't understand the y-axis scale in Figure 1. How can this be 500% and if it is, then 500% of what?

This comment also seems to refer to the analysis of slow wave activity (SWA) in Figure 2 rather than to Figure 1 (histology figure). The percentage of SWA is normalised to the average SWA across the recording. Since NREM sleep is characterised by considerably higher SWA than wakefulness and REM sleep, the level of SWA during NREM sleep is in the range of 200-300%, and can be even higher after long wake episodes which are followed by a rebound of NREM sleep SWA. Hence, the upper limit of the y-axis in these (and subsequent) plots of SWA is 500% (of the average SWA). We have amended the figure legend to clarify that SWA is presented here as percentage of average SWA across the recording.

Author response:

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

eLife Assessment

In this potentially valuable computational study, the authors conducted atomistic and coarsegrained simulations to probe the temperature-dependent phase behaviors of ELF3, a disordered component of the evening complex in plant. The results aim to highlight the role of polyQ tracts in modulating the temperature sensitivity. The level of evidence is considered incomplete, due to the lack of systematic calibration of the coarse-grained model and limited statistical uncertainty analysis, especially considering the relatively subtle nature of the differences due to temperature change.

We agree that the subtle temperature dependence of ELF3-PrD condensation requires rigorous uncertainty reporting and careful interpretation of CG predictions. In the revised manuscript we therefore (i) report mean ± SEM across independent replicas for all CG observables and provide full time series in the Supplementary Information, and (ii) expand our CG analysis beyond cluster counting to include condensate stability (size), lifetime, internal mobility (D, α), dynamic heterogeneity (van Hove), and structural descriptors (anisotropy, singlechain compaction/density). These additions strengthen the robustness of the conclusions and even enable physical explanations of recent experimental measurements on ELF3-PrD condensates.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript explores the role of the Evening Complex (EC), specifically focusing on ELF3, a disordered protein component of the EC, and its temperature-dependent phase behavior. The study highlights the role of polyQ tracts in modulating temperature-sensitive condensate formation and provides a combination of computational approaches, including REST2 simulations and coarse-grained Martini simulations, to investigate how polyQ tract length and sequence context influence this behavior.

Strengths:

The study addresses a key question in plant biology - how temperature influences circadian clock-mediated growth regulation through protein phase behavior. The manuscript introduces the novel finding that polyQ tract length modulates the temperature-dependent formation of helices and condensates.

Weaknesses:

(1) Coarse-Grained Simulation Results Not Supported by Data:

The results presented in Figure 6A of the manuscript do not seem to show a clear trend in the number of clusters formed as a function of polyQ tract length. This is particularly evident in the comparison between 0Q and 7Q polyQ lengths, which display statistically similar values in terms of the number of clusters. The lack of distinction between these values raises questions about the sensitivity of the coarse-grained simulations to polyQ tract length, which the authors claim as a key modulator of condensate formation. This discrepancy weakens the argument that polyQ length directly impacts the clustering behavior in the simulations.

Suggested Analysis:

A more detailed statistical analysis should be performed to assess whether the observed differences between polyQ lengths are significant. This could involve hypothesis testing or the use of error bars in the graphs to better communicate the variability in the data.

Additionally, the authors should examine whether there are other features, such as cluster shape or internal structure, that might differentiate between different polyQ lengths, even if the total number of clusters is similar.

We agree that the number of clusters in Fig. 6A does not show a strong or monotonic dependence on polyQ length (e.g., 0Q vs 7Q can overlap within uncertainty). The cluster number is highly sensitive to coarsening kinetics and rapidly approaches a late-time plateau, and therefore is not our primary discriminator of variant-dependent condensation behavior.

To address the reviewer’s request for statistical rigor and additional differentiating features, we have revised the analysis in two ways. First, we now report mean ± SEM across independent replicas for all key CG observables and provide full replicate time series in the Supplementary Information to make variability and convergence/coarsening explicit.

Second, we shift our main CG conclusions away from “cluster number” and toward more diagnostic observables of condensate robustness and material state, including: (i) stability via the late-time mean largest-cluster size, (ii) persistence/lifetime via the fraction of frames with largest cluster size greater than 50, (iii) internal dynamics via MSD-derived DDD and anomalous exponent ααα, (iv) dynamic heterogeneity via self van Hove distributions relative to a Gaussian reference, and (v) morphology/internal structure via κ² and Rg distributions.

Notably, the κ²/Rg distributions are broadly overlapping at 300 K, indicating that in our system variant differences are expressed more strongly in stability/persistence and internal dynamics (D/α/van Hove) than in a large shift in single-chain compaction at this temperature.

This revised framing also aligns our interpretation with the experimental picture put forward by Huntin et al -- polyQ length modestly affects onset-like behavior but more strongly tunes condensed-phase regimes and dynamics.

Relevant revisions have been made in the Results and the Discussion sections.

(2) Inconsistency in Cluster Size Across Temperatures (Figure 6B):

The results in Figure 6B show a striking difference in the size of the largest cluster between temperatures of 290K and 300K. This abrupt shift in behavior lacks a clear mechanistic explanation. Typically, phase transitions driven by temperature are more gradual, unless there is some underlying structural or chemical shift that the authors have not accounted for. Without a clear explanation, this sudden change in behavior reduces confidence in the simulation Results.

Suggested Analysis:

The authors should explore possible explanations for the dramatic difference in cluster size between 290K and 300K. For example, they could investigate whether specific interactions (such as the breaking or formation of hydrogen bonds or hydrophobic contacts) might explain the behavior at higher temperatures.

It is important to check whether the coarse-grained simulation model has been adequately parameterized and scaled for accurate temperature dependence. Atomistic simulations of monomers and dimers with varying polyQ tract lengths could be used to fine-tune the coarsegrained model, ensuring it accurately reflects molecular behavior. The gross estimate of a 10% scaling factor might be insufficient and could lead to inaccurate representations of cluster formation.

We agree that the apparently sharp change in largest-cluster size between 290 K and 300 K requires clearer interpretation. In the revised manuscript, we clarify that this behavior does not imply an abrupt thermodynamic phase transition; rather, in a finite (~100-chain) simulation box, the largest cluster size is sensitive to both (i) proximity to a coexistence boundary and (ii) coarsening kinetics. Consistent with this, all systems rapidly coarsen early and then approach a late-time plateau, so the dominant cluster size can change steeply when conditions shift the balance between one system-spanning droplet versus multiple long-lived subclusters.

To distinguish “true loss of condensation” from “differences in coarsening state,” we added replica-averaged stability and persistence metrics (mean ± SEM) and full time series. Importantly, the condensate lifetime (fraction of frames with largest aggregate-population > 50) is ~1 at both 290 K and 300 K, indicating that both temperatures correspond to a persistently condensed regime, not intermittent nucleation/dissolution. We therefore interpret the smaller dominant cluster at 290 K as reflecting slower coarsening / stronger kinetic arrest, where reduced chain mobility delays merger/annealing into a single large droplet within the simulated time window, leaving a larger satellite/dispersed population despite sustained condensation.

We further support this interpretation with mechanistic and dynamical analyses added in the revision. As temperature increases from 290 K to 300 K, we observe increased internal mobility (higher effective diffusivity, D) that would accelerate rearrangements and coalescence. In parallel, contact/desolvation analyses show progressive loss of protein-water contacts and gain of protein-protein contacts as clusters mature, and a residue-resolved comparison indicates net contact increases at 300 K relative to 290 K concentrated in aromatic-rich “sticker” regions, consistent with a strengthened intermolecular contact network that promotes more complete annealing at 300 K.

(We address the reviewer’s points regarding Martini temperature scaling/parameterization together with points (3)-(4) below.)

