Reviewer #3 (Public review):

Summary:

This study examines the roles of Rab10 and Rab4 proteins in structural long-term potentiation (sLTP) and AMPA receptor (AMPAR) trafficking in hippocampal dendritic spines using various different methods and organotypic slice cultures as the biological model.<br /> The paper shows that Rab10 inactivation enhances AMPAR insertion and dendritic spine head volume increase during sLTP, while Rab4 supports the initial stages of these processes. The key contribution of this study is identifying Rab10 inactivation as a previously unknown facilitator of AMPAR insertion and spine growth, acting as a brake on sLTP when active. Rab4 and Rab10 seems to be playing opposing roles, suggesting a somewhat coordinated mechanism that precisely controls synaptic potentiation, with Rab4 facilitating early changes and Rab10 restricting the extent and timing of synaptic strengthening.

Strengths:

The study combines multiple techniques such as FRET/FLIM imaging, pharmacology, genetic manipulations and electrophysiology to dissect the roles of Rab10 and Rab4 in sLTP. The authors developed highly sensitive FRET/FLIM-based sensors to monitor Rab protein activity in single dendritic spines. This allowed them to study the spatiotemporal dynamics of Rab10 and Rab4 activity during glutamate uncaging induced sLTP. They also developed various controls to ensure the specificity of their observations. For example, they used a false acceptor sensor to verify the specificity of the Rab10 sensor response.

This study reveals previously unknown roles for Rab10 and Rab4 in synaptic plasticity, showing their opposing functions in regulating AMPAR trafficking and spine structural plasticity during LTP.

Weaknesses:

In the first round of revision I raised these points:

(1) In sLTP, the initial volume of stimulated spines is an important determinant of induced plasticity. To address changes in initial volume and those induced by uncaging, the authors present Extended Data Figure 2. In my view, the methods of fitting, sample selection, or both may pose significant limitations for interpreting the overall results. While the initial spine size distribution for Rab10 experiments spans ~0.1-0.4 fL (with an unusually large single spine at the upper end), Rab4 spine distribution spans a broader range of ~0.1-0.9 fL. If the authors applied initial size-matched data selection or used polynomial rather than linear fitting, panels a, b, e, f, and g might display a different pattern. In that case, clustering analysis based on initial size may be necessary to enable a fair comparison between groups-not only for this figure but also for main Figures 2 and 3.

- The authors responded to this point as follows: For sensor uncaging experiments, we usually uncaged glutamate at large mushroom spines because we need to have a good signal-to-noise ratio. We just happen to choose these spines with different initial sizes for Rab4 sensor and Rab10 sensor uncaging experiments.

Even if they happen to choose these spine sizes, it is possible to compare only those that match in size. This does not require any additional experiments. Because of this, I do not find this response satisfactory.

(2) Another limitation is the absence of in vivo validation, as the experiments were performed in organotypic hippocampal slices, which may not fully replicate the complexity of synaptic plasticity in an intact brain, where excitatory and inhibitory processes occur concurrently. High concentrations of MNI-glutamate (4 mM in this study) are known to block GABAergic responses due to its antagonistic effect on GABA-A receptors, thereby precluding the study of inhibitory network activity or connectivity, which is already known to be altered in organotypic slice cultures.

- I found the Authors following response reasonable and useful:

We appreciate the reviewer's comments and would like to clarify that we have conducted experiments in acute slices for LTP using conditional Rab10 knockout (Fig. 4k, 4l), and we obtained similar results. Additionally, we have recently published findings on the behavioral deficits observed in heterozygous Rab10 knockout mice (PubMed 37156612). These studies further support our conclusions and provide additional context for our findings.

Author response:

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

Reviewer #1 (Public review):

Summary:

Wang et al. created a series of specific FLIM-FRET sensors to measure the activity of different Rab proteins in small cellular compartments. They apply the new sensors to monitor Rab activity in dendritic spines during induction of LTP. They find sustained (30 min) inactivation of Rab10 and transient (5 min) activation of Rab4 after glutamate uncaging in zero Mg. NMDAR function and CaMKII activation are required for these effects. Knockdown of Rab4 reduced spine volume change while knockdown of Rab10 boosted it and enhanced functional LTP (in KO mice). To test Rab effects on AMPA receptor exocytosis, the authors performed FRAP of fluorescently labeled GluA1 subunits in the plasma membrane. Within 2-3 min, new AMPARs appear on the surface via exocytosis. This process is accelerated by Rab10 knock-down and slowed by Rab4 knock-down. The authors conclude that CaMKII promotes AMPAR exocytosis by i) activating Rab4, the exocytosis driver and ii) inhibiting Rab10, possibly involved in AMPAR degradation.

Strengths:

The work is a technical tour de force, adding fundamental insights to our understanding of the crucial functions of different Rab proteins in promoting/preventing synaptic plasticity. The complexity of compartmentalized Ras signaling is poorly understood and this study makes substantial inroads. The new sensors are thoroughly characterized, seem to work very well, and will be quite useful for the neuroscience community and beyond (e.g. cancer research). The use of FLIM for read-out is compelling for precise activity measurements in rapidly expanding compartments (i.e., spines during LTP).

Thank you for the evaluation.

Weaknesses:

The interpretation of the FRAP experiments (Figure 5, Ext. Data Figure 13) is not straightforward as spine volume and surface area greatly expand during uncaging. I appreciate the correction for the added spine membrane shown in Extended Data Figure 14i, but shouldn't this be a correction factor (multiplication) derived from the volume increase instead of a subtraction?

We thank the reviewer for this question. The fluorescence change should reflect a subtraction of surface area, as SEP-GluA1 is only fluorescent on the cell surface, unlike cytosolic mCherry, whose fluorescence intensity is proportional to spine volume. Therefore, the overall fluorescence change (ΔF) should be the addition of the contribution from AMPAR trafficking (ΔF_t) and the change in surface area (ΔS) multiplied by the remaining SEP-GluA1 fluorescence per unit area (f):

ΔF = ΔF_t + fΔS

Since fluorescence immediately after photobleaching (before AMPAR trafficking happens), F_o, is given by fS (S is the surface area of the spine):

ΔF/F_o = ΔF_t/ F_o + fΔS / fS

\= ΔF_t/fS + ΔS/S

Assuming that the surface area change (ΔS/S) is the volume change (ΔV/V) to the power of 2/3, the contribution of the AMPAR trafficking can be calculated as:

ΔF_t/F = ΔF/F – (Δ<sup>V/V)^2/3

This is the reason that we subtracted the contribution of the spine surface area. We have discussed this in the updated method section.

Also, experiments were not conducted or analyzed blind, risking bias in the selection/exclusion of experiments for analysis. This reduces my confidence in the results.

We acknowledge the reviewer's concern regarding the lack of blinding in our experiments. However, it is challenging to conduct blinded experiments for certain types of studies, such as sensor screening for a protein family, where we do not have expected results or a specific hypothesis prior to the experiments. In these cases, our primary readout is whether the sensor indicates any activity change upon stimulation.

To address this concern, after identifying that Rab10 is inactivated during structural LTP (sLTP) and is likely important for inhibiting spine structural LTP, we performed blinded electrophysiology experiments and obtained similar results (deletion of Rab10 from Camk2a-positive neurons leads to enhanced LTP; Fig. 4k, 4l).

Reviewer #2 (Public review):

Summary:

Wang et al. developed a set of optical sensors to monitor Rab protein activity. Their investigation into Rab activity in dendritic spines during structural long-term plasticity (sLTP) revealed sustained Rab10 inactivation (>30min) and transient Rab4 activation (~5 min). Through pharmacological and genetic manipulation to constitutively activate or inhibit Rab proteins, they found that Rab10 negatively regulates sLTP and AMPA receptor insertion, while Rab4 positively influences sLTP but only in the transient phase. The optical sensors provide new tools for studying Rab activity in cells and neurobiology. However, a full understanding of the timing of Rab activity will require a detailed characterization of sensor kinetics.

Strengths:

(1) Introduction of a series of novel sensors that can address numerous questions in Rab biology.

(2) Multiple methods to manipulate Rab proteins to reveal the roles of Rab10 and rab4 in LTP.

(3) Discovery of Rab4 activation and Rab10 inhibition with different kinetics during sLTP, correlating with their functional roles in the transient (Rab4) and both transient and sustained (Rab10) phases of sLTP.

Thank you for the positive evaluation.

Weaknesses:

(1) Lack of characterization of sensor kinetics, making it difficult to determine if the observed Rab kinetics during sLTP were due to sensor behavior or actual Rab activity.

We estimated that the kinetics of the sensors for Rab4 and Rab10 are within a few minutes. For Rab4, we observed rapid increase and decrease of the activation in response to glutamate uncaging. Thus, this would be the upper limit of the ON/OFF time constants of Rab4. For Rab10, we observed a rapid dissociation of the sensor in response to sLTP induction within ~1 min. This means that the donor and acceptor molecules are quickly dissociated during the process. Thus, the off kinetics of the sensor is within the range of minute. Meanwhile, we have the on-kinetics from Rab10 activation (donor/accepter association) in response to NMDA application and again this is within a few minutes. Given these rapid sensor kinetics in neurons, our observation of the sustained inactivation of Rab10 should reflect the true behavior of Rab10, rather than just the sensor’s response.

We revised our manuscript discussion session as follows:

“Understanding the kinetics of Rab4 and Rab10 sensors is essential for interpreting their actual activity during sLTP. The Rab4 sensor exhibits a rapid rise and fall in activation (Fig. 3), indicating ON/OFF times of less than a few minutes. In contrast, the Rab10 sensor rapidly dissociates during sLTP induction (Fig. 2), with OFF kinetics occurring within one minute and fast ON kinetics in response to NMDA (Fig. 1j). Given these rapid kinetics, the observed sustained inactivation of Rab10 likely reflects its true behavior rather than sensor dynamics.”

(2) It is crucial to assess whether the overexpression of Rab proteins as reporters, affects Rab activity and cellular structure and physiology (e.g. spine number and size).

While we did not measure the effects of Rab sensor overexpression on Rab activity or cellular structure and physiology, we showed that sLTP is similar in neurons expressing sensors. This suggests that the overexpression of Rab sensors does not significantly disrupt signaling required for sLTP.

(3) The paper does not explain the apparently different results between NMDA receptor activation and glutamate uncaging. NMDA receptor activation increased Rab10 activity, while glutamate uncaging decreased it. NMDA receptor activation resulted in sustained Rab4 activation, whereas glutamate uncaging caused only brief activation of about 5 minutes. A potential explanation, ideally supported by data, is needed.

It is a long-standing question in the field why simple NMDA receptor activation by bath application of NMDA does not induce LTP, but instead induce LTD. Rab proteins are regulated by many GEFs and GAPs and identifying different mechanisms requires completely different techniques, such as molecular screening. While our manuscript provides some insights into this question by showing that they provide opposing signals for Rab10, we believe that identifying exact mechanisms would be out of the scope of this manuscript.

(4) There is a discrepancy between spine phenotype and sLTP potential with Rab10 perturbation. Rab10 perturbation affected spine density but not size, suggesting a role in spinogenesis rather than sLTP. However, glutamate uncaging affected sLTP, and spinogenesis was not examined. Explaining the discrepancy between spine size and sLTP potential is necessary. Exploring spinogenesis with glutamate uncaging would strengthen these results. Additionally, Figure 4j shows no change in synaptic transmission with Rab10 knockout, despite an increase in spine density. An explanation, ideally supported by data, is needed for the unchanged fEPSP slope despite an increase in spine density.

We thank the reviewer for raising these important questions. In our findings, shRNA-mediated knockdown of Rab10 did not alter spine size but did increase spine density in the basal state (Extended Data Fig. 11i). This suggests that Rab10 may restrict spinogenesis without affecting spine size. Conversely, sLTP induction via glutamate uncaging is an activity-dependent process that may involve different molecular mechanisms. The signal interplay between spinogenesis and sLTP and how the exact roles of Rab signaling in different modalities of plasticity would remain elusive for the future study.

The lack of change in synaptic transmission with Rab10 knockout, despite the increase in spine density from Rab10 shRNA knockdown, may be due to different preparation and developmental stages: spine density measurements were conducted with shRNA knockdown in organotypic slices (sliced at P6-8, DIV 9-13), while electrophysiological recordings were performed in knockout mice in acute slices from adult animals (P30-60).

(5) Spine volume was imaged using acceptor fluorophores (mCherry, or mCherry/Venus) at 920nm, where the two-photon cross-section of mCherry is minimal. 920nm was also used to excite the donor fluorophore, hence the spine volume measurement based on total red channel fluorescence is the sum of minimal mCherry fluorescence from direct 920nm excitation, bleed-through from the green channel, and FRET. This confounded measurement requires correction and clarification.

We assumed that the most of fluorescence is from direct excitation of mCherry at 920 nm. The contribution from the bleed-through from mEGFP-Rab (~3%) and from FRET changes (~20%) may influence the volume measurements. However, since we observed similar fluorescence changes in the green and red channels, these factors would have only a minor impact on our results (Extended Data Fig. 6a, 6d). Also, please note that the volume change in neurons expressing sensors is just to check if the volume change is normal, and not a major point of this manuscript.  We clarified this in the method section as:

“For the sensor experiments, we used mCherry as a volume indicator. We acknowledge that contributions from bleed-through from mEGFP-Rab (approximately 3%) and FRET changes (around 20%) could affect the volume measurements. However, since we observed similar fluorescence changes in both the green and red channels, we believe these factors have a minimal impact on our results (Extended Data Fig. 6a, 6d).”

Reviewer #3 (Public review):

Summary:

This study examines the roles of Rab10 and Rab4 proteins in structural long-term potentiation (sLTP) and AMPA receptor (AMPAR) trafficking in hippocampal dendritic spines using various different methods and organotypic slice cultures as the biological model.

The paper shows that Rab10 inactivation enhances AMPAR insertion and dendritic spine head volume increase during sLTP, while Rab4 supports the initial stages of these processes. The key contribution of this study is identifying Rab10 inactivation as a previously unknown facilitator of AMPAR insertion and spine growth, acting as a brake on sLTP when active. Rab4 and Rab10 seem to be playing opposing roles, suggesting a somewhat coordinated mechanism that precisely controls synaptic potentiation, with Rab4 facilitating early changes and Rab10 restricting the extent and timing of synaptic strengthening.

Strengths:

The study combines multiple techniques such as FRET/FLIM imaging, pharmacology, genetic manipulations, and electrophysiology to dissect the roles of Rab10 and Rab4 in sLTP. The authors developed highly sensitive FRET/FLIM-based sensors to monitor Rab protein activity in single dendritic spines. This allowed them to study the spatiotemporal dynamics of Rab10 and Rab4 activity during glutamate uncaging-induced sLTP. They also developed various controls to ensure the specificity of their observations. For example, they used a false acceptor sensor to verify the specificity of the Rab10 sensor response.

This study reveals previously unknown roles for Rab10 and Rab4 in synaptic plasticity, showing their opposing functions in regulating AMPAR trafficking and spine structural plasticity during LTP.

Thank you for the positive evaluation.

Weaknesses:

In sLTP, the initial volume of stimulated spines is an important determinant of induced plasticity. To address changes in initial volume and those induced by uncaging, the authors present Extended Data Figure 2. In my view, the methods of fitting, sample selection, or both may pose significant limitations for interpreting the overall results. While the initial spine size distribution for Rab10 experiments spans ~0.1-0.4 fL (with an unusually large single spine at the upper end), Rab4 spine distribution spans a broader range of ~0.1-0.9 fL. If the authors applied initial size-matched data selection or used polynomials rather than linear fitting, panels a, b, e, f, and g might display a different pattern. In that case, clustering analysis based on initial size may be necessary to enable a fair comparison between groups not only for this figure but also for main Figures 2 and 3.

We thank the reviewer for these questions. For sensor uncaging experiments, we usually uncaged glutamate at large mushroom spines because we need to have a good signal-to-noise ratio. We just happen to choose these spines with different initial sizes for Rab4 sensor and Rab10 sensor uncaging experiments.

Another limitation is the absence of in vivo validation, as the experiments were performed in organotypic hippocampal slices, which may not fully replicate the complexity of synaptic plasticity in an intact brain, where excitatory and inhibitory processes occur concurrently. High concentrations of MNI-glutamate (4 mM in this study) are known to block GABAergic responses due to its antagonistic effect on GABA-A receptors, thereby precluding the study of inhibitory network activity or connectivity [1], which is already known to be altered in organotypic slice cultures.

(1) https://www.frontiersin.org/journals/neural-circuits/articles/10.3389/neuro.04.002.2009/full

We appreciate the reviewer's comments and would like to clarify that we have conducted experiments in acute slices for LTP using conditional Rab10 knockout (Fig. 4k, 4l), and we obtained similar results. Additionally, we have recently published findings on the behavioral deficits observed in heterozygous Rab10 knockout mice (PubMed 37156612). These studies further support our conclusions and provide additional context for our findings.

Recommendations for the authors:

From the Senior/Reviewing Editor:

I apologize that this took longer than intended. As you will see from the reviews there was some disagreement on several points. There was some disagreement among reviewers as to the strength of the evidence with some characterizing it as "compelling," "convincing," or "solid" while others felt the characterization of the sensors was "incomplete" and that this could have affected some of the conclusions. After extensive discussion, reviewers agreed that there was a valid concern that the conclusion that Rab10 activation is sustained could reflect a feature of the sensor. If Rab10/RBD dissociation rate were very low, and the affinity of binding were very high, this could lead to an incorrect estimate of the sustained binding due to sensor kinetics, not Rab10 activation. It was noted that this has been seen in other sensors previously (e.g. first generation PKA activity sensors), which the developers altered in later generations to increase reversibility and off kinetics of the sensor.

There was also discussion of how this might be addressed and we would be interested in your comments on this issue. It was suggested that it might be helpful to revise Figure 2b to show binding fraction dynamics separately for each spine (to determine whether any actually return to baseline). Subsequently, clustering of these binding dynamics into two groups could be summarized in a version of Fig. 2e for each cluster. Differences in spine volume dynamics between these clusters would provide a measure of how strongly Rab10 binding correlates with spine volume. If they never go back to baseline, some extra experiments with longer post-plasticity induction (150mins instead of 35), might show if any reversible Rab10 binding exists post-LTP induction.

An alternative suggestion was to measure the time course in the presence of a GAP or GEF, which should alter the kinetics.

Thanks for the comments. It is important that the inactivation is observed as the dissociation of the donor and acceptor of the sensor.  Thus, the fact that the sensor rapidly decreases in response to uncaging means that they have rapid off kinetics. In addition, we provide evidence of a rapid increase of Rab10 in response to NMDA application, suggesting that kinetics is also rapid. We added discussion about this in the revised manuscript as:

“Understanding the kinetics of Rab4 and Rab10 sensors is essential for interpreting their actual activity during sLTP. The Rab4 sensor exhibits a rapid rise and fall in activation (Fig. 3), indicating ON/OFF times of just a few minutes. In contrast, the Rab10 sensor rapidly dissociates during sLTP induction (Fig. 2), with OFF kinetics occurring within one minute and fast ON kinetics in response to NMDA (Fig. 1j). Given these rapid kinetics, the observed sustained inactivation of Rab10 likely reflects its true behavior rather than sensor dynamics.”