(3) Scaling of Coarse-Grained Model with Atomistic Simulations:

As mentioned, the coarse-grained model used in the study may not have been properly scaled against atomistic data. A simple scaling factor of 10% may not be appropriate for accurately capturing the behavior of polyQ tracts across different lengths, especially considering their sensitivity to subtle changes in temperature. Without rigorous validation against atomistic simulations, the coarse-grained model's predictions could be skewed.

(4) To address this, the authors should compare the coarse-grained model with atomistic simulations of monomeric and dimeric forms of ELF3 with different polyQ tract lengths. By comparing key structural parameters (e.g., radius of gyration, contact maps, and clustering propensity), the authors could adjust the coarse-grained model to more accurately reflect the atomistic behavior. The authors have wealth of atomistic simulation data that could afford such benchmarking and identification of scaling factor

Additionally, the authors should investigate whether the assumed scaling factor of 10% is appropriate for each polyQ length or whether it needs to be refined based on specific properties, such as the number of hydrophobic interactions or secondary structure stability.

We agree that temperature-dependent CG predictions must be interpreted carefully and that the interaction balance should be justified. In the revision, we therefore clarify both our calibration choice and the scope of inference.

We use Martini 3 with a single, literature-motivated adjustment: protein-water Lennard-Jones interactions are strengthened by 10 percent, following an established strategy shown to improve IDP/multidomain protein behavior in Martini 3. This scaling is applied uniformly to all residues, polyQ lengths, and temperatures to avoid introducing construct-specific parameters and to preserve a controlled comparison across variants.

We emphasize that our CG simulations are used in a comparative manner (how stability/dynamics/structure change with temperature and polyQ length under a fixed model), and we do not claim a quantitatively exact phase boundary or transition temperature for ELF3. In this spirit, and consistent with how Martini 3 has been used in prior work to probe thermally varying properties across temperature windows (while acknowledging documented limits to temperature transferability), we treat the temperature sweep as a comparative probe rather than an absolute calibration (https://doi.org/10.1063/5.0221199, 10.1021/acscentsci.5c00755, https://doi.org/10.1038/s41592-021-01098-3). Accordingly, we report replica uncertainty (mean ± SEM) for all CG observables and restrict conclusions to qualitative trends that are robust to replicate variability.

Finally, while we do not undertake a full ELF3-specific reparameterization, we include qualitative checks linking atomistic and CG behavior: the CG model reproduces the same qualitative features of single-chain reorganization inferred from atomistic simulations — notably the radiusof-gyration (Fig. S8) and the rearrangement/exposure of aromatic “sticker” regions that correlate with strengthened intermolecular contacts in the condensate. We emphasize that these comparisons are intended as qualitative sanity checks on trend direction, not as a quantitative validation or calibration of an absolute phase boundary.

(5) Lack of Analysis for Liquid-Like Behavior in Phase Separation:

The simulations presented in the manuscript do not analyze the liquid-like behavior of ELF3 condensates, which is a key characteristic of liquid-liquid phase separation (LLPS). In LLPS systems, condensates are often dynamic, with chains exchanging between clusters, indicating liquid-like rather than solid-like behavior. The authors fail to probe this crucial aspect, which is necessary to support the claim that ELF3 undergoes phase separation.

Suggested Analysis:

The authors should conduct additional analyses to probe the liquid-like nature of the clusters formed by ELF3. One approach would be to analyze the dynamics of chain exchange between clusters, measuring how frequently chains leave one cluster and join another over time. This analysis would reveal whether the condensates behave as liquid- like, dynamic structures or more static, solid-like aggregates.

Additionally, the temperature dependence of these exchange dynamics should be investigated. In true liquid-liquid phase separation, the rate of chain exchange is often sensitive to temperature. Observing how this rate changes between 290K and 300K, for instance, could help explain the abrupt shift in cluster size seen in Figure 6B.

The authors should also analyze whether the internal structures of the condensates are consistent with a liquid-like phase. For example, radial distribution functions and contact lifetimes could be calculated to reveal whether the clusters exhibit liquid-like organization.

We thank the reviewer for highlighting that liquid-like behavior is a key diagnostic for LLPS. We agree that our original manuscript did not explicitly quantify condensate material properties. In the revision, we therefore add several complementary analyses and figures that directly probe whether the condensed state in our simulations is liquid-like versus dynamically arrested, and how this depends on temperature and polyQ length.

(i) Condensate persistence vs temperature (stability and lifetime).

We now quantify two replica-averaged metrics with uncertainty (mean ± SEM): (a) stability, defined as the mean largest-cluster size over a late-time analysis window, and (b) lifetime, defined as the fraction of frames in which the dominant cluster exceeds a fixed size threshold. These results are shown in the new figures “Stability (Mean cluster size)” and “Lifetime (P [size > 50])”. In our system, both 290 K and 300 K correspond to a persistently condensed regime (lifetime ≈ 1 across variants), whereas at 340 K the lifetime drops substantially (≈0.3-0.5 depending on variant), indicating intermittent condensation / partial dissolution at high temperature. This directly demonstrates temperature-dependent persistence of the condensed state and clarifies that the key qualitative change at high temperature is loss of stability and intermittency, rather than a purely static cluster-size difference.

(ii) Internal mobility and viscoelasticity (D and α).

To probe liquid-like dynamics within the condensed state, we compute internal Mean squared displacement (MSD) and extract an effective internal diffusivity D(T) and anomalous exponent α(T) (new figures FIG X). In our system, D increases systematically with temperature for all variants, confirming that internal rearrangements accelerate at higher temperature. At the same time, α remains strongly subdiffusive (α ≈ 0.3-0.5), indicating constrained, non-Fickian motion rather than simple liquid diffusion. Importantly, we also observe variant-dependent mobility: around 300-320 K, 0Q exhibits markedly lower D than 19Q, consistent with stronger kinetic arrest in 0Q even when both variants are condensed. Together, these dynamics metrics show that our condensates are not ideal liquids, but instead occupy a viscoelastic / dynamically slowed regime with clear temperature dependence.

(ii) Dynamic heterogeneity (self van Hove).

We additionally compute the self van Hove displacement distributions (Fig. SX). In our system, the van Hove distributions deviate from a Gaussian reference matched to the MSD, with an excess of near-zero displacements relative to a simple Gaussian model. This non-Gaussian displacement statistics is consistent with heterogeneous/caging-like dynamics inside the condensed phase, further supporting a viscoelastic (gel-like) rather than purely liquid material state at the timescales accessible to simulation.

(iv) Internal structure and morphology (Rg and anisotropy).

Finally, we add structural descriptors as requested. The new Rg distribution and shape anisotropy (κ²) violin plots quantify single-chain compaction and heterogeneity in morphology within the condensed phase. In our system these structural distributions are broadly overlapping at 300 K, indicating that differences among variants are more strongly expressed in dynamics (D/α/van Hove) and stability/lifetime, rather than in a large change in single-chain compaction at this temperature. We report these results transparently and include them in the SI as additional mechanistic context.

We now explicitly frame our CG condensed phases as viscoelastic/dynamically slowed condensates rather than assuming fully liquid droplets. This interpretation is consistent with experimental observations on ELF3 PrLD that report very slow recovery/gel-like behavior under some conditions (i.e., condensates can age into low-mobility hydrogel states).

(6) Lack of justification of polydispersity of polyQ:

The authors don't provide any rationale for choice of different copies of polyQ used in the manuscript for their chain- growth simulation studies. It will be more apt if it can be motivated via some precedent experimental observations.

We agree and have clarified our rationale in the revised manuscript. ELF3’s polyQ tract is a naturally polymorphic short tandem repeat in Arabidopsis, reported to vary from roughly ~7 to ~29 glutamines in natural populations, and this variation has been linked to ELF3-dependent phenotypes and temperature-responsive growth (Undurraga et al.; Jung et al.). Importantly, recent ELF3 PrLD thermosensing/condensation experiments explicitly compare multiple polyQ lengths (including Q0, short/WT-like constructs such as Q7, and expanded tracts around ~Q20) and show that polyQ length tunes temperature-responsive phase behavior and condensate properties (Jung et al.; Hutin et al.).