There was also further discussion of the nature of the "spine volume" signal, given the fact that the two-photon cross-section of mCherry is minimal at 920nm. It was suggested that this could be due to direct acceptor excitation rather than FRET, but there was agreement that further clarity on this issue would be valuable.

We assumed that the most of fluorescence is from direct excitation of mCherry at 920 nm. The contribution from the bleed-through from mEGFP-Rab (~3%) and from FRET changes (~20%) may influence the volume measurements. However, since we observed similar fluorescence changes in the green and red channels, these factors would have only a minor impact on our results (Extended Data Fig. 6a, 6d). Also, please note that the volume change in neurons expressing sensors is just to check if the volume change is normal, and not a major point of this manuscript.  We clarified this in the method section as:

“For the sensor experiments, we used mCherry as a volume indicator. We acknowledge that contributions from bleed-through from mEGFP-Rab (approximately 3%) and FRET changes (around 20%) could affect the volume measurements. However, since we observed similar fluorescence changes in both the green and red channels, we believe these factors have a minimal impact on our results (Extended Data Fig. 6a, 6d).”

The equations in the methods section differ from other papers by the same lab (e.g. Laviv et al, Neuron 2020, Tu et al. Sci Adv. 2023, Jain et al. Nature 2024). Please clarify which equations are correct.

Thanks for pointing this out. In fact, some of the equations in this manuscript were wrong, and we have corrected them in the method session.

Reviewer #1 (Recommendations for the authors):

The effects of Rab knockdown affect both spine volume expansion and AMPAR recovery in a very similar fashion. To explain this tight coupling, the authors suggest that the availability of membrane could be a limiting factor for spine enlargement. However, some Rabs are known to affect actin dynamics, which could also explain the dual effects on AMPAR exocytosis and spine enlargement. It is not easy to come up with an experiment to differentiate between these alternative explanations, as blocking actin polymerization would likely affect exocytosis, too. The authors should consider/discuss the possibility that all of the observed Ras effects result from altered actin dynamics and that the lipid bilayer is sufficiently fluid to form a minimal surface around the expanding cytoskeleton.

Thanks for the suggestions. We included the discussion about the potential impact on the actin cytoskeleton by Rab10.

Typos: heterougenous, compartmantalization, chemaical, ballistically/biolistically (chose one).

Thanks for pointing out these typos. We have corrected them in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

(1) Venus shows pH sensitivity, which can be significant at synapses due to pH changes. Characterizing the pH sensitivity of the sensors is essential.

Thanks for the suggestions. We did not measure pH dependence, but the PKa of these fluorophores has already been published. PKa for EGFP and Venus are both 6.0, and it is unlikely that it influenced our measurements.

(2) Presenting individual data points within all bar graphs (e.g. Fig. 2c, 2d) would enhance data transparency.

Thanks for the suggestions. We now provide individual data points in the revised main figures.

(3) In Figure 1f: Rab5 GAP expression increased the binding fraction against expectations. In addition, clarifying the color scheme in Figure 1 is needed. Are GAPs supposed to be blue/green, and GEFs red/orange? Figure 1f seems to contradict this color scheme.

Thanks for the suggestions. We clarified these issues.

(4) Quantification of the point spread function of the uncaging laser, response/settle time of the scan mirror during uncaging, and reason for changes in neighboring spines in many example images (e.g. Figure 2a, especially at 240 s; Figure 4a) would be important.

The laser is controlled by Pockels cells, which changes the laser intensity with microsecond resolution. The laser is parked for milliseconds during uncaging, much longer than the settling time of the mirror (~0.1 milliseconds). The point spread function of the uncaging laser is limited by the diffraction (~0.5 um). The uncaging spot size is mostly limited by the diffusion of uncaged glutamate, but our calcium imaging and CaMKII imaging show that the signaling is induced mostly in the stimulated spines (Lee et al., 2009; Chang et al., 2017, 2019).

(5) Please include traces for "false" sensors in stimulated spines in Figures 2b, 2e, 3b, and 3e.

The traces for the false sensors have been presented in Extended Data Fig. 3 and Extended Data Fig. 8.

(6) The traces in Figure 4k (fEPSP slope in response to theta burst stimulation, where there is a decrease in fEPSP slope followed by a gradual increase) differ from prior publications (e.g. PMID: 1359925, 3967730, 19144965, 20016099). An investigation and explanation for these differences are necessary.

We appreciate the reviewer’s comments. We performed the experiments blindly and did not try to find a condition providing control data similar to previous publications. The variations in fEPSP responses compared to prior publications may be attributed to several factors, including differences in experimental conditions such as the genetic background of the animals used, the specific protocols for theta burst stimulation, and variations in the preparation of the hippocampal slices.

(7) The title and text state that Rab10 inactivation promotes AMPAR insertion. It is unclear if this is a direct effect on AMPAR insertion or an indirect effect through membrane remodeling. Providing data to distinguish these possibilities or adjusting the title/text to reflect alternative interpretations would be beneficial.  

We appreciate the reviewer's feedback. To clarify, we have revised our terminology to use "AMPAR trafficking" instead of "AMPAR insertion", as it includes both insertion and other mechanisms of AMPAR movement within the cell.

(8) Please provide an explanation for the initial Rab10 inactivation observed in Figure 1j upon NMDA application.

The application of NMDA in Fig. 1j is similar to the commonly used chemical LTD induction protocol. We used this broad stimulation approach to test whether our sensors could report Rab activity changes in neurons upon strong stimulation. However, it is an entirely different stimulation approach from the sLTP induction protocol, thus resulting in different sensor activity changes.  We describe the phenomenon in the revised manuscript, but we believe that detailed analyses of Rab10 activation in response to NMDA application are beyond the scope of this manuscript.

(9) Please explain why the study focuses on Rab4 and Rab10 instead of other Rab proteins.

During our initial screening of sensors for various Rab proteins, we observed significant activity changes in the sensors for Rab4 and Rab10 upon sLTP induction. This suggested their potential relevance in synaptic processes, leading us to focus on understanding their specific roles in structural long-term potentiation.

Reviewer #3 (Recommendations for the authors):

(1) Although it might seem trivial, the definition of adjacent spine has not been made in the text. It would be nice to have it in the Methods section.

We included it in the Methods section as follows:

"The adjacent spine refers to the first or second spine located next to the stimulated spine, typically positioned opposite the stimulated spine. Additionally, the size of the adjacent spine must be sufficiently large for imaging."

(2) The transfection method has been mentioned as "ballistic" and "biolistic" transfection. You might want to use only one term. Additionally, you can add the equipment used (Bio-rad?) and pressure (psi) in the Methods section.

We use “biolistic” throughout the manuscript now. We also added the equipment and conditions used.

eLife Assessment

This study presents important findings on the role of pyramidal cells driving vasoconstriction in brain arteries through a COX-2/PGE2 pathway, with additional contributions from NPY (interneurons) and 20-HETE (astrocytes). Optogenetic stimulation of cortical pyramidal neurons induces vasoconstriction, potentially leading to oxygen and nutrient undersupply in regions with sustained activation - a mechanism potentially relevant under pathological conditions. The authors provide convincing evidence from brain slice experiments and some in vivo data from anesthetized animals, carefully discussing the strengths and limitations of both approaches.

Reviewer #1 (Public review):

SNeuronal activity spatiotemporal fine-tuning of cerebral blood flow balances metabolic demands of changing neuronal activity with blood supply. Several 'feed-forward' mechanisms have been described that contribute to activity-dependent vasodilation as well as vasoconstriction leading to a reduction in perfusion. Involved messengers are ionic (K+), gaseous (NO), peptides (e.g., NPY, VIP) and other messengers (PGE2, GABA, glutamate, norepinephrine) that target endothelial cells, smooth muscle cells, or pericytes. Contributions of the respective signaling pathways likely vary across brain regions or even within specific brain regions (e.g., across cortex) and are likely influenced by the brain's physiological state (resting, active, sleeping) or pathological departures from normal physiology.

The manuscript "Elevated pyramidal cell firing orchestrates arteriolar vasoconstriction through COX-2-derived prostaglandin E2 signaling" by B. Le Gac, et al. investigates mechanisms leading to activity-dependent arteriole constriction. Here, mainly working in brain slices from mice expressing channelrhodopsin 2 (ChR2) in all excitatory neurons (Emx1-Cre; Ai32 mice), the authors show that strong optogenetic stimulation of cortical pyramidal neurons is leading to constriction that is mediated through the cyclooxygenase-2 / prostaglandin E2 / EP1 and EP3 receptor pathway with contribution of NPY-releasing interneurons and astrocytes releasing 20-HETE. Specifically, using patch clamp, the authors show that 10-s optogenetic stimulation at 10 and 20 Hz leads to vasoconstriction (Figure 1), in line with a stimulation frequency-dependent increase in somatic calcium (Figure 2). The vascular effects were abolished in presence in TTX and significantly reduced in presence of glutamate receptor antagonists (Figure 3). The authors further show with RT-PCR on RNA isolated from patched cells that ~50% of analyzed cells express COX-1 or -2 and other enzymes required to produce PGE2 or PGF2a (Figure 4). Further, blockade of COX-1 and -2 (indomethacin), or COX-2 (NS-398) abolishes constriction. In animals with chronic cranial window that were anesthetized with ketamine and medetomidine, 10-s long optogenetic stimulation at 10 Hz leads to considerable constriction, which is reduced in presence of indomethacin. Blockade of EP1 and EP3 receptors leads to significant reduction of the constriction in slices (Figure 5). Finally, the authors show that blockade of 20-HETE synthesis caused moderate and NPY Y1 receptor blockade a complete reduction of constriction.

The mechanistic analysis of neurovascular coupling mechanisms as exemplified here will guide further in-vivo studies and has important implications for human neuroimaging in health and disease. Most of the data in this manuscript uses brain slices as experimental model which contrasts with neurovascular imaging studies performed in awake (headfixed) animals. However, the slice preparation allows for patch clamp as well as easy drug application and removal. Further, the authors discuss their results in view of differences between brain slices and in vivo observations experiments, including the absence of vascular tone as well as blood perfusion required for metabolite (e.g., PGE2) removal, and the presence of network effects in the intact brain. The manuscript and figures present the data clearly; regarding the presented mechanism, the data supports the authors conclusions. Some of the data was generated in vivo in head-fixed animals under anesthesia; in this regard, the authors should revise introduction and discussion to include the important distinction between studies performed in slices, or in acute or chronic in-vivo preparations under anesthesia (reduced network activity and reduced or blockade of neuromodulation, or in awake animals (virtually undisturbed network and neuromodulatory activity). Further, while discussed to some extent, the authors could improve their manuscript by more clearly stating if they expect the described mechanism to contribute to CBF regulation under 'resting state conditions' (i.e., in absence of any stimulus), during short or sustained (e.g., visual, tactile) stimulation, or if this mechanism is mainly relevant under pathological conditions; especially in context of the optogenetic stimulation paradigm being used (10-s long stimulation of many pyramidal neurons at moderate-high frequencies) and the fact that constriction leading to undersupply in response to strongly increased neuronal activity seems counterintuitive?

The authors have addressed all comments, and I appreciate their insightful discussion and revision of the manuscript.

Reviewer #2 (Public review):

Summary:

The present study by Le Gac et al. investigates the vasoconstriction of cerebral arteries during neurovascular coupling. It proposes that pyramidal neurons firing at high frequency lead to prostaglandin E2 (PGE2) release and activation of arteriolar EP1 and EP3 receptors, causing smooth muscle cell contraction. The authors further claim that interneurons and astrocytes also contribute to the vasoconstriction via neuropeptide Y (NPY) and 20-hydroxyeicosatetraenoic acid (20-HETE) release, respectively. The study mainly uses brain slices and pharmacological tools in combination with Emx1-Cre;Ai32 transgenic mice expressing the H134R variant of channelrhodopsin-2 (ChR2) in the cortical glutamatergic neurons for precise photoactivation. Stimulation with 470 nm light using 10-second trains of 5-ms pulses at frequencies from 1-20 Hz revealed small constrictions at 10 Hz and robust constrictions at 20 Hz, which were abolished by TTX and partially inhibited by a cocktail of glutamate receptor antagonists. Inhibition of cyclooxygenase-1 (COX-1) or -2 (COX-2) by indomethacin blocked the constriction both ex vivo (slices) and in vivo (pial artery), and inhibition of EP1 and EP3 showed the same effect ex vivo. Single-cell RT-PCR from patched neurons confirmed the presence of the PGE2 synthesis pathway. While the data are convincing, the overall experimental setting presents some limitations. How is the activation protocol comparable to physiological firing frequency? The delay (minutes) between the stimulation and the constriction appears contradictory to the proposed pathway, which would be expected to occur rapidly. The experiments are conducted in the absence of vascular "tone," which further questions the significance of the findings. Some of the targets investigated are expressed by multiple cell types, which makes the interpretation difficult; for example, cyclooxygenases are also expressed by endothelial cells. Finally, how is the complete inhibition of the constriction by the NPY Y1 receptor antagonist BIBP3226 consistent with a direct effect of PGE2 and 20-HETE in arterioles? Overall, the manuscript is well-written with clear data, but the interpretation and physiological relevance have some limitations. However, vasoconstriction is a rather understudied phenomenon in neurovascular coupling, and the present findings may be of significance in the context of pathological brain hypoperfusion.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Neuronal activity spatiotemporal fine-tuning of cerebral blood flow balances metabolic demands of changing neuronal activity with blood supply. Several 'feed-forward' mechanisms have been described that contribute to activity-dependent vasodilation as well as vasoconstriction leading to a reduction in perfusion. Involved messengers are ionic (K+), gaseous (NO), peptides (e.g., NPY, VIP), and other messengers (PGE2, GABA, glutamate, norepinephrine) that target endothelial cells, smooth muscle cells, or pericytes. Contributions of the respective signaling pathways likely vary across brain regions or even within specific brain regions (e.g., across the cortex) and are likely influenced by the brain's physiological state (resting, active, sleeping) or pathological departures from normal physiology.

The manuscript "Elevated pyramidal cell firing orchestrates arteriolar vasoconstriction through COX-2derived prostaglandin E2 signaling" by B. Le Gac, et al. investigates mechanisms leading to activitydependent arteriole constriction. Here, mainly working in brain slices from mice expressing channelrhodopsin 2 (ChR2) in all excitatory neurons (Emx1-Cre; Ai32 mice), the authors show that strong optogenetic stimulation of cortical pyramidal neurons leads to constriction that is mediated through the cyclooxygenase-2 / prostaglandin E2 / EP1 and EP3 receptor pathway with contribution of NPY-releasing interneurons and astrocytes releasing 20-HETE. Specifically, using a patch clamp, the authors show that 10-s optogenetic stimulation at 10 and 20 Hz leads to vasoconstriction (Figure 1), in line with a stimulation frequency-dependent increase in somatic calcium (Figure 2). The vascular effects were abolished in the presence of TTX and significantly reduced in the presence of glutamate receptor antagonists (Figure 3). The authors further show with RT-PCR on RNA isolated from patched cells that ~50% of analyzed cells express COX-1 or -2 and other enzymes required to produce PGE2 or PGF2a (Figure 4). Further, blockade of COX-1 and -2 (indomethacin), or COX-2 (NS-398) abolishes constriction. In animals with chronic cranial windows that were anesthetized with ketamine and medetomidine, 10-s long optogenetic stimulation at 10 Hz leads to considerable constriction, which is reduced in the presence of indomethacin. Blockade of EP1 and EP3 receptors leads to a significant reduction of the constriction in slices (Figure 5). Finally, the authors show that blockade of 20-HETE synthesis caused moderate and NPY Y1 receptor blockade a complete reduction of constriction.

The mechanistic analysis of neurovascular coupling mechanisms as exemplified here will guide further in-vivo studies and has important implications for human neuroimaging in health and disease. Most of the data in this manuscript uses brain slices as an experimental model which contrasts with neurovascular imaging studies performed in awake (headfixed) animals. However, the slice preparation allows for patch clamp as well as easy drug application and removal. Further, the authors discuss their results in view of differences between brain slices and in vivo observations experiments, including the absence of vascular tone as well as blood perfusion required for metabolite (e.g., PGE2) removal, and the presence of network effects in the intact brain. The manuscript and figures present the data clearly; regarding the presented mechanism, the data supports the authors' conclusions.

We thank the reviewer for his/her supportive comments as well as for pointing out pros and cons of the brain slice preparation.

Some of the data was generated in vivo in head-fixed animals under anesthesia; in this regard, the authors should revise the introduction and discussion to include the important distinction between studies performed in slices, or in acute or chronic in-vivo preparations under anesthesia (reduced network activity and reduced or blockade of neuromodulation, or in awake animals (virtually undisturbed network and neuromodulatory activity).

We have now added a paragraph in the introduction (lines 52-64) to highlight the distinction between ex vivo and in vivo models. We now also discuss that anesthetized animals exhibit slower NVC (Line 308-309).

Further, while discussed to some extent, the authors could improve their manuscript by more clearly stating if they expect the described mechanism to contribute to CBF regulation under 'resting state conditions' (i.e., in the absence of any stimulus), during short or sustained (e.g., visual, tactile) stimulation, or if this mechanism is mainly relevant under pathological conditions; especially in the context of the optogenetic stimulation paradigm being used (10-s long stimulation of many pyramidal neurons at moderate-high frequencies) and the fact that constriction leading to undersupply in response to strongly increased neuronal activity seems counterintuitive?

We now discuss more extensively the physiological relevance (lines 422-434 and 436-439) and the conditions where the described mechanisms of neurogenic vasoconstriction may occur.

We agree with the reviewer that vasoconstriction in response to a large increase in neuronal activity is counterintuitive as it leads to undersupply despite an increased energy demand. We now discuss its potential physio/pathological role in attenuating neuronal activity by reducing energy supply (lines 453-464).

Reviewer #2 (Public review):

Summary:

The present study by Le Gac et al. investigates the vasoconstriction of cerebral arteries during neurovascular coupling. It proposes that pyramidal neurons firing at high frequency lead to prostaglandin E2 (PGE2) release and activation of arteriolar EP1 and EP3 receptors, causing smooth muscle cell contraction. The authors further claim that interneurons and astrocytes also contribute to vasoconstriction via neuropeptide Y (NPY) and 20-hydroxyeicosatetraenoic acid (20-HETE) release, respectively. The study mainly uses brain slices and pharmacological tools in combination with Emx1Cre; Ai32 transgenic mice expressing the H134R variant of channelrhodopsin-2 (ChR2) in the cortical glutamatergic neurons for precise photoactivation. Stimulation with 470 nm light using 10-second trains of 5-ms pulses at frequencies from 1-20 Hz revealed small constrictions at 10 Hz and robust constrictions at 20 Hz, which were abolished by TTX and partially inhibited by a cocktail of glutamate receptor antagonists. Inhibition of cyclooxygenase-1 (COX-1) or -2 (COX-2) by indomethacin blocked the constriction both ex vivo (slices) and in vivo (pial artery), and inhibition of EP1 and EP3 showed the same effect ex vivo. Single-cell RT-PCR from patched neurons confirmed the presence of the PGE2 synthesis pathway.

While the data are convincing, the overall experimental setting presents some limitations. How is the activation protocol comparable to physiological firing frequency? 