Accordingly, for our chain-growth ensembles we chose a small, experimentally motivated set that brackets this range - 0Q (deletion), 7Q (WT-like short), and expanded lengths 13Q and 19Q (with 19Q closely matching the ~Q20 construct used experimentally), so that our simulations map onto established constructs and naturally occurring variation rather than arbitrary copy numbers.

The manuscript draft has been modified in the Results and Methods sections.

Jung J-H. et al. A prion-like domain in ELF3 functions as a thermosensor in Arabidopsis. Nature (2020).

Undurraga S. et al. Background-dependent effects of polyglutamine variation in the Arabidopsis thaliana gene ELF3. PNAS (2012), DOI: 10.1073/pnas.1211021109.

Hutin S. et al. Phase separation and molecular ordering of the prion-like domain of the Arabidopsis thermosensory protein EARLY FLOWERING 3. PNAS (2023).

(7) Lack of initiative to connect to Experiments:

While the computational models and simulations provide robust theoretical insights, the absence of direct experimental validation weakens the overall impact of the manuscript. For example, experimental data on how specific mutations in the polyQ tract influence ELF3 behavior in vivo would significantly bolster the authors' claims. The manuscript would benefit from either citing existing experimental studies that corroborate these findings or from suggesting future experimental directions.

We agree that our original submission did not make the experimental connections explicit enough, and we have strengthened this in the revision by (i) explicitly anchoring our results to published ELF3 thermosensing/condensation measurements and (ii) articulating concrete, experimentally testable mechanistic predictions that follow from the simulations.

(i) Explicit connection to published experimental benchmarks: We now cite and discuss key experimental studies that directly probe ELF3 temperature responsiveness and polyQ effects. Jung et al. demonstrated temperature-triggered ELF3 condensation/speckle formation in vivo and showed that polyQ length modulates thermoresponsive behavior. More recently, Hutin et al. compared ELF3 PrLD constructs spanning polyQ lengths (e.g., Q0, Q7, and ~Q20) and reported temperature-triggered phase separation, condition-dependent condensed-phase regimes (droplet-like versus more arrested/gel-/hydrogel-like), and reduced mobility/immobile fractions quantified by FRAP in some regimes. In the revised manuscript we explicitly map these observations onto our results: our coarse-grained simulations capture temperature-dependent condensation propensity, while our added condensate dynamics analyses (MSD-derived internal mobility DDD, anomalous exponent α\alphaα, and self van Hove displacement statistics) indicate dynamically slowed/heterogeneous condensates rather than assuming ideal liquid droplets—consistent with experimentally observed slow FRAP recovery and arrested behavior under some conditions.

(ii) Mechanistic Connections: While existing experiments establish that ELF3 condensation is temperature-triggered and tuned by polyQ length, they cannot directly resolve the molecular interaction changes that drive these macroscopic readouts. We therefore emphasize that our atomistic and coarse-grained analyses provide a mechanistic interpretation: temperature shifts reorganize and expose “sticker”-rich regions (notably aromatics), strengthening intermolecular contact networks that tune condensate stability and material properties. This framing aligns our conclusions with the experimental picture that polyQ length has modest effects on onset-like behavior but more strongly tunes condensed-phase robustness and dynamics (persistence, internal mobility, and arrest) across temperature

The modifications relevant to this are in the Discussion section.

Reviewer #2 (Public review):

Summary:

The authors aimed to explore how a key protein in the circadian clock of plants, ELF3, responds to temperature changes by forming molecular condensates. They focused on understanding the role of a specific region of the protein, a polyQ tract, in promoting temperature-sensitive structural changes and regulating the formation of condensates. Through a series of computational simulations, they sought to uncover the molecular basis for ELF3's temperature responsiveness and its broader implications for plant growth and adaptation to environmental conditions.

Strengths:

The study's strength lies in its focus on an important biological question: how plants sense and respond to temperature changes at the molecular level. The authors employed a variety of computational techniques, including coarse-grained simulations, to explore the role of specific molecular features in this process. These methods provide a multi-scale view of protein behavior and offer valuable insights into how molecular structures may influence biological function.

Weaknesses:

However, there are notable weaknesses in the evidence provided. While the authors present trends in molecular changes, such as shifts in helical propensity and the formation of condensates, these results seem subtle and are not strongly substantiated by statistical analysis. The lack of error bars in the figures makes it difficult to distinguish between meaningful signals and potential noise in the data. Furthermore, the temperature-sensitive behavior appears to be influenced more by chain length than by sequence-specific effects of the polyQ region, raising questions about whether the findings truly capture the molecular mechanisms responsible for temperature sensing. Additionally, some simulations, particularly those related to the formation of condensates, do not appear fully converged, which casts further doubt on the robustness of the results.

We appreciate the reviewer’s concerns regarding statistical support, sequence specificity, and convergence. In the revised manuscript we (i) report replicate-averaged means with uncertainty (mean ± SEM) for all key observables and add error bars/shaded bands to the relevant figures, (ii) provide the full time series plots in the Supplementary Information to make variability and equilibration transparent, and (iii) revise our interpretation to emphasize that polyQ length has only modest effects on onset-like metrics but more strongly tunes condensate stability and material state (lifetime, internal mobility (D), subdiffusion exponent (α), and non-Gaussian van Hove signatures). This revised framing is consistent with recent ELF3 PrLD experiments showing that polyQ variation can subtly affect onset while substantially modulating condensed-phase behavior and dynamics. Relevant changes to the main text have been made in the Results and Discussion section.

Additional Context for Readers:

Readers should interpret the results with caution, especially regarding the molecular mechanisms proposed for temperature sensing. While the study presents interesting trends, the evidence is not definitive, and the findings may be more reflective of general protein behavior (such as the effect of chain length on condensate formation) than specific sequence-driven responses to temperature. Further experimental studies and more converged simulations will be necessary to fully understand the role of ELF3 in temperature regulation.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I already have listed my possible recommendations for authors for revising their manuscript in the review. By addressing these issues, the authors could significantly improve the robustness of their conclusions and provide stronger evidence for ELF3's role in temperature-responsive phase separation.

Author Response:

Reviewer #1 (Public review):

Summary:

The authors present a novel approach to subcellular spatial proteomics by combining laser microdissection with expansion microscopy and LC-MS/MS analysis (SPEx). They implement two different workflows for LMD and LC-MS/MS quantification:

(1)The standard approach, where an area of interest is cut out by LMD, subjected to proteomics analysis, and compared to the rest of the cell without the dissected ROI.

(2) The subtraction approach, where ROIs are removed, and the remaining cellular material is compared to samples containing both the surrounding material and the ROI.

The authors assess the technique by applying it to subcellular targets of various sizes, volumes, and protein compositions such as the nucleus, nucleoli, and Golgi. They demonstrate that SPEx can identify proteins enriched or reduced in ROIs.

Strengths:

The broad, relatively easy, and inexpensive applicability of this approach to potentially many cell types and subcellular areas of interest provides an exciting alternative to subcellular fractionation, native immunoprecipitation, or genetically encoded proximity labeling constructs. Moreover, by visually selecting ROIs for subsequent analysis, subcellular context or organelle morphology can be taken into account, as discussed by the authors in the discussion section.

Weaknesses:

While strongly supporting the sharing of this approach, we have a number of comments and questions that will improve the impact of the manuscript:

We thank the reviewer for the careful evaluation of our manuscript and the generally positive assessment. We plan on improving our manuscript based on the reviewers’ comments.

(1) General:

a) The manuscript would benefit from restructuring and language revision. In its current form, the writing is sometimes dense and verbose (in particular, the Results section). This makes it difficult to follow the authors' arguments.

We will improve readability and clarity of the results section in the revised manuscript.

b) The authors mention the possibility of selecting organelles based on morphology. This is left for the discussion, but it seems like a missed opportunity - the authors could compare individual organelles in different morphological states, e.g., connected vs. fragmented mitochondria.

The authors agree with the reviewers’ assessment that investigating proteome of organelles based on morphology or cellular state is an exciting application of SPEx. While we plan experiments along this line in the future, we think that these experiments are beyond the scope of this manuscript, which is meant to describe the method and its general usefulness.

(2) Technical:

a) Why do the authors strive and optimize for a 10x expansion factor? Is SPEx compatible with a more standard 4x expansion, as e.g., used in the classic U-ExM approach (https://www.nature.com/articles/s41592-018-0238-1)? This could be added to the discussion.

We aimed for 10x expansion solely because our ultimate goal is to cut out very small structures. Isolating structures as small as nucleoli would not be as reliable with a lower expansion factor (i.e. 4x) expansion. We did not assess the compatibility with U-ExM. We would assume that SPEx would also work with U-ExM as expansion method; omitting protease treatment, however. Still, we performed pilots with just 4x expansion (using TREx) in the early stages of optimization. We were able to isolate single cells and obtain similar protein coverage as with 10x expansion. We will further clarify our motivation to use 10x expansion in the discussion.

We would also like to point out whether to U-ExM the standard method or not is rather subjective. Even though TREx was published three years later, it is also very widely used. The original expansion microscopy method was published three years prior to U-ExM.

b) The U-ExM approach shows improved ultrastructural preservation when using 3%FA with 0.1% glutaraldehyde fixation (GA). Is SPEx compatible with the use of low amounts of GA for fixation?

We tried different fixation methods in the early stages of this study (where expansion was not yet close to 10x). We saw a mild negative effect of GA on the expansion factor, so we avoided it in the later experiments since it also did not seem necessary to preserve the structure of our organelles of interest. However, the use of GA would generally be compatible with SPEx, potentially at the cost of a mild negative effect on expansion factor (see Author response image 1) and proteome coverage. We can add this information to the discussion.

Author response image 1.

Fixation methods mini-screen. Cells were fixed with the indicated reagents for 10 minutes at 37°C. After TREx expansion, the diameter of the nucleus was measured (A) and the resulting expansion factor compared to the non-expanded control was determined (B).

Related to the above, was the anchoring efficiency reduced only to achieve a 10x expansion factor or does this additionally affect the proteome coverage?

We solely lowered the anchoring in order to allow for higher expansion factors. In earlier pilots we performed proteomic analysis on samples that were just expanded 4x using standard TREx expansion (also using the original anchoring strategy from the TREx publication, consisting of 0.2 mg/ml AcX for overnight at RT). We presented the results of this pilot in Fig S1A. We still detected over 2,000 proteins from 10 cells, a coverage, which is highly similar to what we found in the final experiments (Figure 2F), in which the anchoring was lower yielding 10x expansion. Based on these data, we hypothesize that anchoring (and expansion factor!) has a negligible impact on protein coverage. We will clarify this in the manuscript.

d) Have the authors considered using alternative anchoring approaches, such as GMA (https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0291506#pone.0291506.s001), which potentially increase the amount of sample retained in the hydrogel, thus allowing for better proteome coverage? This could be added to the discussion.

We did not use alternative anchoring approaches. We modified the TREx protocol to fit our purposes and since this was sufficient, we did not explore alternatives. However, using anchoring approaches, in which higher amounts of sample could be retained in the gel might be beneficial for the proteomics coverage. We will keep this suggestion in mind for future experiments. Thank you for the suggestion!

e) The limitation of the approach to near-2D samples should be mentioned, and alternative approaches for more 3D samples could be discussed.

The authors agree that SPEx is limited to near-2D samples at this point. We suggest that SPEx is applicable for 3D samples (e.g. in tissues) by performing cryosectioning. TREx has been shown to be compatible with sectioned tissue (Damstra et al., 2022). We will elaborate this in the discussion.

f) How are peptides that are directly anchored to the hydrogel dealt with during LC-MS/MS analysis? Are they excluded, or can they be identified during the spectral search? The latter would allow us to get a deeper structural understanding of how proteins are actually anchored into hydrogels, which so far has not been assessed.

The reviewer raises an interesting point. In general, peptides carrying the anchoring modification are analysed by LC-MS, but we did not include these specific modifications in the database search. Overall, we assumed that the labeling would be low and stochastic and hence should, if at all, only minimally affect the detection of peptides. Nevertheless, in response to the reviewers’ comment, we searched the MS data again for the crosslinking reagent linked to lysine residues. However, we could not get any confident hit for any peptide containing this modification. Since we cannot exclude that the modification precludes the identification of the corresponding peptides, we compared the number peptides generated by trypsin cleavage after arginine and lysine. As the human genome contains similar proportions of both amino acids, one would expect similar numbers of both peptide types being identified. Any modifications of lysine by the anchoring reagent used, would prevent tryptic cleavage and thus reduce the number of lysine peptides. As shown in Author response image 2, the number of lysine terminating is only slightly lower compared to arginine terminating peptides. Notably, the proteomics results of a different fixed human tissue sample directly extracted by laser capture micro dissection without expansion showed a very similar lysine to arginine peptide ratio. This indicates that the large majority of lysine residues is not modified and affected by the hydrogel anchoring.

Author response image 2.

Number of peptides identified either terminating with lysine (K) or arginine (R) across all samples shown in Figure 5F.

An alternative approach to address this question would be to investigate if the peptide coverage of proteins detected by SPEx is enriched for peptides representing the folded core of proteins as opposed to the surface-exposed regions, which likely get more anchored into the hydrogel.

Because of the negligible amounts of modified peptides, we did not investigate this potential bias of surface-exposed versus folded-core peptides.

g) Same question regarding peptides with NHS labeling. Can they be identified, or do they just compete for ionization and thus negatively affect coverage and dynamic range of the LC-MS/MS approach?

The reviewer raises a similar point as above for another lysine labeling used during the SPEx protocol. Again, we specifically looked for this modification by re-searching the raw MS data, but still could not identify any peptides, carrying this modification on a lysine residue. Even though we cannot exclude that this rather large modification prevents detection, considering the high number of lysine terminating peptides in our dataset (see Figure 2), we would expect that also this labeling step is stochastic and affects only a minor proportion of the proteins.

h) How are the primary and secondary antibodies affecting the proteomics analysis identified as contaminants?

We thank the reviewer for this comment. Since antibodies bind to proteins in a non-covalent manner, they will be released during the denaturing steps of the protocol. Of course, the antibodies will stay in the sample, be digested and analyzed and could, if very abundant, affect the analysis of the proteins from the samples. To check this possibility, we re-searched the MS data including the sequences of the antibodies used. To our surprise, we could not detect any peptides of these antibodies. This suggests that the concentrations of the antibodies used are much lower than those of the sample proteins and thus should not have any impact on the proteomics results.  We interpret this result also as a benefit of our method compared to organellar-IP.

i) Have the authors observed differences in proteomics coverage of only antibody vs NHS-labeling? Depending on the questions above, could pure antibody-based labeling increase proteomic coverage?

We did not perform this comparative analysis, since we always used NHS dyes. In the experiments presented in this manuscript, NHS dyes allowed easy visualization of the whole cell without the use of antibodies. This NHS staining was essential for this particular setup for sample acquisition. We cut out entire cells, cells lacking the nucleus and cells lacking the Golgi apparatus, which served as critical controls. However, other ways of detecting cell boundaries could be used to avoid NHS staining. As shown above, both, the anchor and NHS labeling are likewise sparse and stochastic. Moreover, we could not detect any impact of the antibody labeling to our results. Thus, we assume that both labeling procedures could be used.