As also suggested by Reviewer #1 we have now discussed more extensively the physiological relevance of our observations (lines 422-434 and 436-439).

The delay (minutes) between the stimulation and the constriction appears contradictory to the proposed pathway, which would be expected to occur rapidly. The experiments are conducted in the absence of vascular "tone," which further questions the significance of the findings. 

The slow kinetics observed ex vivo are probably due to the low recording temperature and the absence of pharmacologically induced vascular tone, as already discussed (lines 312-317). Furthermore, as recommended by reviewer #1, we have presented the advantages and limitations of ex vivo and in vivo approaches (lines 52-64).

Some of the targets investigated are expressed by multiple cell types, which makes the interpretation difficult; for example, cyclooxygenases are also expressed by endothelial cells.

Under normal conditions, endothelial cells only express COX-1 and barely COX-2, whose expression is essentially observed in pyramidal cells (see Tasic et al. 2016, Zeisel et al. 2015, Lacroix et al., 2015). As pointed out by Reviewer # 1, our ex vivo pharmacological data clearly indicate that vasoconstriction is mostly due to COX-2 activity, and to a much lesser extent to COX-1. Since it is well established that the previously described vascular effects of pyramidal cells are essentially mediated by COX-2 activity (Iadecola et al., 2000; Lecrux et al., 2011; Lacroix et al., 2015), we are quite confident that vasoconstriction described here is mainly due COX-2 activity of pyramidal cells.

Finally, how is the complete inhibition of the constriction by the NPY Y1 receptor antagonist BIBP3226 consistent with a direct effect of PGE2 and 20-HETE in arterioles? 

We agree with both reviewers that the complete blockade of the constriction by the NPY Y1 receptor antagonist BIBP3226 needs to be more carefully discussed. We have now included in the discussion the possible involvement of Y1 receptors in pyramidal cells, which could promote glutamate release and possibly COX-2, thereby contributing to PGE2 and 20-HETE signaling (lines 402-409).

Overall, the manuscript is well-written with clear data, but the interpretation and physiological relevance have some limitations. However, vasoconstriction is a rather understudied phenomenon in neurovascular coupling, and the present findings may be of significance in the context of pathological brain hypoperfusion.

We thank the reviewer for his/her comment and suggestions, which have helped us to improve our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Methods:

It is not clear if brain slices (or animals) underwent one, two, or several optogenetic stimulations - especially for experiments where 'control' is compared to 'treated' - does this data come from the same vessels (before and after treatment) or from two independent groups of vessels? If repeated stimulations are performed, do these repeated stimulations cause the same vascular response?

As indicated in the Materials and Methods section, line 543: “Only one arteriole was monitored per slice” implies that the comparisons between the ‘control’ and ‘treated’ groups were made from independent groups of vessels. To clarify this point, we have added “receiving a single optogenetic or pharmacological stimulation” to this sentence lines 543-544.

For in vivo experiments, animals underwent 10-20 optogenetic stimulations with a 5-minute interstimulus interval during an experiment lasting 2 hours for maximum. Trials from the same vessel were averaged (with a 0.1 s interpolation) for analysis, and the mean per vessels is presented in the graphics.

Figure 2:

Can the authors speculate about the cause for the slow increase in indicator fluorescence from minute 1.5 onward, which seems dependent on stimulation frequency? Is this increase also present when slices from a ChR2-negative animal undergo the same stimulation paradigm?

Rhod2 was delivered by the patch pipette as indicated in the Materials and Methods section (line 514). Although a period of “at least 15 min after passing in whole-cell configuration to allow for somatic diffusion of the dye” (line 551-552) was observed, this single-wavelength Ca2+ indicator likely continued to diffuse into the cells during the optical recording thereby, inducing a slight increase in delta F/F0, which is consistent with the positive slopes of the mean fluorescence changes observed during the 30-s control baseline (Fig. 2b).

Figure 4: Why did the authors include panel a) here? Also, do the authors observe that cells with different COX-1 or -2 expression profiles show different (electrical, morphological) properties?

The purpose of panel a) in Fig. 4 was to ensure the regular spiking electrophysiological phenotype of the pyramidal neurons whose cytoplasm was harvested for subsequent RT-PCR analysis. Despite our efforts, we found no difference in the 32 electrophysiological features between COX-1 or COX-2 positive and negative cells. This is now clearly stated in the result section (lines 210-212) and a supplementary table of electrophysiological features is now provided. Because it is difficult to determine the morphology of neurons analyzed by single-cell RT-PCR (Devienne et al. 2018), these cells were not processed for biocytin labeling.

Figure 5: (1) Maybe the authors could highlight panels b-f as in vivo experiments to emphasize that these are in-vivo observations while the other experiments (especially panels g, h) are made in slices? 

We thank the reviewer for this suggestion. A black frame is now depicted in Figure 5 to emphasize in vivo experiments.

(2) What is the power of the optogenetic stimulus in this experiment? 

The power of the optogenetic stimulus was 38 mW/mm² in ex vivo experiments (see Line 527). For in vivo experiments, 1 mW pulses of 5 ms were used, the intensity being measured at the fiber end. We now provide the information for in vivo experiments in the Methods lines 639-640.

(3) Experiments were performed with Fluorescein-Dextran at 920-nm excitation which would overlap with EYFP fluorescence from the ChR2-EYFP transgene. Did the authors encounter any issues with crosstalk between the two labels? 

Crosstalk between EYFP and fluorescein fluorescence was indeed an issue. This is why arterioles were monitored at the pial level to avoid fluorescence contamination from the cortical parenchyma. Because of the perivascular space around pial arterioles, it was possible to measure vessel diameter without pollution for the parenchyma (see Author response image 1 below). To clarify this point we added the statement “which are not compromised by the fluorescence from the ChR2-EYFP transgene in the parenchyma (Madisen et al. 2012),” Line 628-629. Note that line scan acquisitions without photoactivation stimulation did not trigger any progressive change in the vessel size or resting fluorescence.

Author response image 1.

Example of a pial arteriole filled with fluorescein dextran (cyan) in an Emx1-EYFP mouse (parenchyma labeled with YFP, in cyan). The red line represents a line scan to record the change in diameter. Due to the perivascular space surrounding the arterioles, the vessel walls are clearly identified and separated from the fluorescent parenchyma.

(4) Could the authors potentially extend the time course in panel e) to show the recovery of the preparation to the baseline? 

Because arterioles were only monitored for a 40-s period during a session of optogenetic stimulation/imaging we cannot extend panel e. Nonetheless, a 5 minutes interstimulus interval was observed to allow the full recovery of the preparation to the baseline. This now clarified line 640. Of note, the arteriole shown in panel d before indomethacin treatment fully recovered to baseline after this treatment.

Also, did the authors observe any 'abnormal' behavior of the vasculature after stimulation, such as large-amplitude oscillations? (5) 

We did not specifically investigate resting state oscillations, such as vasomotion, but the 10-s long baseline recording for each measurement indicates no long lasting, abnormal and de novo behavior with a frequency higher than 0.1-0.2 Hz.

Can the authors show in vivo data from control experiments in EYFP-expressing or WT mice that underwent the same stimulation paradigm (Supplementary Figure 1 shows data from brain slices)?

The reviewer is correct to point out this important control, as optogenetic stimulation can induce a vascular response without channel rhodopsin activation at high power (see our study on the topic, Rungta et al, Nat Com 2017). We therefore tested this potential artefact in a WT mouse using our setup, with different intensities and durations of optogenetic stimulation.

Author response image 2A shows that stimulations of 10 seconds, 10 Hz, 1 mW, 5 ms pulses, i.e. the conditions we used for the experiments in Emx1 mice, did not induce dilation or constriction. Stimulation for 5 seconds with the same number of pulses, but with a higher power (4 mW), longer duration (20 ms pulses) and at a higher frequency elicited a small dilation in 1 of 2 pial arterioles (Author response image 2B). For this reason, we used only shorter (5ms) and less intense (1 mW) optogenetic stimulation to ensure that the observed dilation was solely due to Emx1 activation and not to light-induced artefactual dilation.

Author response image 2.

Optogenetic stimulation in a wild-type mouse. A. No diameter changes upon stimulations of 10 seconds, 10 Hz, 1 mW, 5 ms pulses, i.e. the conditions we used for the experiments in Emx1 mice. B. Stimulation of higher power (4 mW), longer duration (20 ms pulses) and at a higher frequency elicited a small dilation in 1 (grey traces) of 2 pial arterioles.

Figures 6 and 7: It is surprising that blockade of NPY Y1 receptors leads to a complete loss of the constriction response. As shown in Figure 7, the authors suggest that pyramidal neuron-released PGE2 (and glutamate) initiate several cascades acting on smooth muscle directly (PGE2-EP1/EP3), through astrocytes (Glu/COX-1/PGE2 or 20-HETE), or through NPY interneurons (Glu/NPY/Y1 or PGE2/NPY/Y1). This would imply that COX-1/2 and NPY/Y1 pathways act in series (as discussed by the authors). Besides the potential effects on NPY release mentioned in the discussion, could the authors comment if both (NPY and PGE2) pathways need to be co-activated in smooth muscle cells to cause constriction?

We thank the reviewer for raising this surprising complete loss of vasoconstriction by Y1 antagonism, despite the contribution of other vasoconstrictive pathways. We now discuss (lines 402-409) the possibility that activation of the neuronal Y1 receptors in pyramidal cells may also have contributed to the vasoconstriction by promoting glutamate and possibly PGE2 release. The combined activation of vascular and neuronal Y1 receptors may explain the complete blockage of optogenetically induced vasoconstriction by BIBP3226.

Reviewer #2 (Recommendations for the authors):

The complete block of the constriction by BIBP3226 needs to be carefully considered.

We thank the reviewer for stressing this point also raised by Reviewer #1. As mentioned above we now discuss (lines 402-409) the possibility that activation of the neuronal Y1 receptors in pyramidal cells may also have contributed to the vasoconstriction by promoting glutamate and possibly PGE2 release. The combined activation of vascular and neuronal Y1 receptors may explain the complete blockage of optogenetically induced vasoconstriction by BIBP3226.

eLife Assessment

This study presents a useful demonstration that a specific protein fragment may induce the loss of synapses in Alzheimer's disease. The evidence supporting the data is solid but only partially supports the conclusion and would benefit from additional discussion indicated by the literature from reviewer #1. The application of the findings is limited because blocking the formation of the protein fragment has not benefited patients in several clinical trials.

Reviewer #1 (Public review):

Summary of what the authors were trying to achieve:

In this manuscript, the authors investigated the role of β-CTF on synaptic function and memory. They report that β-CTF can trigger the loss of synapses in neurons that were transiently transfected in cultured hippocampal slices and that this synapse loss occurs independently of Aβ. They confirmed previous research (Kim et al, Molecular Psychiatry, 2016) that β-CTF-induced cellular toxicity occurs through a mechanism involving a hexapeptide domain (YENPTY) in β-CTF that induces endosomal dysfunction. Although the current study also explores the role of β-CTF in synaptic and memory function in the brain using mice chronically expressing β-CTF, the studies are inconclusive because potential effects of Aβ generated by γ-secretase cleavage of β-CTF were not considered. Based on their findings, the authors suggest developing therapies to treat Alzheimer's disease by targeting β-CTF. While they acknowledge that clinical trials of potent BACE1 inhibitors - which also target β-CTF - have failed to show clinical improvement, their study lacks in vivo evidence directly linking β-CTF to brain function, which weakens its significance.

Major strengths and weaknesses of the methods and results:

The conclusions of the in vitro experiments using cultured hippocampal slices were well supported by the data, but aspects of the in vivo experiments need additional clarification.<br /> In contrast to the in vitro experiments in which a γ-secretase inhibitor was used to exclude possible effects of Aβ, this possibility was not examined in in vivo experiments assessing synapse loss and function (Fig. 3) and cognitive function (Fig. 4). The absence of plaque formation (Fig. 4C) is not sufficient to exclude the possibility that Aβ is involved. The potential involvement of Aβ is an important consideration given the 4-month duration of protein expression in the in vivo studies. This issue could be addressed using γ-secretase modulators to avoid the off-target effects of inhibitors. Evidence that the detrimental effects in mice are directly caused by β-CTF rather than indirectly via Aβ is critical to support the authors' conclusion.

Appraisal of whether the authors achieved their aims, and whether the results support their conclusion:

See above

Discussion of likely impact of the work on the field, and the utility of the methods and data to the community:

The authors' use of sparse expression to examine the role of β-CTF on spine loss could be a useful general tool for examining synapses in brain tissue.

Any additional context that might help readers interpret or understand the significance of the work:

The discovery of BACE1 stimulated an international effort to develop BACE1 inhibitors to treat Alzheimer's disease. BACE1 inhibitors block the formation of β-CTF which, in turn, prevents the formation of Aβ and other fragments. Unfortunately, BACE1 inhibitors not only did not improve cognition in patients with Alzheimer's disease, they appeared to worsen it, suggesting that β-CTF could facilitate learning and memory. Therefore, it seems unlikely that the disruptive effects of β-CTF on endosomes plays a significant role in the human disease.

Comments on revisions:

The authors may be interested in the study by Ma et al., PNAS 2007 titled "Involvement of β-site APP cleaving enzyme 1 (BACE1) in amyloid precursor protein-mediated enhancement of memory and activity-dependent synaptic plasticity," which provides significant insights into the physiological role of BACE1 in synaptic function. The researchers demonstrated that BACE1-mediated cleavage of amyloid precursor protein (APP) is essential for enhancing learning, memory, and synaptic plasticity in vivo. They observed that overexpression of APP in transgenic mice led to improved spatial memory retention and potentiation of synaptic plasticity, effects that were abolished when one or both copies of the BACE1 gene were eliminated. This suggests that BACE1's cleavage of APP facilitates activity-dependent synaptic modifications, potentially through the production of APP intracellular domain (AICD) via β-CTF, rather than amyloid-β (Aβ) or soluble APPα (sAPPα). These findings highlight a physiological mechanism where BACE1-mediated APP processing leading to β-CTF supports cognitive functions, potentially explaining the detrimental effects of BACE1 inhibitors on cognitive function in clinical trials.

Reviewer #3 (Public review):

Summary:

Most previous studies have focused on the contributions of Abeta and amyloid plaques in the neuronal degeneration associated with Alzheimer's disease, especially in the context of impaired synaptic transmission and plasticity which underlies the impaired cognitive functions, a hallmark in AD. But processes independent of Abeta and plaques are much less explored, and to some extent, the contributions of these processes are less well understood. Luo et all addressed this important question with an array of approaches, and their findings generally support the contribution of beta-CTF-dependent but non-Abeta dependent process to the impaired synaptic properties in the neurons. Interestingly, the above process appears to operate in a cell-autonomous manner. This cell-autonomous effect of beta-CTF as reported here may facilitate our understanding of some potential important cellular processes related to neurodegeneration. Although these findings are valuable, it is key to understand the probability of this process occurring in a more natural condition, such as when this process occurring in many neurons at the same time. This will put the authors' findings into a context for a better understanding of their contribution to either physiological or pathological processes, such as Alzheimer's. The experiments and results using cell system are quite solid, but the in vivo results are incomplete and hence less convincing (see below). The mechanistic analysis is interesting but primitive, and does not add much more weight to the significance. Hence, further efforts from the authors are required to clarify, and solidify their results, in order to provide a complete picture and support for the authors' conclusions.

Strengths:

(1) The authors have addressed an interesting and potentially important question<br /> (2) The analysis using the cell system are solid and provides strong support for the authors' major conclusions. This analysis has used various technical approaches to support the authors' conclusions from different aspects and most of these results are consistent with each other.

Weaknesses:

(1) The relevance of the authors' major findings to the pathology, especially the Abeta-dependent processes is less clear, and hence the importance of these findings may be limited.<br /> (2) In vivo analysis is incomplete, with certain caveats in the experimental procedures and some of the results need to be further explored to confirm the findings.<br /> (3) The mechanistic analysis is rather primitive and does not add further significance.

Comments on revisions:

The authors have satisfactorily addressed my main questions.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary of what the authors were trying to achieve:

In this manuscript, the authors investigated the role of β-CTF on synaptic function and memory. They report that β-CTF can trigger the loss of synapses in neurons that were transiently transfected in cultured hippocampal slices and that this synapse loss occurs independently of Aβ. They confirmed previous research (Kim et al, Molecular Psychiatry, 2016) that β-CTF-induced cellular toxicity occurs through a mechanism involving a hexapeptide domain (YENPTY) in β-CTF that induces endosomal dysfunction. Although the current study also explores the role of β-CTF in synaptic and memory function in the brain using mice chronically expressing β-CTF, the studies are inconclusive because potential effects of Aβ generated by γ-secretase cleavage of β-CTF were not considered. Based on their findings, the authors suggest developing therapies to treat Alzheimer's disease by targeting β-CTF, but did not address the lack of clinical improvement in trials of several different BACE1 inhibitors, which target β-CTF by preventing its formation.

We would like to thank the reviewer for his/her suggestions. We have addressed the specific comments in following sections.

Major strengths and weaknesses of the methods and results:

The conclusions of the in vitro experiments using cultured hippocampal slices were well supported by the data, but aspects of the in vivo experiments and proteomic studies need additional clarification.

(1) In contrast to the in vitro experiments in which a γ-secretase inhibitor was used to exclude possible effects of Aβ, this possibility was not examined in in-vivo experiments assessing synapse loss and function (Figure 3) and cognitive function (Figure 4). The absence of plaque formation (Figure 4B) is not sufficient to exclude the possibility that Aβ is involved. The potential involvement of Aβ is an important consideration given the 4-month duration of protein expression in the in vivo studies.

We appreciate the reviewer for raising this question. While our current data did not exclude the potential involvement of Aβ-induced toxicity in the synaptic and cognitive dysfunction observed in mice overexpressing β-CTF, addressing this directly remains challenging. Treatment with γ-secretase inhibitors could potentially shed light on this issue. However, treatments with γ-secretase inhibitors are known to lead to brain dysfunction by itself likely due to its blockade of the γ-cleavage of other essential molecules, such as Notch[1, 2]. Therefore, this approach is unlikely to provide a clear answer, which prevents us from pursuing it further experimentally in vivo. We hope the reviewer understands this limitation. We have included additional discussion (page 14 of the revised manuscript) to highlight this question.

(2) The possibility that the results of the proteomic studies conducted in primary cultured hippocampal neurons depend in part on Aβ was also not taken into consideration.

We thank the reviewer for raising this question. In the revised manuscript, we examined the protein levels of synaptic proteins after treatment with γ-secretase inhibitors and found that the levels of certain synaptic proteins were further reduced in neurons expressing β-CTF (Supplementary figure 5A-B). These results do not support Aβ as a major contributor of the proteomic changes induced by β-CTF.

Likely impact of the work on the field, and the utility of the methods and data to the community:

The authors' use of sparse expression to examine the role of β-CTF on spine loss could be a useful general tool for examining synapses in brain tissue.

We thank the reviewer for these comments.

Additional context that might help readers interpret or understand the significance of the work:

The discovery of BACE1 stimulated an international effort to develop BACE1 inhibitors to treat Alzheimer's disease. BACE1 inhibitors block the formation of β-CTF which, in turn, prevents the formation of Aβ and other fragments. Unfortunately, BACE1 inhibitors not only did not improve cognition in patients with Alzheimer's disease, they appeared to worsen it, suggesting that producing β-CTF actually facilitates learning and memory. Therefore, it seems unlikely that the disruptive effects of β-CTF on endosomes plays a significant role in human disease. Insights from the authors that shed further light on this issue would be welcome.

Response: We would like to express our gratitude to the reviewer for raising this question. It remains puzzling why BACE1 inhibition has failed to yield benefits in AD patients, while amyloid clearance via Aβ antibodies are able to slow down disease progression. One possible explanation is that pharmacological inhibition of BACE1 may not be as effective as its genetic removal. Indeed, genetic depletion of BACE1 leads to the clearance of existing amyloid plaques[3], whereas its pharmacological inhibition prevents the formation of new plaques but does not deplete the existing ones[4]. We think the negative results of BACE1 inhibitors in clinical trials may not be sufficient to rule out the potential contribution of β-CTF to AD pathogenesis. Given that cognitive function continues to deteriorate rapidly in plaque-free patients after 1.5 years of treatment with Aβ antibodies in phase three clinical studies[5], it is important to consider the potential role of other Aβ-related fragments in AD pathogenesis, such as β-CTF. We included further discussion in the revised manuscript (page 15 of the revised manuscript) to discusss this question.

Reviewer #2 (Public Review):

Summary:

In this study, the authors investigate the potential role of other cleavage products of amyloid precursor protein (APP) in neurodegeneration. They combine in vitro and in vivo experiments, revealing that β-CTF, a product cleaved by BACE1, promotes synaptic loss independently of Aβ. Furthermore, they suggest that β-CTF may interact with Rab5, leading to endosomal dysfunction and contributing to the loss of synaptic proteins.

We would like to thank the reviewer for his/her suggestions. We have addressed the specific comments in following sections.

Weaknesses:

Most experiments were conducted in vitro using overexpressed β-CTF. Additionally, the study does not elucidate the mechanisms by which β-CTF disrupts endosomal function and induces synaptic degeneration.

We would like to thank the reviewer for this comment. While a significant portion of our experiments were conducted in vitro, the main findings were also confirmed in vivo (Figure 3 and 4). Repeating all the experiments in vivo would be challenging and may not be possible because of technical difficulties. Regarding the use of overexpressed β-CTF, we acknowledge that this represents a common limitation in neurodegenerative disease studies. These diseases progress slowly over decades in patients. To model this progression in cell or mouse models within a time frame feasible for research, overexpression of certain proteins is often inevitable. Since β-CTF levels are elevated in AD patients[6], its overexpression is not a irrelevant approach to investigate its potential effects.

We did not further investigate the mechanisms by which β-CTF disrupted endosomal function because our preliminary results align with previous findings that could explain its mechanism. Kim et al. demonstrated that β-CTF recruits APPL1 (a Rab5 effector) via the YENPTY motif to Rab5 endosomes, where it stabilizes active GTP-Rab5, leading to pathologically accelerated endocytosis, endosome swelling and selectively impaired transport of Rab5 endosomes[6]. However, this paper did not show whether this Rab5 overactivation-induced endosomal dysfunction leads to any damages in synapses. In our study, we observed that co-expression of Rab5_S34N with β-CTF effectively mitigated β-CTF-induced spine loss in hippocampal slice cultures (Figures 6L-M), indicating that Rab5 overactivation-induced endosomal dysfunction contributed to β-CTF-induced spine loss. We included further discussion in the revised manuscript to clarify this (page 15 of the revised manuscript).

Reviewer #3 (Public Review):

Summary:

Most previous studies have focused on the contributions of Abeta and amyloid plaques in the neuronal degeneration associated with Alzheimer's disease, especially in the context of impaired synaptic transmission and plasticity which underlies the impaired cognitive functions, a hallmark in AD. But processes independent of Abeta and plaques are much less explored, and to some extent, the contributions of these processes are less well understood. Luo et all addressed this important question with an array of approaches, and their findings generally support the contribution of beta-CTF-dependent but non-Abeta-dependent process to the impaired synaptic properties in the neurons. Interestingly, the above process appears to operate in a cell-autonomous manner. This cell-autonomous effect of beta-CTF as reported here may facilitate our understanding of some potentially important cellular processes related to neurodegeneration. Although these findings are valuable, it is key to understand the probability of this process occurring in a more natural condition, such as when this process occurs in many neurons at the same time. This will put the authors' findings into a context for a better understanding of their contribution to either physiological or pathological processes, such as Alzheimer's. The experiments and results using the cell system are quite solid, but the in vivo results are incomplete and hence less convincing (see below). The mechanistic analysis is interesting but primitive and does not add much more weight to the significance. Hence, further efforts from the authors are required to clarify and solidify their results, in order to provide a complete picture and support for the authors' conclusions.

We would like to thank the reviewer for the suggestions. We have addressed the specific comments in following sections.

Strengths:

(1) The authors have addressed an interesting and potentially important question

(2) The analysis using the cell system is solid and provides strong support for the authors' major conclusions. This analysis has used various technical approaches to support the authors' conclusions from different aspects and most of these results are consistent with each other.

We would like to thank the reviewer for these comments.

Weaknesses:

(1) The relevance of the authors' major findings to the pathology, especially the Abeta-dependent processes is less clear, and hence the importance of these findings may be limited.

We would like to thank the reviewer for this question. Phase 3 clinical trial data from Aβ antibodies show that cognitive function continues to decline rapidly, even in plaque-free patients, after 1.5 years of treatment[5]. This suggests that plaque-independent mechanisms may drive AD progression. Therefore, it is crucial to consider the potential contributions of other Aβ species or related fragments, such as alternative forms of Aβ and β-CTF. While it is early to predict how much β-CTF contributes to AD progression, it is notable that β-CTF induced synaptic deficits in mice, which recapitulates a key pathological feature of AD. Ultimately, the contribution of β-CTF in AD pathogenesis can only be tested through clinical studies in the future.

(2) In vivo analysis is incomplete, with certain caveats in the experimental procedures and some of the results need to be further explored to confirm the findings.

We would like to thank the reviewer for this suggestion. We have corrected these caveats in the revised manuscript.

(3) The mechanistic analysis is rather primitive and does not add further significance.

We would like to thank the reviewer for this comment. We did not delve further into the underlying mechanisms because our analysis indicates that Rab5 overactivation-induced endosomal dysfunction underlies β-CTF-induced synaptic dysfunction, which is consistent with another study and has been addressed in our study[6]. We hope the reviewer could understand that our focus in this paper is on how β-CTF triggers synaptic deficits, which is why we did not investigate the mechanisms of β-CTF-induced endosomal dysfunction further.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses:

(1) In Figures 4H, 4J, 4K and Supplemental Figures 3C, 3E, and 3G, it was unclear whether a repeated measures 2-way ANOVA, rather than a 2-way ANOVA, followed by appropriate post-hoc analyses was used to strengthen the conclusion that there were significant effects in the behavioral tests.

We appreciate the reviewer for raising this point and apologize for the lack of clear description in the manuscript. In those figures mentioned above, we use a repeated measures 2-way ANOVA to analyze the data by Graphpad Prism. In Figure 4H, fear conditioning tests were conducted. The same cohort of mice were used in the baseline, contextual and cued tests. Firstly, baseline freezing was tested; then these mice underwent tone and foot shock training, followed by contextual test and cued test. So, a repeated measures 2-way ANOVA is more appropriate for the experiment.

In water T maze tests (Figure 4J and K), the same cohort of mice were trained and tested each day. So, it’s also appropriate to use a repeated measures 2-way ANOVA.

In Supplementary figure 3C, 3E and 3G, OFT was conducted. In this experiment, the locomotion of the same cohort of mice were recorded. Also, it’s appropriate to use a repeated measures 2-way ANOVA.

Clearer description for these experiments has been provided in the revised manuscript.

(2) Including gender analyses would be helpful.

The mice we used in this study were all males.

Minor corrections to text and figures:

(1) Quantitative analyses in Figures 5A-C, 5H, 6G, 6H, and Supplementary Figures 4 and 5C would be helpful.

We have provided quantitative analysis of these results (Figure 5D, 5J, 6K, Supplementary figure 4D, 5F) mentioned above in the revised manuscript.

(2) Percent correct (%) in Figures 4J and 4K should be labeled as 0, 50, and 100 instead of 0.0, 0.5, and 1.0.

We would like to thank the reviewer for pointing out this. We have made corrections in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

In the study conducted by Luo et al, it was observed that the fragment of amyloid precursor protein (APP) cleaved by beta-site amyloid precursor protein cleaving enzyme 1 (BACE1), known as β-CTF, plays a crucial role in synaptic damage. The study found increasing expression of β-CTF in neurons could induce synapse loss both in vitro and in vivo, independent of Aβ. Mechanistically, they explored how β-CTF could interfere with the endosome system by interacting with RAB5. While this study is intriguing, there are several points that warrant further investigation:

(1) The study involved overexpressing β-CTF in neurons. It would be valuable to know if the levels of β-CTF are similarly increased in Alzheimer's disease (AD) patients or AD mouse models.

We would like to thank the reviewer for the suggestion. It’s reported β-CTF levels were significantly elevated in the AD cerebral cortex[6]. Most AD mouse models are human APP transgenic mouse models with elevated β-CTF levels[7].

(2) The study noted that β-CTF in neurons is a membranal fragment, but the overexpressed β-CTF was not located in the membrane. It is important to ascertain whether the membranal β-CTF and cytoplasmic β-CTF lead to synapse loss in a similar manner.

We apologize for not clearly explaining the localization of β-CTF in the original manuscript. β-CTF is produced from APP through β-cleavage, a process that occurs in organelles such as endo-lysosomes[8]. The overexpressed β-CTF is also primarily localized in the endo-lysosomal systems (Figure 5C and Supplementary figure 4C), similar to those generated by APP cleavage.

(3) The study found a significant decrease in GluA1, a subunit of AMPA receptors, due to β-CTF. It would be beneficial to investigate whether there are systematic alterations in NMDA receptors, including GluN2A and GluN2B.

We would like to express our gratitude to the reviewer for bringing up this question. The protein levels of GluN2A and GluN2B are also reduced in neurons expressing β-CTF (Figure 6E-F)

(4) The study showed a significant decrease in the frequency of miniature excitatory postsynaptic currents (mEPSC), indicating disrupted presynaptic vesicle neurotransmitter release. It would be pertinent to test whether the expression level of the presynaptic SNARE complex, which is required for vesicle release, is altered by β-CTF.

We would like to express our gratitude to the reviewer for bringing up this question. The protein level of the presynaptic SNARE complex, such as VAMP2, is also reduced in neurons expressing β-CTF (Figure 6E, G).

(5) Since AMPA receptors are glutamate receptors, it is important to determine whether the ability of glutamate release is altered by β-CTF. In vivo studies using a glutamate sensor should be conducted to examine glutamate release.

We would like to express our gratitude to the reviewer for this suggestion. It will be interesting to use glutamate sensors to assess the ability of glutamate release in the future.

(6) The quality of immunostaining associated with Figures 4B and 4C was noted to be suboptimal.

We apologize for the suboptimal quality of these images. The immunostaining in Figures 4B and 4C were captured using the stitching function of a confocal microscope to display larger areas, including the entire hemisphere and hippocampus. We have reprocessed the images to obtain higher-quality versions.

(7) It would be insightful to investigate whether treatment with a BACE1 inhibitor in the study could reverse synaptic deficits mediated by β-CTF.

We would like to thank the reviewer for this sggestion. In Figure 1I-M, we constructed an APP mutant (APP_MV), which cannot be cleaved by BACE1 to produce β-CTF and Aβ but has no impact on β’-cleavage. When co-expressed with BACE1, APP_MV failed to induce spine loss, supporting the effect of β-CTF. We think these results domonstrate that β-CTF underlies the synaptic deficits. It would be interesting to test the effects of BACE1 inhibition in the future.

(8) Considering the potential implications for therapeutics, it is worth exploring whether extremely low levels of β-CTF have beneficial effects in regulating synaptic function or promoting synaptogenesis at a physiological level.

We would like to thank the reviewer for raising this question. We found that when the plasmid amount was reduced to 1/8 of the original dose, β-CTF no longer induced a decrease in dendritic spine density (Supplementary figure 2E-F). It’s reported APP-Swedish mutation in familial AD increased synapse numbers and synaptic transmission, whereas inhibition of BACE1 lowered synapse numbers, suppressed synaptic transmission in wild type neurons, suggesting that at physiological level, β-CTF might be synaptogenic[9].

(9) The molecular mechanism through which β-CTF interferes with Rab5 function should be elucidated.

We would like to thank the reviewer for raising this question. Kim et al have elucidated the mechanism through which β-CTF interferes with Rab5 function. β-CTF recruited APPL1 (a Rab5 effector) via YENPTY motif to Rab5 endosomes, where it stabilizes active GTP-Rab5, leading to pathologically accelerated endocytosis, endosome swelling and selectively impaired transport of Rab5 endosomes[6]. We have included additional discussion for this question in the revised manuscript (page 15 of the revised manuscript).

(10) The study could compare the role of β-CTF and Aβ in neurodegeneration in AD mouse models.

We would like to thank the reviewer for raising this point. While it is easier to dissect the role of Aβ and β-CTF in vitro, some of the critical tools are not applicabe in vivo, such as γ-secretase inhibitors, which lead to severe side effects because of their inhibition on other γ substrates[1, 2]. Therefore it will be difficult to deomonstrate their different roles in vivo. There are studies showing that β-CTF accumulation precedes Aβ deposition in model mice and mediates Aβ independent intracellular pathologies[10, 11], consistent with our results.

(11) Based on the findings, it would be valuable to discuss possible explanations for the failure of most BACE1 inhibitors in recent clinical trials for humans.

Response: We would like to express our gratitude to the reviewer for raising this recommendation. It is a big puzzle why BACE1 inhibition failed to provide beneficial effects in AD patients whereas clearance of amyloid by Aβ antibodies could slow down the AD progress. One potential answer is that pharmacological inhibition of BACE1 might be not as effective as its genetic removal. Indeed, genetic depletion of BACE1 leads to clearance of existing amyloid plaques[3], whereas pharmacological inhibition of BACE1 could not stop growth of existing plaques, although it prevents formation of new plaques[4]. The negative result of BACE1 inhibitors might not be sufficient to exclude the possibility that β-CTF could also contribute to the AD pathogenesis. We have included additional discussion for this question in the revised manuscript (page 15 of the revised manuscript).

Reviewer #3 (Recommendations For The Authors):

Major:

(1) The cell experiments were performed at DIV 9, do the authors know whether at this age, the neurons are still developing and spine density has not reached a pleated yet? If so, the observed effect may reflect the impact on development and/or maturation, rather than on the mature neurons. The authors should be more specific about this issue.

We would like to thank the reviewer for pointing out this question. These slice cultures were made from 1-week-old rats. DIV 9 is about two weeks old. These neurons are still developing and spine density has not reached a plateau yet[12]. In addition, we also investigated the effects of β-CTF on the synapses of mature neurons in two-month-old mice (Figure 3). So we think the observed effect reflects the impact on both immature and mature neurons.

(2) mEPSCs shown in Figure 3D were of small amplitudes, perhaps also indicating that these synapses are not yet mature.

In Figure 3D, the mEPSC results were obtained from pyramidal neurons in the CA1 region of two-month-old mice. At the age of two months, neurotransmitter levels and synaptic density have reached adult levels[13].

(3) There was no data on the spine density or mEPSCs in the mice OE b-CTF, hence it is unclear whether a primary impact of this manipulation (b-CTF effect) on the synaptic transmission still occurs in vivo.

In Figure 3, we examined the density of dendritic spines and mEPSCs from CA1 pyramidal neurons infected with lentivirus expressing β-CTF in mice and showed that those neurons expressing additional amount of β-CTF exhibited lower spine density and less mEPSCs, supporting that β-CTF also damaged synaptic transmission in vivo.

(4) OE of b-CTF should lead to the production of Abeta, although this may not lead to the formation of significant plaques. How do the authors know whether their findings on behavioral and cognitive impairments were not largely mediated by Abeta, which has been widely reported by previous studies?

We would like to thank the reviewer for pointing out this question. Indeed, our in vivo data could not exclude the potential involvement of Aβ in the pathology, despite the absence of amyloid plaque formation. It will be difficult to demonstrate this question in vivo because of the severe side effects from γ inhibition.

(5) Figure 4H, the freezing level in the cued fear conditioning was very high, likely saturated; this may mask a potential reduction in the b-CTF OE mice (there is a hint for that in the results). The authors should repeat the experiments using less strong footshock strength (hence resulting in less freezing, <70%).

We would like to express our gratitude to the reviewer for bringing up this question. The contextual fear conditioning test assesses hippocampal function, while the cued fear conditioning test assesses amygdala function. We hope the reviewer understands that our primary goal is to assess hippocampus-related functions in this experiment and we did see a significant difference between GFP and β-CTF groups. Therefore, we think the intensity of footshock we used was suitable to serve the primary purpose of this experiment.

(6) Why was the deficit in the Morris water maze in the b-CTF OE mice only significant in the training phase?

We would like to thank the reviewer for rasing this question and apologize for not describing the test clearly. This is a water T maze test, not Morris water maze test.

To make the behavioral paradigm of the water T maze test easier to understand, we have provided a more detailed description of the methods in the new version of the manuscript.

The acquisition phase of the Water T Maze (WTM) evaluates spatial learning and memory, where mice use spatial cues in the environment to navigate to a hidden platform and escape from water, while the reversal learning measures cognitive flexibility in which mice must learn a new location of the hidden platform[14]. In reversal learning task (Figure 4J-K), the learning curves of the two groups of mice did not show any significant differences, indicating that the expression of β-CTF only damages spatial learning and memory but not cognitive flexibility. This is consistent with a previous report using APP/PS1 mice[15].

(7) Will the altered Rab5 in the b-CTF OE condition also affect the level of other proteins?

We would like to express our gratitude to the reviewer for raising this interesting question.  Expression of Rab5_S34N in β-CTF-expressing neurons did not alter the levels of synapse-related proteins that were reduced in these neurons (Supplementary figure 5G-H), suggesting Rab5 overactivation did not contribute to these protein expression changes induced by β-CTF.

(8) How do the authors reconcile their findings with the well-established findings that Abeta affects synaptic transmission and spine density? Do they think these two processes may occur simultaneously in the neurons, or, one process may dominate in the other?

APP, Aβ, and presenilins have been extensively studied in mouse models, providing convincing evidence that high Aβ concentrations are toxic to synapses[16]. Moreover, addition of Aβ to murine cultured neurons or brain slices is toxic to synapses[17]. However, Aβ-induced synaptotoxicity was not observed in our study. A major difference between our study and others is that our study used a isolated expression system that apply Aβ only to individual neurons surrounded by neurons without excessive amount of Aβ, whereas the rest studies generally apply Aβ to all the neurons. Therefore, we predict that Aβ does not lead to synaptic deficits from individual neurons in cell autonomous manners, whereas β-CTF does. Aβ and β-CTF represent two parallel pathways of action. Additional discussion for this question has been included in the revised manuscript (page 14 of the revised manuscript).

Minor:

Fig 2F-G, "prevent" rather than "reverse"?