Reviewer #2 (Public review):

Summary:

This study introduces a method that combines physical expansion of cells, imaging-guided isolation of defined regions, and protein identification to enable compartment-resolved analysis of protein composition at the subcellular scale. The authors aim to address a central limitation in existing approaches, namely the loss of spatial information during sample preparation or the indirect nature of proximity-based labeling methods. Using several cellular compartments as examples, they demonstrate that their approach can recover compartment-enriched protein sets and identify candidate proteins with previously unassigned localization.

Strengths:

A major strength of this work is the conceptual simplicity and accessibility of the approach. By combining established techniques in a modular way, the method avoids the need for genetic manipulation or specialized labeling strategies, making it broadly adaptable across experimental systems. The ability to directly select regions of interest based on imaging represents a clear advantage over indirect enrichment strategies and allows flexible targeting of both membrane-bound and non-membrane-bound compartments.

The experimental design is also a strong aspect of the study. The use of complementary comparison strategies-analyzing isolated compartments alongside matched "subtracted" controls-provides an internal framework for assessing enrichment and depletion, increasing confidence in spatial assignment. The application of the method across multiple organelles of different sizes and properties demonstrates versatility, and the reported specificity for several compartments is encouraging. In particular, the ability to profile small and biochemically challenging structures highlights a potentially important niche for the approach.

Weaknesses:

Despite these strengths, several methodological limitations constrain the interpretation of the results. The most important relates to spatial accuracy in three dimensions. While lateral resolution is improved through physical expansion, the lack of depth resolution introduces uncertainty regarding contributions from structures above and below the selected region. Although the authors argue that this does not substantially affect specificity, the current evidence is largely indirect, and a more rigorous quantification of potential contamination would strengthen this conclusion.

Quantitative interpretation also remains challenging. Because the measurements reflect total protein abundance rather than local concentration, differences in compartment size and protein density can influence enrichment values, particularly for small structures embedded within larger volumes. This issue is evident in the analysis of smaller compartments and complicates direct comparison across conditions. Additional normalization or modeling would help clarify how to interpret these measurements.

Another limitation concerns variability in the expansion process and its downstream consequences. Differences in expansion factor across samples may affect the definition of regions of interest and introduce variability in sampling, yet the impact of this variability is not fully explored. Similarly, the use of a modified chemical treatment to preserve proteins for downstream analysis is central to the workflow but is not extensively validated with respect to preservation of spatial organization.

While the identification of previously unannotated proteins is an appealing aspect of the study, validation is limited to a small number of examples, and broader support from independent datasets or literature context is lacking. In addition, the study primarily focuses on steady-state measurements in a single cell type, and therefore does not yet demonstrate the ability of the method to capture dynamic or condition-dependent changes in protein localization.

Finally, the positioning of the method relative to existing approaches could be more clearly articulated. Although qualitative comparisons are provided, a more systematic and quantitative benchmarking against alternative strategies would help readers better understand the specific advantages and trade-offs.

We thank the reviewer for the careful evaluation of the manuscript and for the constructive feedback. We think the reviewer raises valid points and will address them in the revised manuscript.

Reviewer #3 (Public review):

Franziscus et al. describe an elegant approach for spatially specific proteome analysis. To achieve this, they expand fixed cells and subsequently use a laser to micro-dissect a region of interest, which is then analyzed by mass spectrometry.

They demonstrate the effectiveness of their approach by analyzing the nucleus, nucleolus, and the Golgi, and benchmark their hits against previous datasets for these organelles.

The manuscript is very well written and nicely guides the reader through the applied methods. The presented data is convincing, and I do not see the need for additional experimental verification of the protocol. The only minor concern is the novelty of the method and the presentation. A combination of expansion, laser microdissection, and proteomics has been applied in the past (PMID: 36450705, PMID: 39477916). In the manuscript, one of these studies is cited, though it does not become clear that this approach is already described. However, Franziscus et al. describe the approach better and make it more accessible to the reader, especially since the other studies described this methodology in combination with tissue expansion and not in combination with single cell expansion as it is done here. I would ask the authors to be clearer in the introduction about what others have already done and what their contribution is here. In general, I am convinced that the community will benefit from the presented protocol to analyze organelle proteomics in detail.

We thank the reviewer for the careful evaluation of our manuscript and overwhelmingly positive assessment. We apologize for the omission of the mentioned citations, and will adjust the introduction to make it clearer what has already been done and what the advance our method provides.

References

Damstra HG, Mohar B, Eddison M, Akhmanova A, Kapitein LC, Tillberg PW. 2022. Visualizing cellular and tissue ultrastructure using Ten-fold Robust Expansion Microscopy (TREx). eLife 11:e73775. DOI: https://doi.org/10.7554/eLife.73775

Gambarotto D, Hamel V, Guichard P. 2021. Ultrastructure expansion microscopy (U-ExM). Methods in Cell Biology 161:57–81. DOI: https://doi.org/10.1016/bs.mcb.2020.05.006, PMID: 33478697

Liffner B, Silva TLA e., Vega-Rodriguez J, Absalon S. 2024. Mosquito Tissue Ultrastructure-Expansion Microscopy (MoTissU-ExM) enables ultrastructural and anatomical analysis of malaria parasites and their mosquito. BMC Methods 1:13. DOI: https://doi.org/10.1186/s44330-024-00013-4

Author response:

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

We thank the editor and reviewers for their constructive questions, valuable feedback, and for approving our manuscript. We truly appreciate the opportunity to improve our work based on their insightful comments. Before addressing the editor’s and each referee’s remarks individually, we provide below a point-by-point response summarizing the revisions made.

Duplication of control groups across experiments

We appreciate the reviewers’ concern regarding the potential duplication of control groups. In the revised manuscript, we have explicitly clarified that independent groups of control mice were used for each experiment. These details are now clearly indicated in the Materials and Methods section to avoid any ambiguity and to reinforce the rigor of our experimental design (Page 15, Line 453-455): “Furthermore, knockout animals and those treated with pharmacological inhibitors or neutralizing antibodies shared the same control groups (chow and HFCD), as required by the animal ethics committee.”

Validation of the MASLD model

To strengthen the metabolic characterization of our MASLD model, we have now included additional parameters, including liver weight, Picrosirius staining and blood glucose measurements. These data are presented as new graphs in the revised manuscript and support the metabolic relevance of the HFCD diet model (Figure Suplementary S1). The corresponding description has been added to the Results section (Page 5, Lines 116-117) as follows: “Mice fed HFCD showed no increase in liver weight and collagen deposition as evidenced by Picrosirius staining (Fig. S1A and Fig. S1C)”

Assessment of liver injury in RagKO and anti-NK1.1 mice

We fully agree that assessment of liver injury is essential for these models. For mice treated with antiNK1.1, ALT levels are shown in Figure 4G, confirming increased liver injury after treatment. Regarding Rag⁻/⁻ mice, the animals exhibit exacerbation of liver injury when fed a HFCD diet and challenged with LPS (Page 7, Lines 183–184). The corresponding description has been added to the Results section (Page 7, Lines 175-176) as follows: “Interestingly, Rag1-deficient animals under the HFCD remained susceptible to the LPS challenge (Fig. 4C) with exacerbation of liver injury (Fig. 4D) ”

Discussion of limitations

We have expanded the Discussion section to provide a more comprehensive and balanced perspective on the limitations of our model and experimental approach (Page 13-14, Lines 401–414) “Our study presents several limitations that should be acknowledged and discussed. First, we cannot entirely rule out the possibility that our mice deficient in pro-inflammatory components exhibit reduced responsiveness to LPS. However, our ex vivo analyses using splenocytes from these animals revealed a preserved cytokine production following LPS stimulation. These results suggest that the in vivo differences observed are primarily driven by the MAFLD condition rather than by intrinsic defects in LPS sensitivity. Second, the absence of publicly available single-cell RNA-seq datasets from MAFLD subjects under endotoxemic or septic conditions limited our ability to perform direct translational comparisons. To overcome this, we analyzed existing MAFLD patients and experimental MAFLD datasets, which consistently demonstrated upregulation of IFN-y and TNF-α inflammatory pathways in MALFD. In line with these findings, our murine model revealed TNF-α⁺ myeloid and IFN-y⁺ NK cell populations, thereby reinforcing the validity and translational relevance of our results.”. This revision highlights the constraints of the MASLD model, the inherent variability among in vivo experiments, and the interpretative limitations related to immunodeficient mouse strains.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In Figure 4 the authors are showing the number of IFN+ positive CD4, CD8, and NK 1.1+ cells. Could they show from total IFNg production, how much it goes specifically on NK cells and how much on other cell populations since NK1.1 is NK but also NKT and gamma delta T cell marker? Also, in Figure 2E the authors see a substantial increase in IFNg signal in T cells.

While we did not specifically assess IFNγ production in NKT cells or other minor populations, our data indicate that the NK1.1+CD3+ cells (NKT cells) cited in Page 7, Lines  188-192 were essentially absent in the liver tissue of LPS-challenged animals, as shown in Supplementary Figures 3C and S10. The corresponding description has been added to the Results section (Page 7, Lines 188-192) as follows: “We observed that the number of NK cells increased in the liver tissue of PBS-treated MAFLD mice compared with mice fed a control diet (Fig. 4E). LPS challenge increased the accumulation of NK1.1+CD3− NK cells in the liver tissue of MAFLD mice and the absence of NK1.1+CD3+ NKT cells (Fig. S3C and 4E)”.

This absence was consistent across all experimental conditions, corroborating our focus on NK1.1+CD3− cells as the primary source of NK1.1-associated IFNγ production. Furthermore, data demonstrated in Figure 2E illustrate the presence of IFNγ primarily in NK cells. Therefore, the observed IFNγ signal, attributed to NK1.1+ cells, predominantly reflects conventional NK cells, with minimal contribution from NKT or γδ T cells.

(2) In Figure 4C, the authors state that the results suggest that T and B cells do not contribute to susceptibility to LPS challenge. However, they observe a drop in survival compared to chow+LPS. Are the authors certain there is no statistical significance there?

The observed decrease in survival is consistent with our expectations, as T and B cells are not the primary source of interferon-gamma (IFNγ) in this context. Even in their absence, animals remain susceptible to LPS challenge due to the presence of other IFNγ-producing cells that drive the observed lethality. We have carefully re-examined the statistical analysis and confirm that it was correctly performed.  

(3) Since the survival curve and rate are exactly the same (60%) in Figures 3F, 3G, 4C, 4F, 5G, and 5H I would just like to double-check that the authors used different controls for each experiment.

The number of mice used in each experiment was carefully determined to ensure sufficient statistical power while fully complying with the limits established by our institutional Animal Ethics Committee. To minimize animal use, the same control group was shared across multiple survival experiments. Despite using shared controls, the total number of animals per experimental group was adequate to produce robust and reproducible survival outcomes. All groups were properly randomized, and the shared control data were rigorously incorporated into statistical analyses. This strategy allowed us to maintain both ethical standards and the scientific rigor of our findings.

(4) In Figure 5 the authors are saying that it is neutrophils but not monocytes mediate susceptibility of animals with NAFLD to endotoxemia. However, CXCR2i depletion and CCR2 knock out mice affect both monocytes/macrophages and neutrophils. And in Figures 5E, 5G, and 5H they see that a) LPS+CXCR2i decreases liver damage more than LPS+anti Ly6G, b) HFCD mice challenged with LPS and treated with anti-LY6G do not rescue survival to levels of CHOW LPS and c) anti Ly6G treatment helps less than CXCR2i. Therefore, from both knock out mice and depletion experiments the authors can conclude that most likely monocytes (but potentially also other cells) together with neutrophils are substantial for the development of endotoxemic shock in choline-deficient high-fat diet model.

While neutrophils express CCR2, our data clearly show that CCR2 deficiency does not impair neutrophil migration, as demonstrated in Supplemental Figures 5A and 5B (added to the manuscript, page 8, lines 213–217). The corresponding description has been added to the Results section (Page 8, Lines 213217) as follows: ``Interestingly, animals deficient in monocyte migration (CCR2-/-) showed a high mortality rate compared to wild type after LPS challenge and neutrophil migration is not altered (Fig. 5SA and Fig. 5SB)``, In contrast, CCR2 deficiency primarily affects monocyte recruitment, yet in our experimental conditions, monocyte depletion or CCR2 knockout did not significantly alter the severity of endotoxemic shock, indicating that monocytes play a minimal role in mediating susceptibility in HFCD-fed mice.

To specifically investigate neutrophils, we used pharmacological blockade of CXCR2 to inhibit migration and antibody-mediated neutrophil depletion. Both approaches have consistently demonstrated that neutrophils are critical factors in endotoxemic shock.

These findings support our conclusion that neutrophils are the primary cellular contributors to susceptibility in HFCD-fed mice during endotoxemia, with monocytes making a negligible contribution under the tested conditions.

(6) In Figure 6A (but also others with PD-L1) did the authors do isotype control? And can they show how much of PD1+ population goes on neutrophils, and how much on all the other populations?

To address this issue, we performed additional analyses to assess the distribution of PD-L1 expression on CD45+CD11B+ leukocytes. These new results, detailed on Page 9, lines 245-250, and now presented in Supplemental Figure 6, demonstrate that PD-L1 expression is predominantly enriched in neutrophils compared to other immune subsets. This observation further reinforces our conclusion that neutrophils represent a major source of PD-L1 in our experimental model.

To ensure the robustness of these findings, we also included FMO controls for PD-L1 staining in the newly added Supplemental Figure S6. These controls validate the specificity of our gating strategy and confirm the reliability of the detected PD-L1 signal. The corresponding description has been added to the Results section (Page 9, Lines 245-250) as follows: ``First, we observed that only the MAFLD diet caused a significant increase in PD-L1 expression in CD45+CD11b+ leukocytes after LPS challenge (Fig. S6C). We observed that within this population, neutrophils predominate in their expression when compared to monocytes (Fig. 6SA, Fig. 6SB, and Fig. 6SD). Furthermore, PD-L+1 neutrophils showed an exacerbated migration of PD-L1+ neutrophils towards the liver (Fig. 6A and 6B)”

(7) In Figure 6D it is interesting that there is not an increase in PD-L1+ neutrophils in LPS HFCD IFNg+/+ mice in comparison to LPS chow IFNg+/+ mice, since those should be like WT mice (Figure 6A going from 50% to 97%) and so an increase should be seen?

The apparent difference between Figures 6A and 6D likely reflects inter-experimental variability rather than a biological discrepancy. Although the absolute percentages of PD-L1⁺ neutrophils varied slightly among independent experiments, the overall phenotype and trend were consistently maintained namely, that PD-L1 expression on neutrophils is enhanced in response to LPS stimulation and modulated by IFNγ signaling. Thus, the data shown in Figure 6D are representative of this consistent phenotype despite minor quantitative variation.

(8) In Figure 7 do the authors have isotype control for TNFa because gating seems a bit random so an isotype control graph would help a lot as supplementary information, in order to make the figure more persuasive

To address the concern regarding gating in Figure 7, we have included the FMO showing TNFα as a histogram Supplementary Figure 8gG. These control reaffirm the accuracy and reliability of our gating strategy for TNFα, further supporting the robustness of our data. The corresponding description has been added to the Results section (Page 9, Lines 272-274) as follows:`` We observed an exacerbated TNF-α expression by PD-L1+ neutrophils from MAFLD when compared to control chow animals (Fig. 7A, Fig. 7B, Fig. 7D, and Fig8SG).

(9) Figure 6C IFNg+/+ mice on CHOW +LPS is same as Figure 8E mice chow +LPS but just with different numbers. Can the authors explain this?

Although the data points in Figures 6C and 8E may appear similar, we confirm that they originate from entirely independent experiments and represent distinct datasets. To enhance clarity and avoid any potential confusion, we have adjusted the figure presentation and sizing in the revised manuscript. These changes make it clear that the datasets, while comparable, are derived from separate experimental replicates.