We would like to thank the reviewer for pointing this out. We have made corrections in the revised manuscript.

Reference:

(1) GüNER G, LICHTENTHALER S F. The substrate repertoire of γ-secretase/presenilin [J]. Seminars in cell & developmental biology, 2020, 105: 27-42.

(2) DOODY R S, RAMAN R, FARLOW M, et al. A phase 3 trial of semagacestat for treatment of Alzheimer's disease [J]. The New England journal of medicine, 2013, 369(4): 341-50.

(3) HU X, DAS B, HOU H, et al. BACE1 deletion in the adult mouse reverses preformed amyloid deposition and improves cognitive functions [J]. The Journal of experimental medicine, 2018, 215(3): 927-40.

(4) PETERS F, SALIHOGLU H, RODRIGUES E, et al. BACE1 inhibition more effectively suppresses initiation than progression of β-amyloid pathology [J]. Acta neuropathologica, 2018, 135(5): 695-710.

(5) SIMS J R, ZIMMER J A, EVANS C D, et al. Donanemab in Early Symptomatic Alzheimer Disease: The TRAILBLAZER-ALZ 2 Randomized Clinical Trial [J]. Jama, 2023, 330(6): 512-27.

(6) KIM S, SATO Y, MOHAN P S, et al. Evidence that the rab5 effector APPL1 mediates APP-βCTF-induced dysfunction of endosomes in Down syndrome and Alzheimer's disease [J]. Molecular psychiatry, 2016, 21(5): 707-16.

(7) MONDRAGóN-RODRíGUEZ S, GU N, MANSEAU F, et al. Alzheimer's Transgenic Model Is Characterized by Very Early Brain Network Alterations and β-CTF Fragment Accumulation: Reversal by β-Secretase Inhibition [J]. Frontiers in cellular neuroscience, 2018, 12: 121.

(8) ZHANG X, SONG W. The role of APP and BACE1 trafficking in APP processing and amyloid-β generation [J]. Alzheimer's research & therapy, 2013, 5(5): 46.

(9) ZHOU B, LU J G, SIDDU A, et al. Synaptogenic effect of APP-Swedish mutation in familial Alzheimer's disease [J]. Science translational medicine, 2022, 14(667): eabn9380.

(10) LAURITZEN I, PARDOSSI-PIQUARD R, BAUER C, et al. The β-secretase-derived C-terminal fragment of βAPP, C99, but not Aβ, is a key contributor to early intraneuronal lesions in triple-transgenic mouse hippocampus [J]. The Journal of neuroscience : the official journal of the Society for Neuroscience, 2012, 32(46): 16243-1655a.

(11) KAUR G, PAWLIK M, GANDY S E, et al. Lysosomal dysfunction in the brain of a mouse model with intraneuronal accumulation of carboxyl terminal fragments of the amyloid precursor protein [J]. Molecular psychiatry, 2017, 22(7): 981-9.

(12) HARRIS K M, JENSEN F E, TSAO B. Three-dimensional structure of dendritic spines and synapses in rat hippocampus (CA1) at postnatal day 15 and adult ages: implications for the maturation of synaptic physiology and long-term potentiation [J]. The Journal of neuroscience : the official journal of the Society for Neuroscience, 1992, 12(7): 2685-705.

(13) SEMPLE B D, BLOMGREN K, GIMLIN K, et al. Brain development in rodents and humans: Identifying benchmarks of maturation and vulnerability to injury across species [J]. Progress in neurobiology, 2013, 106-107: 1-16.

(14) GUARIGLIA S R, CHADMAN K K. Water T-maze: a useful assay for determination of repetitive behaviors in mice [J]. Journal of neuroscience methods, 2013, 220(1): 24-9.

(15) ZOU C, MIFFLIN L, HU Z, et al. Reduction of mNAT1/hNAT2 Contributes to Cerebral Endothelial Necroptosis and Aβ Accumulation in Alzheimer's Disease [J]. Cell reports, 2020, 33(10): 108447.

(16) CHAPMAN P F, WHITE G L, JONES M W, et al. Impaired synaptic plasticity and learning in aged amyloid precursor protein transgenic mice [J]. Nature neuroscience, 1999, 2(3): 271-6.

(17) WANG Z, JACKSON R J, HONG W, et al. Human Brain-Derived Aβ Oligomers Bind to Synapses and Disrupt Synaptic Activity in a Manner That Requires APP [J]. The Journal of neuroscience : the official journal of the Society for Neuroscience, 2017, 37(49): 11947-66.

eLife Assessment

NAD deficiency perturbs embryonic development resulting in multiple congenital malformations, collectively termed Congenital NAD Deficiency Disorder (CNDD). The authors report fundamental findings demonstrating that extra-embryonic visceral yolk sac endoderm is critical for NAD de novo synthesis during early organogenesis and perturbations of this pathway may underlie CNDD. The authors combine gene expression with metabolic assays to provide solid evidence of an essential role of the extra-embryonic visceral yolk sac in both mouse and human embryos.

Reviewer #1 (Public review):

Summary:

This study investigated the mechanism underlying Congenital NAD Deficiency Disorder (CNDD) using a mouse model with loss of function of the HAAO enzyme which mediates a key step in the NAD de novo synthesis pathway. This study builds on the observation that the kynurenine pathway is required in the conceptus, as HAAO null embryos are sensitive to maternal deficiency of NAD precursors (vitamin B3) and tryptophan, and narrows the window of sensitivity to a 3 day period.

An important finding is that de novo NAD synthesis occurs in an extra-embryonic tissue, the visceral yolk sac, before the liver develops in the embryo. It is suggested that lack of this yolk sac activity leads to impaired NAD supply in the embryo leading to structural abnormalities found later in development.

Strengths:

Previous studies show a requirement for HAOO activity for normal development of the embryos develop abnormalities under conditions of maternal vitamin B3 deficiency, indicating a requirement for NAD synthesis in the conceptus. Analysis of scRNA-seq datasets combined with metabolite analysis of yolk sac tissue shows that the NAD synthesis pathway is expressed and functional in the yolk sac from E10.5 onwards (prior to liver development).

HAOO enzyme assay enabled quantification of enzyme activity in relevant tissues including liver (from E12.5), embryo, placenta and yolk sac (from E11.5).<br /> Comprehensive metabolite analysis of the NAD synthesis pathway supports the predicted effects of HAOO knockout and provides analysis of yolk sac, placenta and embryo at a series of stages.

The dietary study (with lower vitamin B3 in maternal diet from E7.5-10.5) is an incremental addition to previous studies which imposed similar restrictions from E7.5-12.5. Nevertheless, this emphasises the importance of the synthesis pathway on the conceptus at stages before liver activity is prominent.

Weaknesses:

The current dietary study narrows the period when deficiency can cause malformations (analysed at E18.5), and altered metabolite profiles (eg, increased 3HAA, lower NAD) are detected in yolk sac and embryo at E10.5.

More importantly, there is still a question of whether in addition to the yolks sac, there is HAAO activity within the embryo itself has been assayed as early as E11.5, with minimal activity prior to E12.5 (when it is assayed in liver). These findings support the hypothesis that within the conceptus (embryo, chorioallantoic placenta and visceral yok sac) the embryo is unlikely to be the site of NAD synthesis prior to liver development.

Evidence for lack of function of the NAD synthesis pathway in the embryos itself from kynurenine at E7.5-10.5 comes from reanalysis of scRNA-seq. This suggests low or absent expression of HAAO in the embryo prior to E10.5 (corresponding to the period when the authors have demonstrated that de novo NAD synthesis in the conceptus is needed). The caveat to this conclusion is that additional analysis of RNA and/or protein expression in the embryos at E7.5-10.5 has not been performed to validate the scRNA-seq data.

Reviewer #2 (Public review):

Summary:

Disruption of the nicotinamide adenine dinucleotide (NAD) de novo Synthesis Pathway, by which L-tryptophan is converted to NAD results in multi-organ malformations which collectively has been termed Congenital NAD Deficiency Disorder (CNDD).

While NAD de novo synthesis is primarily active in the liver postnatally, the site of activity prior to and during organogenesis is unknown. However, mouse embryos are susceptible to CNDD between E7.5-E12.5, before the embryo has developed a functional liver. Therefore, NAD de novo synthesis is likely active in another cell or tissue during this time window of susceptibility.

The body of work presented in this paper continues the corresponding author's labs investigation of the cause and effects of NAD Deficiency and the primary goal was to determine the cell or tissue responsible for NAD de novo synthesis during early embryogenesis.

The authors conclude that visceral yolk sac endoderm is the source of NAD de novo synthesis, which is essential for mouse embryonic development, and furthermore that the dynamics of NAD synthesis are conserved in human equivalent cells and tissues, the perturbation of which results in CNDD.

Strengths:

Overall, the primary findings regarding the source of NAD synthesis, the temporal requirement and conservation between rodent and human species is quite novel and important for our understanding of NAD synthesis and function and role in CNDD.

The authors used UHPLC-MS/MS to quantify NAD+ and NAD-related metabolites and showed convincingly that the NAD salvage pathway can compensate for the loss of NAD synthesis in Haao-/- embryos, then determined that Haao activity was present in the yolk sac prior to hepatic development identifying this organ as the site of de novo NAD synthesis. Dietary modulation between E7.5-10.5 was sufficient to induce CNDD phenotypes, narrowing the window of susceptibility, and then re-analysis of RNA-seq datasets suggested the endoderm was the cell source of NAD synthesis.

Weaknesses:

Page 4 and Table S4. The descriptors for malformations of organs such as the kidney and vertebrae are quite vague and uninformative. More specific details are required to convey the type and range of anomalies observed as a consequence of NAD deficiency.

Can the authors define whether the role for the NAD pathway in a couple of tissue or organ systems is the same. By this I mean is the molecular or cellular effect of NAD deficiency the same in the vertebrae and organs such as the kidney. What unifies the effects on these specific tissues and organs and are all tissues and organs affected. If some are not, can the authors explain why they escape the need for the NAD pathway.

Page 5 and Figure 6C. The expectation and conclusion for whether specific genes are expressed in particular cell types in scRNA-seq datasets depends on number of cells sequenced, the technology (methodology) used, the depth of sequencing and also the resolution of the analysis. It is therefore essential to perform secondary validation of the analysis of scRNA-seq data. At a minimum, the authors should perform in situ hybridization or immunostaining for Tdo2, Afmid, Kmo, Kynu, Haao, Qprt and Nadsyn1 or some combination thereof at multiple time points during early mouse embryogenesis to truly understand the spatiotemporal dynamics of expression and NAD synthesis.

Absolute functional proof of the yolk sac endoderm as being essential and required for NAD synthesis in the context of CNDD might require conditional deletion of Haao in the yolk sac versus embryo using appropriate Cre driver lines or in the absence of a conditional allele, could be performed by tetraploid embryo-ES cell complementation approaches. But temporal dietary intervention can also approximate the same thing by perturbing NAD synthesis then the yolk sac is the primary source versus when the liver becomes the primary source in the embryo.

In further revisions, the authors have added data to Supp Table 4 and Supplemental Figures 1 and 2

Although the authors did not perform in situ hybridization for some of the genes requested to define the critical cell type of expression, available scRNA-sequencing suggests the yolk sac endoderm are the only likely source of NAD synthesis prior to its synthesis in the liver. Absolute functional proof of the yolk sac endoderm as being essential and required for NAD synthesis in the context of CNDD still requires validation but nonetheless it seems likely given the absence of a functional liver in embryos prior to E12.5. The authors provided some additional data pertaining to the type of kidney and vertebral anomalies observed which makes this data more complete.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

A number of modifications/additions have been made to the text which help to clarify the background and details of the study and I feel have improved the study.

NAD deficiency induced using the dietary/Haao null model showed a window of susceptibility at E7.5-10.5. Further, HAAO enymze activity data has been added at E11.5 and the minimal HAAO activity in the embryo act E11.5 supports the hypothesis that the NAD synthesis pathway from kynurenine is not functional until the liver starts to develop.

The caveat to this is that absence of expression/activity in embryonic cells at E7.5-10/5 relies on previous scRNA-seq data. Both reviewers commented that analysis of RNA and/or protein expression at these stages (E7.5-10.5) would be necessary to rule this out, and would strongly support the conclusions regarding the necessity for yolk sac activity.

There are a number of antibodies for HAAO, KNYU etc so it is surprising if none of these are specific for the mouse proteins, while an alternative approach in situ hydridisation would also be possible.

We have tested 2 anti-HAAO antibodies, 2 anti-KYNU antibodies and 1 anti-QPRT antibody on adult liver and various embryonic tissues.

Given that all tested antibodies only detected a specific band in tissues with very high expression and abundant target protein levels (adult liver), they were determined to be unsuitable to conclusively prove that these proteins of the NAD _de novo_synthesis pathway are absent in embryos prior to the development of a functional liver. They were also unsuitable for IHC experiments to determine which cell types (if any) have these proteins.

The antibodies, tested assays and samples, and the results obtained were as follows:

Anti-HAAO antibody (ab106436, Abcam, UK) 

• Was tested in western blots of liver, E11.5-E14.5 yolk sac, E14.5 placenta, and E14.5 and E16.5 embryonic liver lysates from wild-type (WT) and Haao-/- mice. The target band (32.5 KD) was visible in the WT liver samples and absent in_Haao_-/- livers, and faintly visible in E11.5-E14.5 WT yolk sac, with intensity gradually increasing in E12.5 and E13.5 WT yolk sac. Multiple strong non-specific bands occurred in all samples, requiring cutting off the >50 KD area of the blots.

• Was re-tested in western blots comparing WT, Haao-/-, and Kynu-/- E9.5-E11.5 embryo, E9.5 yolk sac, and adult liver tissues. It detected the target band faintly only in WT and Kynu-/- liver lysates. No target band could be resolved in E9.5 yolk sac or embryo lysates. Due to the low sensitivity of the antibody, it is unsuitable to conclusively determine whether HAAO is present or absent in E9.5 yolk sacs and E9.5-E11.5 embryos.

• Was tested in IHC with DAB and IF, producing non-specific staining on both WT and Haao-/- liver and kidney tissue. 

Anti-HAAO antibody (NBP1-77361, Novus Biologicals, LLC, CO, USA)

• Was tested in western blots and detected a very faint target band in WT liver lysate that was absent in Haao-/- lysate, with stronger non-specific bands occurring in both genotypes.

• Was tested in IHC with DAB, producing non-specific staining on both WT and Haao-/- liver and kidney tissue 

Anti-L-Kynurenine Hydrolase antibody (11796-1-AP, Proteintech Group, IL, USA)

• Was tested in western blots and detected a faint target band (52 KD) in E11.5, E12.5 E13.5, and E14.5 yolk sac lysates. Detected a weak band in E14.5 liver, a stronger band in E16.5 liver, but not in E14.5 placenta. The target band was only resolved with normal ECL substrate and extended exposure when the >75 KD part of the blot was cut off. 

• Was re-tested in western blots comparing WT, Haao-/-, and Kynu-/- E9.5-E11.5 embryo, E9.5 yolk sac, and adult liver tissues. It detected the target band only in WT and Haao-/- liver lysates, requiring Ultra Sensitive Substrate. No target band could be resolved in yolk sac or embryo lysates of any genotype.

Anti-L-Kynurenine Hydrolase antibody (ab236980, Abcam, UK)

• Was tested in western blots and detected a very faint target band (52 KD) in WT liver lysates and no band in Kynu-/- liver lysates. Multiple non-specific bands occurred irrespective of the Kynu genotype of the lysate.

• Was tested in IHC with DAB and IF, producing non-specific staining on both WT and Kynu-/- liver and kidney tissue 

Anti-QPRT (orb317756, Biorbyt, NC, USA)

• Was tested in western blots and detected a faint target band (31 KD) with multiple other bands between 25-75 KD and an extremely strong band around 150 KD on WT liver lysates.

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

Reviewer 1 Public Review:

The current dietary study narrows the period when deficiency can cause malformations (analysed at E18.5), and altered metabolite profiles (eg, increased 3HAA, lower NAD) are detected in the yolk sac and embryo at E10.5. However, without analysis of embryos at later stages in this experiment it is not known how long is needed for NAD synthesis to be recovered - and therefore until when the period of exposure to insufficient NAD lasts. This information would inform the understanding of the developmental origin of the observed defects.

Our previous published work (Cuny et al 2023 https://doi.org/10.1242/dmm.049647) indicates that the timing of NAD de novo synthesis pathway precursor availability and consequently the timing of NAD deficiency during organogenesis drives which organs are affected in their development. Furthermore, experimental data of another project (manuscript submitted) shows that mouse embryos (from mothers on an NAD precursor restricted diet that induces CNDD) were NAD deficient at E9.5 and E11.5, but embryo NAD levels were fully recovered at E14.5 when compared to same-stage embryos from mothers on precursor-sufficient diet. This was observed irrespective of the embryos’ Haao genotype. In the current study, NAD precursor provision was only restricted until E10.5. Thus, we expect that our embryos phenotyped at E18.5 had recovered their NAD levels back to normal by E14.5 at the latest.  More research, beyond the scope of the current manuscript, is required to spatio-temporally link embryonic NAD deficiency to the occurrence of specific defect types and elucidate the mechanistic origin of the defects. To acknowledge this, we updated the respective Discussion paragraph on page 7 and added the following statement: “This observation supports our hypothesis that the timing of NAD deficiency during organogenesis determines which organs/tissues are affected (Cuny et al., 2023), but more research is needed to fully characterise the onset and duration of embryonic NAD deficiency in dietary NAD precursor restriction mouse models.”

More importantly, there is still a question of whether in addition to the yolk sac, there is HAAO activity within the embryo itself prior to E12.5 (when it has first been assayed in the liver - Figure 1C). The prediction is that within the conceptus (embryo, chorioallantoic placenta, and visceral yok sac) the embryo is unlikely to be the site of NAD synthesis prior to liver development. Reanalysis of scRNA-seq (Fig 1B) shows expression of all the enzymes of the kynurenine pathway from E9.5 onwards. However, the expression of another available dataset at E10.5 (Fig S3) suggested that expression is 'negligible'. While the expression in Figure 1B, Figure S1 is weak this creates a lack of clarity about the possible expression of HAAO in the hepatocyte lineage, or especially elsewhere in the embryo prior to E10.5 (corresponding to the period when the authors have demonstrated that de novo NAD synthesis in the conceptus is needed). Given these questions, a direct analysis of RNA and/or protein expression in the embryos at E7.5-10.5 would be helpful. 

We now have included additional data showing that whole embryos at E11.5 and embryos with their livers removed at E14.5 have negligible HAAO enzyme activity. The observed lack of HAAO activity in the embryo at E11.5 is consistent with the absence of a functional embryonic liver at that stage. Thus, it confirms that the embryo is dependent of extraembryonic tissues (the yolk sac) for NAD de novo synthesis prior to E12.5. The additional datasets are now included in Supplementary Table S1 and as Supplementary Figure 2. The Results section on page 2 has been updated to refer to these datasets.

Reviewer #2 (Public Review): 

Page 4 and Table S4. The descriptors for malformations of organs such as the kidney and vertebrae are quite vague and uninformative. More specific details are required to convey the type and range of anomalies observed as a consequence of NAD deficiency. 

We now provide more information about the malformation types in the Results on page 4. Also, Table S4 now defines the missing vertebral, sternum, and kidney descriptors.