(10) Figure 1E chow B6+LPS is the same as Figure 5D B6+LPS but should they be different since those should be two different experiments?

We confirm that Figures 1E and 5D correspond to data obtained from independent experiments. Although the experimental conditions were similar, each dataset was generated and analyzed separately to ensure the reproducibility and robustness of our results.

Reviewer #2 (Recommendations for the authors):

(1) Why did you look at kidney injury in Figure 1D? I think this should be explained a little.

We assessed kidney injury alongside ALT, a marker of liver damage, because both the liver and kidneys are among the primary organs affected during sepsis and endotoxemia. This rationale has been added to the manuscript (page 5, lines 129–131): “Remarkably, compared to the Chow group, HFCD mice exposed to LPS did not show greater changes in other organs commonly affected by endotoxemia, such as the kidneys (Figure 1D).” By evaluating markers of injury in both organs, we aimed to determine whether our physiopathological condition was liver-specific or indicative of broader systemic injury.

(2) I know Figure 2C isn't your data, but why are there so few NK cells, considering NK cells are a resident liver cell type? Doesn't that also bring into question some of your data if there are so few NK cells? And the IFNG expression (2E) looks to mostly come from T-cells (CD8?).

The data shown in Figure 2C were reanalyzed from a separate NAFLD model based on a 60% high-fat diet. Although this model differs from ours, the observed low number of NK cells is consistent with expectations for animals subjected solely to a hyperlipidic diet, which primarily provides an inflammatory stimulus that promotes recruitment rather than maintaining high baseline NK cell numbers.

In our experimental model, these observations align with published data. Specifically, liver tissue from NAFLD animals typically exhibits low baseline NK cell numbers, but upon LPS challenge, there is a marked increase in NK cell recruitment to the liver. This dynamic illustrates the interplay between dietinduced inflammation and immune cell recruitment in our experimental context and supports the interpretation of our IFNγ data.

(3) In your methods, I think you didn't explain something. You said LPS was administered to 56 week old mice, but that HFCD diet was started in 5-6 week old mice and lasted 2 weeks, then LPS was administered. So LPS administration happened when the mice were 7-8 weeks old, right?

We thank the reviewer for pointing out this inconsistency in our Methods section. The reviewer is correct: the HFCD diet was initiated in 5–6-week-old mice, and LPS was administered after 2 weeks on the diet, such that LPS challenge occurred when the mice were 7–8 weeks old.

We have revised the Methods section (add page 15-16, lines 474–480).  to clarify this timeline and ensure it is accurately described in the manuscript. The corresponding description has been added to the Materials and Methods section (Page 14, Lines 436-442) as follows: “Lipopolysaccharide (LPS; Escherichia coli (O111:B4), L2630, Sigma-Aldrich, St. Louis, MO, USA) was administered intraperitoneally (i.p.; 10 mg/kg) in C57BL/6, CCR2 -/-, IFN-/-, and TNFR1R2 -/- mice. The HFCD was initiated in 5–6 week-old mice, and LPS was administered after 2 weeks on the diet, meaning that LPS administration occurred when the mice were 7–8 weeks old, with body weights ranging from 22 to 26 g. LPS was previously solubilized in sterile saline and frozen at -70°C. The animals were euthanized 6 hours after LPS administration”.

(4) Throughout the manuscript, I would consider changing the term NAFLD to something else. I think HFCD diet is a closer model to NASH, so there needs to be some discussion on that. And the field is changing these terms, so NAFLD is now MASLD and NASH is now MASH.

We appreciate the reviewer’s comment regarding the terminology and disease classification. In our experimental conditions, the animals were subjected to a high-fat, choline-deficient (HFCD) diet for only two weeks, a period considered very early in the progression of diet-induced liver disease. At this stage, histological analysis revealed lipid accumulation in hepatocytes without evidence of hepatocellular injury, inflammation, or fibrosis. Therefore, our model more closely resembles the metabolic-associated fatty liver disease (MAFLD, formerly NAFLD) stage rather than the more advanced metabolic-associated steatohepatitis (MASH, formerly NASH).

Indeed, prolonged exposure to HFCD diets, typically 8 to 16 weeks, is required to induce the inflammatory and fibrotic features characteristic of MASH. Since our objective was to study the initial metabolic and immune alterations preceding overt liver injury, we believe that using the term MAFLD more accurately reflects the pathological stage represented in our model. Accordingly, we have revised the text to align with the updated nomenclature and disease context.

(6) I am concerned about over interpretation of the publicly available RNA-seq data in Figure 2. This data comes from human NAFLD patients with unknown endotoxemia and mouse models using a traditional high-fat diet model. So it is hard to compare these very disparate datasets to yours. Also, if these datasets have elevated IFNG, why does your model require LPS injection?

We thank the reviewer for their thoughtful comments regarding the interpretation of the RNA-seq data presented in Figure 2. We would like to clarify that the human NAFLD datasets referenced in our study do not specifically include patients with endotoxemia; rather, they focus on individuals with NAFLD alone.

Comparing data from human and murine MAFLD models, we observed that NK cells, T cells, and neutrophils are present and contribute to the hepatic inflammatory environment. Our reanalysis indicates that the elevations of IFNγ and TNF in NAFLD are primarily derived from NK cells, T cells, and myeloid cells, respectively.

In our experimental model, LPS administration was used to evaluate whether these immune populations particularly NK cells are further potentiated under a hyperinflammatory state, leading to exacerbated IFNγ production. This approach allows us to determine whether increased IFNγ contributes to worsening outcomes in NAFLD, providing mechanistic insights that cannot be obtained from static human or traditional mouse datasets alone.

(7) The zoom-ins for the histology (for example, Figure 1E) don't look right compared to the dotted square. The shape and area expanded don't match. And the cells in the zoom-in don't look exactly the same either.

We have thoroughly re-examined the histological sections and the corresponding zoom-ins, including the example in Figure 1E. Upon verification, we confirm that the zoom-ins accurately represent the highlighted areas indicated by the dotted squares. The apparent discrepancies in shape or cellular appearance are likely due to minor differences in orientation or cropping during figure preparation. Nevertheless, the content and regions depicted are consistent with the original sections.  

(8) Did the authors measure myeloid infiltration in the CCR2-/- mice? Did you measure Neutrophil infiltration in the TNF-Receptor KO mice?

Analysis of CD45+ cell migration in CCR2 knockout mice, as shown in Supplemental Figure 5C and 5D, demonstrates that the absence of CCR2 does not impair overall leukocyte migration. Similarly, assessment of neutrophil migration in TNF receptor (TNFR1/2) knockout mice, presented in Supplemental Figure 8A, shows that neutrophil trafficking is not affected in these animals. These results indicate that the respective knockouts do not compromise the migration of the analyzed immune populations, supporting the interpretations presented in our study.

(9) Regarding Methods for RNA-seq Analysis. Was the Mitochondrial percentage cutoff 0.8%, because that seems low. And was there not a Padj or FDR cutoff for the differential expression?

The mitochondrial percentage in our scRNA-seq analysis reflects the proportion of mitochondrial gene expression per cell, which serves as a quality control metric. A low mitochondrial gene expression percentage, such as the 0.8% cutoff used here, is indicative of highly viable cells.

For differential gene expression analysis, we employed the FindMarkers function in Seurat with standard parameters: adjusted p-value (Padj) < 0.05 and log2 fold change > 0.25 for upregulated genes, and adjusted p-value < 0.05 with log2 fold change < -0.25 for downregulated genes. These thresholds ensure robust identification of differentially expressed genes while balancing sensitivity and specificity.

(10) Regarding Methods for Flow Cytometry. How were IFNG and TNF staining performed? Was this an intracellular stain? Did you need to block secretion? TNF and IFNG antibodies have the same fluorophore (PE), so were these stainings and analyses performed separately?