Can the authors define whether the role of the NAD pathway in a couple of tissue or organ systems is the same? By this I mean is the molecular or cellular effect of NAD deficiency is the same in the vertebrae and organs such as the kidney. What unifies the effects on these specific tissues and organs and are all tissues and organs affected? If some are not, can the authors explain why they escape the need for the NAD pathway? 

This is a good comment, highlighting that further research, beyond the scope of this manuscript, is needed to better understand the underlying mechanisms of CNDD causation. We have expanded the Discussion paragraph “NAD deficiency in early organogenesis is sufficient to cause CNDD” to indicate that while the timing of NAD deficiency during embryogenesis explains variability in phenotypes among the CNDD spectrum, it is unknown why other organs/tissues are seemingly not affected by NAD deficiency.

To answer the reviewer’s questions and elucidate the underlying cellular and molecular processes in individual organs affected by NAD deficiency, a multiomic approach is required. This is because NAD is involved in hundreds of molecular and cellular processes affecting gene expression, protein levels, metabolism, etc. For details of NAD functions that have relevance to embryogenesis, the reviewer may refer to our recent review article (Dunwoodie et al 2023 https://doi.org/10.1089/ars.2023.0349). 

Page 5 and Figure 6C. The expectation and conclusion for whether specific genes are expressed in particular cell types in scRNA-seq datasets depend on the number of cells sequenced, the technology (methodology) used, the depth of sequencing, and also the resolution of the analysis. It is therefore essential to perform secondary validation of the analysis of scRNA-seq data. At a minimum, the authors should perform in situ hybridization or immunostaining for Tdo2, Afmid, Kmo, Kynu, Haao, Qprt, and Nadsyn1 or some combination thereof at multiple time points during early mouse embryogenesis to truly understand the spatiotemporal dynamics of expression and NAD synthesis. 

We have tested antibodies against HAAO, KYNU, and QPRT in adult mouse liver samples (the main site of NAD de novo synthesis) but these produced non-specific bands in western blotting experiments. Therefore, immunostaining studies on embryonic tissues were not feasible. 

However, we agree that histological methods such as in situ hybridisation would provide secondary validation of the exact cell types that express these genes. To acknowledge this, we have updated a sentence on page 5 referring to the data shown in Figure 6C as follows: “While histological methods such as in situ hybridisation would be required to confirm the exact cell types expressing these genes, the available expression data indicates that the genes encoding those enzymes required to convert L-kynurenine to NAD (kynurenine pathway) are exclusively expressed in the yolk sac endoderm lineage from the onset of organogenesis (E8.0-8.5).”

Absolute functional proof of the yolk sac endoderm as being essential and required for NAD synthesis in the context of CNDD might require conditional deletion of Haao in the yolk sac versus embryo using appropriate Cre driver lines or in the absence of a conditional allele, could be performed by tetraploid embryo-ES cell complementation approaches. But temporal dietary intervention can also approximate the same thing by perturbing NAD synthesis Shen the yolk sac is the primary source versus when the liver becomes the primary source in the embryo. 

Reviewer 1 has made a similar comment about confirming that indeed NAD de novo synthesis activity is limited to extraembryonic tissues (=yolk sacs) and absent in the embryo prior to development of an embryonic liver. We now have included additional data showing that whole embryos at E11.5 and embryos with their livers removed at E14.5 have negligible HAAO enzyme activity. The observed lack of HAAO activity in the embryo at E11.5 is consistent with the absence of a functional embryonic liver at that stage. We think this provides enough proof that the embryo is dependent of extraembryonic tissues (the yolk sac) for NAD de novo synthesis prior to E12.5. The additional datasets are now included in Supplementary Table S1 and as Supplementary Figure 2. The Results section on page 2 has been updated to refer to these data.

Reviewer #1 (Recommendations For The Authors): 

(1) Introduction (page 1) introduces mouse models with defects in the kynurenine pathway "confirming that NAD de novo synthesis is required during embryogenesis ...". This requirement is revealed by the imposition of maternal dietary deficiency and more detail (or a more clear link to the following sentences) here would help the reader who is not familiar with the previous papers using the HAAO mice and dietary modulation.

We have updated this paragraph in the Introduction to better indicate that the requirement of NAD de novo synthesis for embryogenesis was confirmed in mouse models by modulating the maternal dietary NAD precursor provision during pregnancy.

(2) Discussion - throughout the introduction and results the authors refer to the NAD de novo synthesis pathway, with the study focussing on the effects of HAAO loss of function. Data implies that the kynurenine pathway is active in the yolk sac but whether de novo synthesis from L-tryptophan occurs has not been addressed. The first sub-heading of the discussion could be more accurate referring to the kynurenine pathway, or synthesis from kynurenine. 

We agree that our manuscript needed to make better distinction between NAD de novo synthesis starting from kynurenine and starting from tryptophan. We removed “from Ltryptophan” from the sub-heading in the Discussion and clarified in this paragraph which genes are required to convert tryptophan to kynurenine and which genes to convert kynurenine to NAD. We also updated two Results paragraphs (page 2, 2nd paragraph; page 5, 5th paragraph) to improve clarity.

It is worth noting that our statement in the Discussion “this is the first demonstration of NAD de novo synthesis occurring in a tissue outside of the liver and kidney.” is valid because vascular smooth muscle cells express Tdo2 and in combination with the other requisite genes expressed in endoderm cells, the yolk sac has the capability to synthesise NAD de novo from L-tryptophan.

(3) Outlook - While this section is designed to be looking ahead to the potential implications of the work, the last section on gene therapy of the yolk sac seems far removed from the paper content and highly speculative. I feel this could detract from the main points of the study and could be removed. 

We have updated the Outlook paragraph and shortened the final part to “Further research is required to better understand the mechanisms of CNDD causation and of other causes of adverse pregnancy outcomes involving the yolk sac.”

(4) In Figure 2D it would be useful to label the clusters as the colours in the legend are difficult to match to the heatmap. 

We now have labelled the clusters with lowercase letters above the heatmap to make it easier to match the clusters in Figure 2D to the colours used for designating tissues and genotypes. These labels are described in the figure’s key and the figure legend.  

Reviewer #2 (Recommendations For The Authors): 

Page 4 and Table S4. The descriptors for malformations of organs such as the kidney and vertebrae are quite vague and uninformative. More specific details are required to convey the type and range of anomalies observed as a consequence of NAD deficiency. 

We now provide more information about the malformation types in the Results on page 4. Also, Table S4 now defines the missing vertebral, sternum, and kidney descriptors.

Can the authors define whether the role of the NAD pathway in a couple of tissue or organ systems is the same? By this I mean is the molecular or cellular effect of NAD deficiency is the same in the vertebrae and organs such as the kidney. What unifies the effects on these specific tissues and organs and are all tissues and organs affected? If some are not, can the authors explain why they escape the need for the NAD pathway? 

This is a good comment, highlighting that further research, beyond the scope of this manuscript, is needed to better understand the underlying mechanisms of CNDD causation. We have expanded the Discussion paragraph “NAD deficiency in early organogenesis is sufficient to cause CNDD” to indicate that while the timing of NAD deficiency during embryogenesis explains variability in phenotypes among the CNDD spectrum, it is unknown why other organs/tissues are seemingly not affected by NAD deficiency.

To answer the reviewer’s questions and elucidate the underlying cellular and molecular processes in individual organs affected by NAD deficiency, a multiomic approach is required. This is because NAD is involved in hundreds of molecular and cellular processes affecting gene expression, protein levels, metabolism, etc. For details of NAD functions that have relevance to embryogenesis, the reviewer may refer to our recent review article (Dunwoodie et al 2023 https://doi.org/10.1089/ars.2023.0349). 

Page 5 and Figure 6C. The expectation and conclusion for whether specific genes are expressed in particular cell types in scRNA-seq datasets depend on the number of cells sequenced, the technology (methodology) used, the depth of sequencing, and also the resolution of the analysis. It is therefore essential to perform secondary validation of the analysis of scRNA-seq data. At a minimum, the authors should perform in situ hybridization or immunostaining for Tdo2, Afmid, Kmo, Kynu, Haao, Qprt, and Nadsyn1 or some combination thereof at multiple time points during early mouse embryogenesis to truly understand the spatiotemporal dynamics of expression and NAD synthesis. 

We have tested antibodies against HAAO, KYNU, and QPRT in adult mouse liver samples (the main site of NAD de novo synthesis) but these produced non-specific bands in western blotting experiments. Therefore, immunostaining studies on embryonic tissues were not feasible. 

However, we agree that histological methods such as in situ hybridisation would provide secondary validation of the exact cell types that express these genes. To acknowledge this, we have updated a sentence on page 5 referring to the data shown in Figure 6C as follows: “While histological methods such as in situ hybridisation would be required to confirm the exact cell types expressing these genes, the available expression data indicates that the genes encoding those enzymes required to convert L-kynurenine to NAD (kynurenine pathway) are exclusively expressed in the yolk sac endoderm lineage from the onset of organogenesis (E8.0-8.5).”

eLife Assessment

This manuscript addresses the role of alpha oscillations in sensory gain control. The authors use an attention-cuing task in an initial EEG study followed by a separate MEG replication study to demonstrate that whilst (occipital) alpha oscillations are increased when anticipating an auditory target, so is visual responsiveness as assessed with frequency tagging. The authors propose their results demonstrate a general vigilance effect on sensory processing and offer a re-interpretation of the inhibitory role of the alpha rhythm. While these results are valuable, the provided evidence is incomplete.

Reviewer #1 (Public review):

In this paper by Brickwedde et al., the authors observe an increase in posterior alpha when anticipating auditory as opposed to visual targets. The authors also observe an enhancement in both visual and auditory steady-state sensory evoked potentials in anticipation of auditory targets, in correlation with enhanced occipital alpha. The authors conclude that alpha does not reflect inhibition of early sensory processing, but rather orchestrates signal transmission to later stages of the sensory processing stream. However, there are several major concerns that need to be addressed in order to draw this conclusion.

First, I am not convinced that the frequency tagging method and the associated analyses are adequate for dissociating visual vs auditory steady-state sensory evoked potentials.

Second, if the authors want to propose a general revision for the function of alpha, it would be important to show that alpha effects in the visual cortex for visual perception are analogous to alpha effects in the auditory cortex for auditory perception.

Third, the authors propose an alternative function for alpha - that alpha orchestrates signal transmission to later stages of the sensory processing stream. However, the supporting evidence for this alternative function is lacking. I will elaborate on these major concerns below.

(1) Potential bleed-over across frequencies in the spectral domain is a major concern for all of the results in this paper. The fact that alpha power, 36Hz and 40Hz frequency-tagged amplitude and 4Hz intermodulation frequency power is generally correlated with one another amplifies this concern. The authors are attaching specific meaning to each of these frequencies, but perhaps there is simply a broadband increase in neural activity when anticipating an auditory target compared to a visual target?

(2) Moreover, 36Hz visual and 40Hz auditory signals are expected to be filtered in the neocortex. Applying standard filters and Hilbert transform to estimate sensory evoked potentials appears to rely on huge assumptions that are not fully substantiated in this paper. In Figure 4, 36Hz "visual" and 40Hz "auditory" signals seem largely indistinguishable from one another, suggesting that the analysis failed to fully demix these signals.

(3) The asymmetric results in the visual and auditory modalities preclude a modality-general conclusion about the function of alpha. However, much of the language seems to generalize across sensory modalities (e.g., use of the term 'sensory' rather than 'visual').

(4) In this vein, some of the conclusions would be far more convincing if there was at least a trend towards symmetry in source-localized analyses of MEG signals. For example, how does alpha power in the primary auditory cortex (A1) compare when anticipating auditory vs visual target? What do the frequency-tagged visual and auditory responses look like when just looking at the primary visual cortex (V1) or A1?

(5) Blinking would have a huge impact on the subject's ability to ignore the visual distractor. The best thing to do would be to exclude from analysis all trials where the subjects blinked during the cue-to-target interval. The authors mention that in the MEG experiment, "To remove blinks, trials with very large eye-movements (> 10 degrees of visual angle) were removed from the data (See supplement Fig. 5)." This sentence needs to be clarified since eye-movements cannot be measured during blinking. In addition, it seems possible to remove putative blink trials from EEG experiments as well, since blinks can be detected in the EEG signals.

(6) It would be interesting to examine the neutral cue trials in this task. For example, comparing auditory vs visual vs neutral cue conditions would be indicative of whether alpha was actively recruited or actively suppressed. In addition, comparing spectral activity during cue-to-target period on neutral-cue auditory correct vs incorrect trials should mimic the comparison of auditory-cue vs visual-cue trials. Likewise, neutral-cue visual correct vs incorrect trials should mimic the attention-related differences in visual-cue vs auditory-cue trials.

(7) In the abstract, the authors state that "This implies that alpha modulation does not solely regulate 'gain control' in early sensory areas but rather orchestrates signal transmission to later stages of the processing stream." However, I don't see any supporting evidence for the latter claim, that alpha orchestrates signal transmission to later stages of the processing stream. If the authors are claiming an alternative function to alpha, this claim should be strongly substantiated.

Reviewer #2 (Public review):

Brickwedde et al. investigate the role of alpha oscillations in allocating intermodal attention. A first EEG study is followed up with a MEG study that largely replicates the pattern of results (with small to be expected differences). They conclude that a brief increase in the amplitude of auditory and visual stimulus-driven continuous (steady-state) brain responses prior to the presentation of an auditory - but not visual - target speaks to the modulating role of alpha that leads them to revise a prevalent model of gating-by-inhibition.

Overall, this is an interesting study on a timely question, conducted with methods and analysis that are state-of-the-art. I am particularly impressed by the author's decision to replicate the earlier EEG experiment in MEG following the reviewer's comments on the original submission. Evidently, great care was taken to accommodate the reviewer's suggestions.

Nevertheless, I am struggling with the report for two main reasons: It is difficult to follow the rationale of the study, due to structural issues with the narrative and missing information or justifications for design and analysis decisions, and I am not convinced that the evidence is strong, or even relevant enough for revising the mentioned alpha inhibition theory. Both points are detailed further below.

Strength/relevance of evidence for model revision: The main argument rests on 1) a rather sustained alpha effect following the modality cue, 2) a rather transient effect on steady-state responses just before the expected presentation of a stimulus, and 3) a correlation between those two. Wouldn't the authors expect a sustained effect on sensory processing, as measured by steady-state amplitude irrespective of which of the scenarios described in Figure 1A (original vs revised alpha inhibition theory) applies? Also, doesn't this speak to the role of expectation effects due to consistent stimulus timing? An alternative explanation for the results may look like this: Modality-general increased steady-state responses prior to the expected audio stimulus onset are due to increased attention/vigilance. This effect may be exclusive (or more pronounced) in the attend-audio condition due to higher precision in temporal processing in the auditory sense or, vice versa, too smeared in time due to the inferior temporal resolution of visual processing for the attend-vision condition to be picked up consistently. As expectation effects will build up over the course of the experiment, i.e., while the participant is learning about the consistent stimulus timing, the correlation with alpha power may then be explained by a similar but potentially unrelated increase in alpha power over time.

Structural issues with the narrative and missing information: Here, I am mostly concerned with how this makes the research difficult to access for the reader. I list the major points below:

In the introduction the authors pit the original idea about alpha's role in gating against some recent contradictory results. If it's the aim of the study to provide evidence for either/or, predictions for the results from each perspective are missing. Also, it remains unclear how this relates to the distinction between original vs revised alpha inhibition theory (Fig. 1A). Relatedly if this revision is an outcome rather than a postulation for this study, it shouldn't be featured in the first figure.

The analysis of the intermodulation frequency makes a surprise entrance at the end of the Results section without an introduction as to its relevance for the study. This is provided only in the discussion, but with reference to multisensory integration, whereas the main focus of the study is focussed attention on one sense. (Relatedly, the reference to "theta oscillations" in this sections seems unclear without a reference to the overlapping frequency range, and potentially more explanation.) Overall, if there's no immediate relevance to this analysis, I would suggest removing it.

Reviewer #3 (Public review):

Brickwedde et al. attempt to clarify the role of alpha in sensory gain modulation by exploring the relationship between attention-related changes in alpha and attention-related changes in sensory-evoked responses, which surprisingly few studies have examined given the prevalence of the alpha inhibition hypothesis. The authors use robust methods and provide novel evidence that alpha likely exhibits inhibitory control over later processing, as opposed to early sensory processing, by providing source-localization data in a cross-modal attention task.

This paper seems very strong, particularly given that the follow-up MEG study both (a) clarifies the task design and separates the effect of distractor stimuli into other experimental blocks, and (b) provides source-localization data to more concretely address whether alpha inhibition is occurring at or after the level of sensory processing, and (c) replicates most of the EEG study's key findings.

There are some points that would be helpful to address to bolster the paper. First, the introduction would benefit from a somewhat deeper review of the literature, not just reviewing when the effects of alpha seem to occur, but also addressing how the effect can change depending on task and stimulus design (see review by Morrow, Elias & Samaha (2023). Additionally, the discussion could benefit from more cautionary language around the revision of the alpha inhibition account. For example, it would be helpful to address some of the possible discrepancies between alpha and SSEP measures in terms of temporal specificity, SNR, etc. (see Peylo, Hilla, & Sauseng, 2021). The authors do a good job speculating as to why they found differing results from previous cross-modal attention studies, but I'm also curious whether the authors think that alpha inhibition/modulation of sensory signals would have been different had the distractors been within the same modality or whether the cues indicated target location, rather than just modality, as has been the case in so much prior work?

Overall, the analyses and discussion are quite comprehensive, and I believe this paper to be an excellent contribution to the alpha-inhibition literature.

Author response:

Public Reviews:

Reviewer #1 (Public review):

In this paper by Brickwedde et al., the authors observe an increase in posterior alpha when anticipating auditory as opposed to visual targets. The authors also observe an enhancement in both visual and auditory steady-state sensory evoked potentials in anticipation of auditory targets, in correlation with enhanced occipital alpha. The authors conclude that alpha does not reflect inhibition of early sensory processing, but rather orchestrates signal transmission to later stages of the sensory processing stream. However, there are several major concerns that need to be addressed in order to draw this conclusion.

First, I am not convinced that the frequency tagging method and the associated analyses are adequate for dissociating visual vs auditory steady-state sensory evoked potentials.

Second, if the authors want to propose a general revision for the function of alpha, it would be important to show that alpha effects in the visual cortex for visual perception are analogous to alpha effects in the auditory cortex for auditory perception.

Third, the authors propose an alternative function for alpha - that alpha orchestrates signal transmission to later stages of the sensory processing stream. However, the supporting evidence for this alternative function is lacking. I will elaborate on these major concerns below.

(1) Potential bleed-over across frequencies in the spectral domain is a major concern for all of the results in this paper. The fact that alpha power, 36Hz and 40Hz frequency-tagged amplitude and 4Hz intermodulation frequency power is generally correlated with one another amplifies this concern. The authors are attaching specific meaning to each of these frequencies, but perhaps there is simply a broadband increase in neural activity when anticipating an auditory target compared to a visual target?

We appreciate the reviewer’s insightful comment regarding the potential bleed-over across frequencies in the spectral domain. We fully acknowledge that the trade-off between temporal and frequency resolution is a challenge, particularly given the proximity of the frequencies we are examining.