Six hours after LPS challenge, non-parenchymal liver cells were isolated using Percoll gradient centrifugation. Because the animals were in a hyperinflammatory state induced by LPS, no in vitro stimulation was performed; all staining was carried out immediately after cell isolation. Detection of IFNγ and TNF was performed via intracellular staining using the Foxp3 staining kit (eBioscience). Due to both antibodies being conjugated to PE, IFN-γ and TNF-α staining and analyses were conducted in separate experiments. These distinct staining protocols and analyses are detailed in Supplemental Figures 10 and 11. The corresponding description has been added to the Materials and Methods section (Page 16, Lines 490-493) as follows: ``As animals were already in a hyperinflammatory state, no additional in vitro stimulation was required. Intracellular detection of IFN-γ and TNF-α was conducted using the Foxp3 staining kit (eBioscience). Since both antibodies were conjugated to PE, staining and analyses were performed in separate experiments``

Reviewer #3 (Recommendations for the authors):

(1) Achieving an NAFLD model/disease is the starting point of this study. I understand that a two-week HFCD diet period was applied due to the decrease in lymphocyte numbers. Was it enough to initiate NAFLD then? Or is it a milder metabolic disease? Which parameters have been evaluated to accept this model as a NAFLD model?

Indeed, the two-week HFCD diet induces an early-stage form of NAFLD, characterized by initial fat accumulation in the liver without significant hepatic injury. While this represents a milder metabolic phenotype, it is sufficient to study the inflammatory and immune responses associated with NAFLD. To validate this model, we assessed multiple parameters: liver weight, blood glucose levels, and collagen deposition. These measurements confirmed the presence of early-stage NAFLD features in the animals, providing a relevant and reliable context for investigating susceptibility to endotoxemia and immune cell dynamics. They are shown in Figure Suplementary 1 and the text was included in the manuscript (Page 5, Lines 116-117): “Mice fed HFCD showed no increase in liver weight and collagen deposition as evidenced by Picrosirius staining (Fig. S1A and Fig. S1C) ”.

(2) It is true that the CD274 gene (encoding PD-L1) and the IFNGR2 gene, corresponding to the IFNγ receptor, are among the upregulated genes when authors analyzed the publicly available RNAseq data but they are not the most significantly elevated genes. What is the reasoning behind this cherrypicking? Why are other high DEGs not analyzed but these two are analyzed?

We highlighted the expression of the IFN-γ receptor (IFNGR2) and CD274 (encoding PD-L1) in the publicly available RNA-seq data to align and corroborate these findings with the key results observed later in our study. To avoid redundancy, we chose to present these genes in the initial figures as they are directly relevant to the subsequent analyses. Regarding the broader analysis of human RNA-seq data, our primary objective was to identify enriched biological processes and pathways, which served as a foundation for the focus and direction of this study.

(3) Figures 3C-3G: I understand that IFNg-/- and NFR1R2a-/- mice are not showing elevated liver damage but it may simply be because of the non-responsiveness to the LPS challenge. I suggest using a different challenge or recovery experiments with the cytokines to show that the challenge is successful and results are caused by NAFLD, truly. The same goes for Figure 6: Looking at Figure 6D one may think that IFNg deficiency alters the LPS response independent of the diet condition (or NAFLD condition).

We appreciate the reviewer’s insightful comment and fully understand the concern regarding the potential non-responsiveness of IFN-γ⁻/⁻ and TNFR1R2a⁻/⁻ mice to the LPS challenge. To address this point and confirm that these knockout animals are indeed responsive to LPS stimulation, we conducted an additional set of ex vivo experiments.

Specifically, WT and cytokine-deficient (IFN-γ⁻/⁻) mice were fed either Chow or HFCD for two weeks, after which spleens were collected, and splenocytes were challenged in vitro with LPS. We then quantified TNF, IFN, and IL-6 production to confirm that these mice are capable of mounting cytokine responses upon LPS stimulation.

Due to current breeding limitations and a temporary issue in colony maintenance of TNF-deficient mice, we were unable to include TNFR1R2a⁻/⁻ animals in this additional experiment. Nevertheless, we prioritized performing the analysis with the available knockout line to avoid leaving this important point unaddressed.

These additional data demonstrate that IFN-γ-deficient mice remain responsive to LPS, reinforcing that the differences observed in vivo are related to the NAFLD condition rather than a lack of LPS responsiveness.

(4) Figure 1 vs Figure 4: Rag-/- mice seem more susceptible to LPS-derived death even after normal conditions. But If I compare the survival data between Figure 1 and Figure 4, Rag-/- HFCD diet mice seem to be doing better than wt mice after LPS treatment. (1 day survival vs 2 days survival). How do you explain these different outcomes?

We thank the reviewer for this insightful question regarding the survival data in Figures 1 and 4. Although there is a one-day difference in survival outcomes, Rag-/- mice consistently exhibit increased susceptibility to LPS-induced mortality can influence the exact survival timing. Nonetheless, across all experiments, Rag-/- mice display a reproducible phenotype of heightened sensitivity to LPS challenge, which is supported by multiple independent observations in our study.

(5) How do you explain Figure 4J in connection to the observation presented with Figure 7: TNFa tissue levels, even though significant, seem very similar between the conditions?

We would like to clarify that the animals in this study are in a metabolic syndrome state, with early-stage NAFLD characterized by hepatic fat accumulation without significant tissue injury, as shown in Figure 1C.

Under these conditions, the LPS challenge triggers an exacerbated inflammatory response, leading to increased secretion of IFN-γ and TNF-α, primarily from NK cells and neutrophils. While TNFα levels may appear visually similar across conditions, the HFCD mice exhibit a heightened predisposition for an amplified immune response compared to chow-fed mice. This difference is consistent with the functional outcomes observed in our study and highlights the diet-specific sensitization of the immune system.

Author response:

We will extend and clarify the text of the paper according to the suggestions of the reviewers. In particular we will extend the description and discussion of the calcium chelator approach, re-patching and multiple probability fluctuation analysis. We will also include in the Results section that volume-averaged calcium signals were measured and extend the description about measurement of the resting calcium and variability between boutons. Literature will be included and discussed as suggested.

In order to avoid any misunderstandings, we will also make it clearer that recordings from

L5PN – L5PN synapses in S1 were published in our preceding papers (Bornschein et al., 2019a, b), but that these data were partially reanalyzed for the comparison with recordings from L5PN – L5PN synapses in PFC (this paper). We will also emphasize that the recordings from L2/3 to L5PN synapses in S1 and PFC were made directly in the present study. We will include a supplementary table, which explicitly shows for each figure which data are from Bornschein et al. (2019a, b) and which data were obtained in the present study. 

We will consider all points of the reviewers and the recommendations of the editors in detail in the revised manuscript and/or our pointwise response.

We recognized one factual error in the public reviews:

Reviewer 2, point 7: “Methods: The authors use Student's t-test for data comparison. The authors should verify that the data distribution was indeed normal, e.g. by using a Shapiro-Wilk test. If this is not the case, non-parametric tests should be used.”

A detailed description of the statistics, including test for normality, is given in the Methods section. In particular we wrote in the Methods: “Normality was tested using the Shapiro-Wilk Test. (…) To compare pre- and post-treatment data the paired t-test or the Wilcoxon signed rank test (WSR) was used, depending on the distribution of the data. (…)”

To further emphasize that the data was tested for normal distribution, we have also extended the description of the statistical tests in the figure legends.

Bornschein G, Brachtendorf S, Schmidt H (2019a) Developmental increase of neocortical  presynaptic efficacy via maturation of vesicle replenishment. Front Synaptic Neurosci 11:36.

Bornschein G, Eilers J, Schmidt H (2019b) Neocortical high probability release sites are formed by distinct Ca2+ channel-to-release sensor topographies during development. Cell Rep 28:1410-1418 e1414.