To address this concern, we performed additional analyses to investigate whether there is indeed a broadband increase in neural activity when anticipating an auditory target as compared to a visual target, as opposed to distinct frequency-specific effects. Our results show that the bleed-over between frequencies is minimal and does not significantly affect our findings. Specifically, we repeated the analyses using the same filter and processing steps for the 44 Hz frequency. At this frequency, we did not observe any significant differences between conditions.

These findings suggest that the effects we report are indeed specific to the 40 Hz frequency band and not due to a general broadband increase in neural activity. We hope this addresses the reviewer’s concern and strengthens the validity of our frequency-specific results.

Author response image 1.

Illustration of bleeding over effects over a span of 4 Hz. A, 40 Hz frequency-tagging data over the significant cluster differing between when expecting an auditory versus a visual target (identical to Fig. 9 in the manuscript). B, 44 Hz signal over the same cluster chosen for A. The analysis was identical with the analysis performed in  A, apart from the frequency for the band-pass filter.

We do, however, not specifically argue against the possibility of a broadband increase when anticipating an auditory compared to a visual target. But even a broadband-increase would directly contradict the alpha inhibition hypothesis, which poses that an increase in alpha completely disengages the whole cortex. We will clarify this point in the revised manuscript.

(2) Moreover, 36Hz visual and 40Hz auditory signals are expected to be filtered in the neocortex. Applying standard filters and Hilbert transform to estimate sensory evoked potentials appears to rely on huge assumptions that are not fully substantiated in this paper. In Figure 4, 36Hz "visual" and 40Hz "auditory" signals seem largely indistinguishable from one another, suggesting that the analysis failed to fully demix these signals.

We appreciate the reviewer’s insightful concern regarding the filtering and demixing of the 36 Hz visual and 40 Hz auditory signals, and we share the same reservations about the reliance on standard filters and the Hilbert transform method.

To address this, we would like to draw attention to Author response image 1, which demonstrates that a 4 Hz difference is sufficient to effectively demix the signals using our chosen filtering and Hilbert transform approach. We believe that the reason the 36 Hz visual and 40 Hz auditory signals show similar topographies lies not in incomplete demixing but rather in the possibility that this condition difference reflects sensory integration, rather than signal contamination.

This interpretation is further supported by our findings with the intermodulation frequency at 4 Hz, which also suggests cross-modal integration. Furthermore, source localization analysis revealed that the strongest condition differences were observed in the precuneus, an area frequently associated with sensory integration processes. We will expand on this in the discussion section to better clarify this point.

(3) The asymmetric results in the visual and auditory modalities preclude a modality-general conclusion about the function of alpha. However, much of the language seems to generalize across sensory modalities (e.g., use of the term 'sensory' rather than 'visual').

We thank the reviewer for pointing this out and agree that in some cases we have not made a good enough distinction between visual and sensory. We will make sure, that when using ‘sensory’, we either describe overall theories, which are not visual-exclusive or refer to the possibility of a broad sensory increase. However, when directly discussing our results and the interpretation thereof, we will now use ‘visual’ in the revised manuscript.

(4) In this vein, some of the conclusions would be far more convincing if there was at least a trend towards symmetry in source-localized analyses of MEG signals. For example, how does alpha power in the primary auditory cortex (A1) compare when anticipating auditory vs visual target? What do the frequency-tagged visual and auditory responses look like when just looking at the primary visual cortex (V1) or A1?

We thank the reviewer for this important suggestion and have added a virtual channel analysis. We were however, not interested in alpha power in primary auditory cortex, as we were specifically interested in the posterior alpha, which is usually increased when expecting an auditory compared to a visual target (and used to be interpreted as a blanket inhibition of the visual cortex). We will improve upon the clarity concerning this point in the manuscript.

We have however, followed the reviewer’s suggestion of a virtual channel analysis, showing that the condition differences are not observable in primary visual cortex for the 36 Hz visual signal and in primary auditory cortex for the 40 Hz auditory signal. Our data clearly shows that there is an alpha condition difference in V1, while there no condition difference for 36 Hz in V1 and for 40 Hz in Heschl’s Gyrus (see Author response image 2).

Author response image 2.

Virtual channels for V1 and Helschl’s gyrus. A, alpha power for the virtual channel created in V1 (Calcerine_L and Calcerine_R from AAL atlas; Tzourio-Mazoyer et al., 2002, NeuroImage). A cluster permutation analysis over time (between -2 and 0) revealed a significant condition difference between ~ -2 and -1.7 s (p = 0.0449). B, 36 Hz frequency-tagging signal for the virtual channel created in V1 (equivalent to the procedure in A). The same cluster permutation as performed in A revealed no significant condition differences. C, 40 Hz frequency-tagging signal for the virtual channel created in Heschl’s gryrus (Heschl_L and Heschl_R from AAL atlas; Tzourio-Mazoyer et al., 2002, NeuroImage). The same cluster permutation as performed in A revealed no significant condition differences.

(5) Blinking would have a huge impact on the subject's ability to ignore the visual distractor. The best thing to do would be to exclude from analysis all trials where the subjects blinked during the cue-to-target interval. The authors mention that in the MEG experiment, "To remove blinks, trials with very large eye-movements (> 10 degrees of visual angle) were removed from the data (See supplement Fig. 5)." This sentence needs to be clarified since eye-movements cannot be measured during blinking. In addition, it seems possible to remove putative blink trials from EEG experiments as well, since blinks can be detected in the EEG signals.

We thank the reviewer for mentioning that we were making this point confusing. From the MEG-data, we removed eyeblinks using ICA. Alone for the supplementary Fig. 5 analysis, we used the eye-tracking data to confirm that participants were in fact fixating the centre of the screen. For this analysis, we removed trials with blinks (which can be seen in the eye-tracker as huge amplitude movements or as large eye-movements in degrees of visual angle; see Author response image 3 below to show a blink in the MEG data and the according eye-tracker data in degrees of visual angle). We will clarify this in the methods section.

As for the concern closed eyes to ignore visual distractors, in both experiments we can observe highly significant distractor cost in accuracy for visual distractors, which we hope will convince the reviewer that our visual distractors were working as intended.

Author response image 3.

Illustration of eye-tracker data for a trial without and a trial with a blink. All data points recorded during this trial are plottet. A, ICA component 1, which reflects blinks and its according data trace in a trial. No blink is visible. B, eye-tracker data transformed into degrees of visual angle for the trial depicted in A. C, ICA component 1, which reflects blinks and its according data trace in a trial. A clear blink is visible. D, eye-tracker data transformed into degrees of visual angle for the trial depicted in C.

(6) It would be interesting to examine the neutral cue trials in this task. For example, comparing auditory vs visual vs neutral cue conditions would be indicative of whether alpha was actively recruited or actively suppressed. In addition, comparing spectral activity during cue-to-target period on neutral-cue auditory correct vs incorrect trials should mimic the comparison of auditory-cue vs visual-cue trials. Likewise, neutral-cue visual correct vs incorrect trials should mimic the attention-related differences in visual-cue vs auditory-cue trials.

We thank the reviewer for this suggestion. We have analysed the neutral cue trials in the EEG dataset (see suppl. Fig. 1) and will expand this figure to show all conditions. There were no significant differences to auditory or visual cues, but descriptively alpha power was higher for neutral cues compared to visual cues and lower for neutral cues compared to auditory cues. While this may suggest that for visual trials alpha is actively suppressed and for auditory trials actively recruited, we do not feel comfortable to make this claim, as the neutral condition may not reflect a completely neutral state. The neutral task can still be difficult, especially because of the uncertainty of the target modality.

As for the analysis of incorrect versus correct trials, we love the idea, but unfortunately the accuracy rate was quite high so that the number of incorrect trials would not be sufficient to perform a reliable analysis.

(7) In the abstract, the authors state that "This implies that alpha modulation does not solely regulate 'gain control' in early sensory areas but rather orchestrates signal transmission to later stages of the processing stream." However, I don't see any supporting evidence for the latter claim, that alpha orchestrates signal transmission to later stages of the processing stream. If the authors are claiming an alternative function to alpha, this claim should be strongly substantiated.

We thank the reviewer for pointing out, that we have not sufficiently explained our case. The first point refers to gain control akin to the alpha inhibition hypothesis, which claims that increases in alpha disengage a whole cortical area. Since we have confirmed the alpha increase in our data to originate from primary visual cortex through source analysis, this should lead to decreased visual processing. The increase in 36 Hz visual processing therefore directly contradicts the alpha inhibition hypothesis. We propose an alternative explanation for the functionality of alpha activity in this task. Through pulsed inhibition, information packages of relevant visual information could be transmitted down the processing stream, thereby enhancing relevant visual signal transmission. We believe the fact that the enhanced visual 36 Hz signal we found correlated with visual alpha power on a trial-by-trial basis, and did not originate from primary visual cortex, but from areas known for sensory integration supports our claim.

We will make this point clearer in our revised manuscript.

Reviewer #2 (Public review):

Brickwedde et al. investigate the role of alpha oscillations in allocating intermodal attention. A first EEG study is followed up with a MEG study that largely replicates the pattern of results (with small to be expected differences). They conclude that a brief increase in the amplitude of auditory and visual stimulus-driven continuous (steady-state) brain responses prior to the presentation of an auditory - but not visual - target speaks to the modulating role of alpha that leads them to revise a prevalent model of gating-by-inhibition.

Overall, this is an interesting study on a timely question, conducted with methods and analysis that are state-of-the-art. I am particularly impressed by the author's decision to replicate the earlier EEG experiment in MEG following the reviewer's comments on the original submission. Evidently, great care was taken to accommodate the reviewer's suggestions.

We thank the reviewer for the positive feedback and expression of interest in the topic of our manuscript.

Nevertheless, I am struggling with the report for two main reasons: It is difficult to follow the rationale of the study, due to structural issues with the narrative and missing information or justifications for design and analysis decisions, and I am not convinced that the evidence is strong, or even relevant enough for revising the mentioned alpha inhibition theory. Both points are detailed further below.

We thank the reviewer for raising this important point. We will revise our introduction and results in line with the reviewer’s suggestions, hoping that our rationale will then be easier to follow and that our evidence will be more convincing.

Strength/relevance of evidence for model revision: The main argument rests on 1) a rather sustained alpha effect following the modality cue, 2) a rather transient effect on steady-state responses just before the expected presentation of a stimulus, and 3) a correlation between those two. Wouldn't the authors expect a sustained effect on sensory processing, as measured by steady-state amplitude irrespective of which of the scenarios described in Figure 1A (original vs revised alpha inhibition theory) applies? Also, doesn't this speak to the role of expectation effects due to consistent stimulus timing? An alternative explanation for the results may look like this: Modality-general increased steady-state responses prior to the expected audio stimulus onset are due to increased attention/vigilance. This effect may be exclusive (or more pronounced) in the attend-audio condition due to higher precision in temporal processing in the auditory sense or, vice versa, too smeared in time due to the inferior temporal resolution of visual processing for the attend-vision condition to be picked up consistently. As expectation effects will build up over the course of the experiment, i.e., while the participant is learning about the consistent stimulus timing, the correlation with alpha power may then be explained by a similar but potentially unrelated increase in alpha power over time.

We thank the reviewer for raising these insightful questions and suggestions.

It is true that our argument rests on a rather sustained alpha effect and a rather transient effect on steady-state responses and a correlation between the two. However, this connection would not be expected under the alpha inhibition hypothesis, which states that alpha activity would inhibit a whole cortical area (when irrelevant to the task), exerting “gain control”. This notion directly contradicts our results of the “irrelevant” visual information a) being transmitted at all and b) increasing.

However, it has been shown on many occasions that alpha activity exerts pulsed inhibition, so we proposed an alternative theory of an involvement in signal transmission. In this case, the cyclic inhibition would serve as an ordering system, which only allows for high-priority information to pass, resulting in higher signa-to-noise. We do not make a claim about how fast or when these signals are transmitted in relation to alpha power. For instance, it could be that alpha power increases as a preparatory state even before signal is actually transmitted.  Zhigalov (2020 Hum. Brain M.) has shown that in V1, frequency-tagging responses were up-and down regulated with attention – independent of alpha activity.

But we do believe that the fact that visual alpha power correlates on a trial-by-trial level with visual 36 Hz frequency-tagging increases and (a relationship which has not been found in V1, see Zhigalov 2020, Hum. Brain Mapp.) suggest a strong connection. Furthermore, the fact that the alpha modulation originates from early visual areas and occurs prior to any frequency-tagging changes, while the increase in frequency-tagging can be observed in areas which are later in the processing stream (such as the precuneus) is strongly indicative for an involvement of alpha power in the transmission of this signal. We cannot fully exclude alternative accounts and mechanisms which effect both alpha power and frequency-tagging responses. 

We do believe that the alternative account described by the reviewer does not contradict our theory, as we do believe that the alpha power modulation may reflect an expectation effect (and the idea that it could be related to the resolution of auditory versus visual processing is very interesting!). It is also possible that this expectation is, as the reviewer suggests, related to attention/vigilance and might result in a modality-general signal increase. And indeed, we can observe an increase in the frequency-tagging response in sensory integration areas. Accordingly, we believe that the alternative explanation provided by the reviewer contradicts the alpha inhibition hypothesis, but not necessarily our alternative theory.

We will revise the discussion, which we hope will make our case stronger and easier to follow. Additionally, we will mention the possibility for alternative explanations as well as the possibility, that alpha networks fulfil different roles in different locations/task environments.

Structural issues with the narrative and missing information: Here, I am mostly concerned with how this makes the research difficult to access for the reader. I list the major points below:

In the introduction the authors pit the original idea about alpha's role in gating against some recent contradictory results. If it's the aim of the study to provide evidence for either/or, predictions for the results from each perspective are missing. Also, it remains unclear how this relates to the distinction between original vs revised alpha inhibition theory (Fig. 1A). Relatedly if this revision is an outcome rather than a postulation for this study, it shouldn't be featured in the first figure.

We agree with the reviewer that we have not sufficiently clarified our goal as well as how different functionalities of alpha oscillations would lead to different outcomes. We will revise the introduction and restructure the results and hope that it will be easier to follow.

The analysis of the intermodulation frequency makes a surprise entrance at the end of the Results section without an introduction as to its relevance for the study. This is provided only in the discussion, but with reference to multisensory integration, whereas the main focus of the study is focussed attention on one sense. (Relatedly, the reference to "theta oscillations" in this sections seems unclear without a reference to the overlapping frequency range, and potentially more explanation.) Overall, if there's no immediate relevance to this analysis, I would suggest removing it.

We thank the reviewer for pointing this out and will add information about this frequency to the introduction part. We believe that the intermodulation frequency analysis is important, as it potentially supports the notion that condition differences in the visual-frequency tagging response are related to downstream processing rather than overall visual information processing in V1. We would therefore prefer to leave this analysis in the manuscript.

Reviewer #3 (Public review):

Brickwedde et al. attempt to clarify the role of alpha in sensory gain modulation by exploring the relationship between attention-related changes in alpha and attention-related changes in sensory-evoked responses, which surprisingly few studies have examined given the prevalence of the alpha inhibition hypothesis. The authors use robust methods and provide novel evidence that alpha likely exhibits inhibitory control over later processing, as opposed to early sensory processing, by providing source-localization data in a cross-modal attention task.

This paper seems very strong, particularly given that the follow-up MEG study both (a) clarifies the task design and separates the effect of distractor stimuli into other experimental blocks, and (b) provides source-localization data to more concretely address whether alpha inhibition is occurring at or after the level of sensory processing, and (c) replicates most of the EEG study's key findings.

We are very grateful to the reviewer for their positive feedback and evaluation of our work.

There are some points that would be helpful to address to bolster the paper. First, the introduction would benefit from a somewhat deeper review of the literature, not just reviewing when the effects of alpha seem to occur, but also addressing how the effect can change depending on task and stimulus design (see review by Morrow, Elias & Samaha (2023).

We thank the reviewer for this suggestion and agree. We will add a paragraph to the introduction which refers to missing correlation studies and the impact of task design.

Additionally, the discussion could benefit from more cautionary language around the revision of the alpha inhibition account. For example, it would be helpful to address some of the possible discrepancies between alpha and SSEP measures in terms of temporal specificity, SNR, etc. (see Peylo, Hilla, & Sauseng, 2021). The authors do a good job speculating as to why they found differing results from previous cross-modal attention studies, but I'm also curious whether the authors think that alpha inhibition/modulation of sensory signals would have been different had the distractors been within the same modality or whether the cues indicated target location, rather than just modality, as has been the case in so much prior work?

We thank the reviewer for suggesting these interesting discussion points and will include a paragraph in our discussion which goes deeper into these topics.

Overall, the analyses and discussion are quite comprehensive, and I believe this paper to be an excellent contribution to the alpha-inhibition literature.

eLife Assessment

This study presents a valuable finding on the importance of the plasma metabolome in glaucoma risk prediction. The authors have used the UK Biobank data to interrogate the association between plasma metabolites and glaucoma. The evidence supporting the claims of the authors is solid and the work offers insights into the design of protective therapeutic strategies for glaucoma.

Reviewer #1 (Public review):

Summary:

The authors explore associations between plasma metabolites and glaucoma, a primary cause of irreversible vision loss worldwide. The study relies on measurements of 168 plasma metabolites in 4,658 glaucoma patients and 113,040 controls from the UK Biobank. The authors show that metabolites improve the prediction of glaucoma risk based on polygenic risk score (PRS) alone, albeit weakly. The authors also report a "metabolomic signature" that is associated with a reduced risk (or "resilience") for developing glaucoma among individuals in the highest PRS decile (reduction of risk by an estimated 29%). The authors highlight the protective effect of pyruvate, a product of glycolysis, for glaucoma development and show that this molecule mitigates elevated intraocular pressure and optic nerve damage in a mouse model of this disease.

Strengths:

This work provides additional evidence that glycolysis may play a role in the pathophysiology of glaucoma. Previous studies have demonstrated the existence of an inverse relationship between intraocular pressure and retinal pyruvate levels in animal models (Hader et al. 2020, PNAS 117(52)) and pyruvate supplementation is currently being explored for neuro-enhancement in patients with glaucoma (De Moraes et al. 2022, JAMA Ophthalmology 140(1)). The study design is rigorous and relies on validated, standard methods. Additional insights gained from a mouse model are valuable.

Weaknesses:

Caution is warranted when examining and interpreting the results of this study. Among all participants (cases and controls) glaucoma status was self-reported, determined on the basis of ICD codes or previous glaucoma laser/surgical therapy. This is problematic as it is not uncommon for individuals in the highest PRS decile to have undiagnosed glaucoma (as shown in previous work by some of the authors of this article). The authors acknowledge a "relatively low glaucoma prevalence in the highest decile group" but do not explore how undiagnosed glaucoma may affect their results. This also applies to all controls selected for this study. The authors state that "50 to 70% of people affected [with glaucoma] remain undiagnosed". Therefore, the absence of self-reported glaucoma does not necessarily indicate that the disease is not present. Validation of the findings from this study in humans is, therefore, critical. This should ideally be performed in a well-characterized glaucoma cohort, in which case and control status has been assessed by qualified clinicians.

The authors indicate that within the top decile of PRS participants with glaucoma are more likely to be of white ethnicity, while they are more likely to be of Black and Asian ethnicity if they are in the bottom half of PRS. Have the authors explored how sensitive their predictions are to ethnicity? Since their cohort is predominantly of European ancestry (85.8%), would it make sense to exclude other ethnicities to increase the homogeneity of the cohort and reduce the risk for confounders that may not be explicitly accounted for?

The authors discuss the importance of pyruvate, and lactate for retinal ganglion cell survival, along with that of several lipoproteins for neuroprotection. However, there is a distinction to be made between locally produced/available glycolysis end products and lipoproteins and those circulating in the blood. It may be useful to discuss this in the manuscript, and for the authors to explore if plasma metabolites may be linked to metabolism that takes place past the blood-retinal barrier.

Reviewer #2 (Public review):

Summary:

The authors have used the UK Biobank data to interrogate the association between plasma metabolites and glaucoma.

(1) They initially assessed plasma metabolites as predictors of glaucoma: The addition of NMR-derived metabolomic data to existing models containing clinical and genetic data was marginal.

(2) They then determined whether certain metabolites might protect against glaucoma in individuals at high genetic risk: Certain molecules in bioenergetic pathways (lactate, pyruvate, and citrate) conferred protection.

(3) They provide support for protection conferred by pyruvate in a murine model.

Strengths:

(1) The huge sample size supports a powerful statistical analysis and the opportunity for the inclusion of multiple covariates and interactions without overfitting the models.

(2) The authors have constructed a robust methodology and statistical design.

(3) The manuscript is well written, and the study is logically presented.

(4) The figures are of good quality.

(5) Broadly, the conclusions are justified by the findings.

Weaknesses:

(1) Although it is an invaluable treasure trove of data, selection bias and self-reporting are inescapable problems when using the UK Biobank data for glaucoma research. The high-impact glaucoma-related GWAS publications (references 26 and 27) referenced in support of the method suffer the same limitations. This doesn't negate the conclusions but must be taken into consideration. The authors might note that it is somewhat reassuring that the proportion of glaucoma cases (4%) is close to what would be expected in a population-based study of 40-69-year-olds of predominantly white ethnicity.

(2) As noted by the authors, a limitation is the predominantly white ethnicity profile that comprises the UK Biobank.

(3) Also as noted by the authors, the study is cross-sectional and is limited by the "correlation does not imply causation" issue.

(4) The optimal collection, transport, and processing of the samples for NMR metabolite analysis is critical for accurate results. Strict policies were in place for these procedures, but deviations from protocol remain an unknown influence on the data.

(5) In addition, all UK Biobank blood samples had unintended dilution during the initial sample storage process at UK Biobank facilities. (Julkunen, H. et al. Atlas of plasma NMR biomarkers for health and disease in 118,461 individuals from the UK Biobank. Nat Commun 14, 604 (2023) Samples from aliquot 3, used for the NMR measurements, suffered from 5-10% dilution. (Allen, Naomi E., et al. Wellcome Open Research 5 (2021): 222.) Julkunen et al. report that "The dilution is believed to come from mixing of participant samples with water due to seals that failed to hold a system vacuum in the automated liquid handling systems. While this issue is likely to have an impact on some of the absolute biomarker concentration values, it is expected to have limited impact on most epidemiological analyses."

Impact:

The findings advance personalized prognostics for glaucoma that combine metabolomic and genetic data. In addition, the protective effect of certain metabolites influences further research on novel therapeutic strategies.

eLife Assessment

This important study examines the neuronal mechanisms underlying visual perception of integrated face and body cues. The innovative paradigm, which employs monkey avatars in combination with electrophysiological recordings from fMRI-defined brain areas, is a compelling approach. These results should be of wide interest to system and cognitive neuroscientists, psychologists, and behavioural biologists working on visual and social cognition.

Reviewer #1 (Public review):

Summary:

The study addresses how faces and bodies are integrated in two STS face areas revealed by fMRI in the primate brain. It builds upon recordings and analysis of the responses of large populations of neurons to three sets of images, that vary face and body positions. These sets allowed the authors to thoroughly investigate invariance to position on the screen (MC HC), to pose (P1 P2), to rotation (0 45 90 135 180 225 270 315), to inversion, to possible and impossible postures (all vs straight), to the presentation of head and body together or in isolation. By analyzing neuronal responses, they found that different neurons showed preferences for body orientation, head orientation, or the interaction between the two. By using a linear support vector machine classifier, they show that the neuronal population can decode head-body angle presented across orientations, in the anterior aSTS patch (but not middle mSTS patch), except for mirror orientation.

Strengths:

These results extend prior work on the role of Anterior STS fundus face area in face-body integration and its invariance to mirror symmetry, with a rigorous set of stimuli revealing the workings of these neuronal populations in processing individuals as a whole, in an important series of carefully designed conditions.

Minor issues and questions that could be addressed by the authors:

(1) Methods. While monkeys certainly infer/recognize that individual pictures refer to the same pose with varying orientations based on prior studies (Wang et al.), I am wondering whether in this study monkeys saw a full rotation of each of the monkey poses as a video before seeing the individual pictures of the different orientations, during recordings.

(2) Experiment 1. The authors mention that neurons are preselected as face-selective, body-selective, or both-selective. Do the Monkey Sum Index and ANOVA main effects change per Neuron type?

(3) I might have missed this information, but the correlation between P1 and P2 seems to not be tested although they carry similar behavioral relevance in terms of where attention is allocated and where the body is facing for each given head-body orientation.

(4) Is the invariance for position HC-MC larger in aSTS neurons compared to mSTS neurons, as could be expected from their larger receptive fields?

(5) L492 "The body-inversion effect likely results from greater exposure to upright than inverted bodies during development". Monkeys display more hanging upside-down behavior than humans, however, does the head appear more tilted in these natural configurations?

(6) Methods in Experiment 1. SVM. How many neurons are sufficient to decode the orientation?

(7) Figure 3D 3E. Could the authors please indicate for each of these neurons whether they show a main effect of face, body, or interaction, as well as their median corrected correlation to get a flavor of these numbers for these examples?

(8) Methods and Figure 1A. It could be informative to precise whether the recordings are carried in the lateral part of the STS or in the fundus of the STS both for aSTS and mSTS for comparison to other studies that are using these distinctions (AF, AL, MF, ML).

Wang, G., Obama, S., Yamashita, W. et al. Prior experience of rotation is not required for recognizing objects seen from different angles. Nat Neurosci 8, 1768-1775 (2005). https://doi-org.insb.bib.cnrs.fr/10.1038/nn1600

Reviewer #2 (Public review):

Summary:

This paper investigates the neuronal encoding of the relationship between head and body orientations in the brain. Specifically, the authors focus on the angular relationship between the head and body by employing virtual avatars. Neuronal responses were recorded electrophysiologically from two fMRI-defined areas in the superior temporal sulcus and analyzed using decoding methods. They found that: (1) anterior STS neurons encode head-body angle configurations; (2) these neurons distinguish aligned and opposite head-body configurations effectively, whereas mirror-symmetric configurations are more difficult to differentiate; and (3) an upside-down inversion diminishes the encoding of head-body angles. These findings advance our understanding of how visual perception of individuals is mediated, providing a fundamental clue as to how the primate brain processes the relationship between head and body - a process that is crucial for social communication.

Strengths:

The paper is clearly written, and the experimental design is thoughtfully constructed and detailed. The use of electrophysiological recordings from fMRI-defined areas elucidated the mechanism of head-body angle encoding at the level of local neuronal populations. Multiple experiments, control conditions, and detailed analyses thoroughly examined various factors that could affect the decoding results. The decoding methods effectively and consistently revealed the encoding of head-body angles in the anterior STS neurons. Consequently, this study offers valuable insights into the neuronal mechanisms underlying our capacity to integrate head and body cues for social cognition-a topic that is likely to captivate readers in this field.

Weaknesses:

I did not identify any major weaknesses in this paper; I only have a few minor comments and suggestions to enhance clarity and further strengthen the manuscript, as detailed in the Private Recommendations section.

Reviewer #3 (Public review):

Summary:

Zafirova et al. investigated the interaction of head and body orientation in the macaque superior temporal sulcus (STS). Combining fMRI and electrophysiology, they recorded responses of visual neurons to a monkey avatar with varying head and body orientations. They found that STS neurons integrate head and body information in a nonlinear way, showing selectivity for specific combinations of head-body orientations. Head-body configuration angles can be reliably decoded, particularly for neurons in the anterior STS. Furthermore, body inversion resulted in reduced decoding of head-body configuration angles. Compared to previous work that examined face or body alone, this study demonstrates how head and body information are integrated to compute a socially meaningful signal.

Strengths:

This work presents an elegant design of visual stimuli, with a monkey avatar of varying head and body orientations, making the analysis and interpretation straightforward. Together with several control experiments, the authors systematically investigated different aspects of head-body integration in the macaque STS. The results and analyses of the paper are mostly convincing.

Weaknesses:

(1) Using ANOVA, the authors demonstrate the existence of nonlinear interactions between head and body orientations. While this is a conventional way of identifying nonlinear interactions, it does not specify the exact type of the interaction. Although the computation of the head-body configuration angle requires some nonlinearity, it's unclear whether these interactions actually contribute. Figure 3 shows some example neurons, but a more detailed analysis is needed to reveal the diversity of the interactions. One suggestion would be to examine the relationship between the presence of an interaction and the neural encoding of the configuration angle.

(2) Figure 4 of the paper shows a better decoding of the configuration angle in the anterior STS than in the middle STS. This is an interesting result, suggesting a transformation in the neural representation between these two areas. However, some control analyses are needed to further elucidate the nature of this transformation. For example, what about the decoding of head and body orientations - dose absolute orientation information decrease along the hierarchy, accompanying the increase in configuration information?

(3) While this work has characterized the neural integration of head and body information in detail, it's unclear how the neural representation relates to the animal's perception. Behavioural experiments using the same set of stimuli could help address this question, but I agree that these additional experiments may be beyond the scope of the current paper. I think the authors should at least discuss the potential outcomes of such experiments, which can be tested in future studies.

eLife Assessment

This study presents SegPore, a valuable new method for processing direct RNA nanopore sequencing data, which improves the segmentation of raw signals into individual bases and boosts the accuracy of modified base detection. The evidence presented to benchmark SegPore is solid and the authors provide a fully documented implementation of the method. If updated to process newer RNA nanopore sequencing data types, SegPore will be of great interest to researchers studying RNA modifications.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors describe a new computational method (SegPore), which segments the raw signal from nanopore-direct RNA-Seq data to improve the identification of RNA modifications. In addition to signal segmentation, SegPore includes a Gaussian Mixture Model approach to differentiate modified and unmodified bases. SegPore uses Nanopolish to define a first segmentation, which is then refined into base and transition blocks. SegPore also includes a modification prediction model that is included in the output. The authors evaluate the segmentation in comparison to Nanopolish and Tombo, and they evaluate the impact on m6A RNA modification detection using data with known m6A sites. In comparison to existing methods, SegPore appears to improve the ability to detect m6A, suggesting that this approach could be used to improve the analysis of direct RNA-Seq data.

Strengths:

SegPore addresses an important problem (signal data segmentation). By refining the signal into transition and base blocks, noise appears to be reduced, leading to improved m6A identification at the site level as well as for single-read predictions. The authors provide a fully documented implementation, including a GPU version that reduces run time. The authors provide a detailed methods description, and the approach to refine segments appears to be new.

Weaknesses:

In addition to Nanopolish and Tombo, f5c and Uncalled4 can also be used for segmentation, however, the comparison to these methods is not shown. The overall improvement in accuracy appears to be relatively small. The run time and resources that are required to run SegPore are not shown, however, it appears that the GPU version is essential, which could limit the application of this method in practice. The method was only applied to data from the RNA002 direct RNA-Sequencing version, which is not available anymore, currently, it remains unclear if the methods still work on RNA004.

Reviewer #2 (Public review):

Summary:

The work seeks to improve the detection of RNA m6A modifications using Nanopore sequencing through improvements in raw data analysis. These improvements are said to be in the segmentation of the raw data, although the work appears to position the alignment of raw data to the reference sequence and some further processing as part of the segmentation, and result statistics are mostly shown on the 'data-assigned-to-kmer' level.

As such, the title, abstract, and introduction stating the improvement of just the 'segmentation' does not seem to match the work the manuscript actually presents, as the wording seems a bit too limited for the work involved.

The work itself shows minor improvements in m6Anet when replacing Nanopolish eventalign with this new approach, but clear improvements in the distributions of data assigned per kmer. However, these assignments were improved well enough to enable m6A calling from them directly, both at site-level and at read-level.

Strengths:

A large part of the improvements shown appear to stem from the addition of extra, non-base/kmer specific, states in the segmentation/assignment of the raw data, removing a significant portion of what can be considered technical noise for further analysis. Previous methods enforced the assignment of all raw data, forcing a technically optimal alignment that may lead to suboptimal results in downstream processing as data points could be assigned to neighbouring kmers instead, while random noise that is assigned to the correct kmer may also lead to errors in modification detection.

For an optimal alignment between the raw signal and the reference sequence, this approach may yield improvements for downstream processing using other tools.<br /> Additionally, the GMM used for calling the m6A modifications provides a useful, simple, and understandable logic to explain the reason a modification was called, as opposed to the black models that are nowadays often employed for these types of tasks.

Weaknesses:

The work seems limited in applicability largely due to the focus on the R9's 5mer models. The R9 flow cells are phased out and not available to buy anymore. Instead, the R10 flow cells with larger kmer models are the new standard, and the applicability of this tool on such data is not shown. We may expect similar behaviour from the raw sequencing data where the noise and transition states are still helpful, but the increased kmer size introduces a large amount of extra computing required to process data and without knowledge of how SegPore scales, it is difficult to tell how useful it will really be. The discussion suggests possible accuracy improvements moving to 7mers or 9mers, but no reason why this was not attempted.

The manuscript suggests the eventalign results are improved compared to Nanopolish. While this is believably shown to be true (Table 1), the effect on the use case presented, downstream differentiation between modified and unmodified status on a base/kmer, is likely limited as during actual modification calling the noisy distributions are usually 'good enough', and not skewed significantly in one direction to really affect the results too terribly.

Furthermore, looking at alternative approaches where this kind of segmentation could be applied, Nanopolish uses the main segmentation+alignment for a first alignment and follows up with a form of targeted local realignment/HMM test for modification calling (and for training too), decreasing the need for the near-perfect segmentation+alignment this work attempts to provide. Any tool applying a similar strategy probably largely negates the problems this manuscript aims to improve upon.

Finally, in the segmentation/alignment comparison to Nanopolish, the latter was not fitted(/trained) on the same data but appears to use the pre-trained model it comes with. For the sake of comparing segmentation/alignment quality directly, fitting Nanopolish on the same data used for SegPore could remove the influences of using different training datasets and focus on differences stemming from the algorithm itself.

Appraisal:

The authors have shown their method's ability to identify noise in the raw signal and remove their values from the segmentation and alignment, reducing its influences for further analyses. Figures directly comparing the values per kmer do show a visibly improved assignment of raw data per kmer. As a replacement for Nanopolish eventalign it seems to have a rather limited, but improved effect, on m6Anet results. At the single read level modification modification calling this work does appear to improve upon CHEUI.

Impact:

With the current developments for Nanopore-based modification largely focusing on Artificial Intelligence, Neural Networks, and the like, improvements made in interpretable approaches provide an important alternative that enables a deeper understanding of the data rather than providing a tool that plainly answers the question of whether a base is modified or not, without further explanation. The work presented is best viewed in the context of a workflow where one aims to get an optimal alignment between raw signal data and the reference base sequence for further processing. For example, as presented, as a possible replacement for Nanopolish eventalign. Here it might enable data exploration and downstream modification calling without the need for local realignments or other approaches that re-consider the distribution of raw data around the target motif, such as a 'local' Hidden Markov Model or Neural Networks. These possibilities are useful for a deeper understanding of the data and further tool development for modification detection works beyond m6A calling.

Reviewer #3 (Public review):

Summary:

Nucleotide modifications are important regulators of biological function, however, until recently, their study has been limited by the availability of appropriate analytical methods. Oxford Nanopore direct RNA sequencing preserves nucleotide modifications, permitting their study, however, many different nucleotide modifications lack an available base-caller to accurately identify them. Furthermore, existing tools are computationally intensive, and their results can be difficult to interpret.

Cheng et al. present SegPore, a method designed to improve the segmentation of direct RNA sequencing data and boost the accuracy of modified base detection.

Strengths:

This method is well-described and has been benchmarked against a range of publicly available base callers that have been designed to detect modified nucleotides.

Weaknesses:

However, the manuscript has a significant drawback in its current version. The most recent nanopore RNA base callers can distinguish between different ribonucleotide modifications, however, SegPore has not been benchmarked against these models.

I recommend that re-submission of the manuscript that includes benchmarking against the rna004_130bps_hac@v5.1.0 and rna004_130bps_sup@v5.1.0 dorado models, which are reported to detect m5C, m6A_DRACH, inosine_m6A and PseU.

A clear demonstration that SegPore also outperforms the newer RNA base caller models will confirm the utility of this method.

eLife Assessment

The study is a valuable contribution to the question of evolutionary shifts in neuronal proliferation patterns and the timing of developmental progressions. The authors present convincing data which confirm the presence of type-II NB lineages in beetle with the same molecular characteristics as the Drosophila counterparts but differing in lineage size and number. The data lay the foundation for future analysis of the role and molecular characteristics of individual lineages and of whether differences in the identity, proliferation pattern and timing of developmental progression can be linked to differences in the development of functionality of the central complex.

Reviewer #1 (Public review):

Summary:

Insects inhabit diverse environments and have neuroanatomical structures appropriate to each habitat. Although the molecular mechanism of insect neural development has been mainly studied in Drosophila, the beetle, Tribolium castaneum has been introduced as another model to understand the differences and similarities in the process of insect neural development. In this manuscript, the authors focused on the origin of the central complex. In Drosophila, type II neuroblasts have been known as the origin of the central complex. Then, the authors tried to identify those cells in the beetle brain. They established a Tribolium fez enhancer trap line to visualize putative type II neuroblasts and successfully identified 9 of those cells. In addition, they also examined expression patterns of several genes that are known to be expressed in the type II neuroblasts or their lineage in Drosophila. They concluded that the putative type II neuroblasts they identified were type II neuroblasts because those cells showed characteristics of type II neuroblasts in terms of genetic codes, cell diameter, and cell lineage.

Strengths:

The authors established a useful enhancer trap line to visualize type II neuroblasts in Tribolium embryos. Using this tool, they have identified that there are 9 type II neuroblasts in the brain hemisphere during embryonic development. Since the enhancer trap line also visualized the lineage of those cells, the authors found that the lineage size of the type II neuroblasts in the beetle is larger than that in the fly. They also showed that several genetic markers are also expressed in the type II neuroblasts and their lineages as observed in Drosophila.

Comments on revisions:

The revisions have improved the manuscript greatly. However, I still have some concerns about the lack of examination of the expression of NB markers. Without examining the expression of at least one unequivocal neuroblast marker, no one can say confidently that it is a neuroblast. However, it is acknowledged that such a marker is currently not available for Tribolium.

Reviewer #2 (Public review):

The authors address the question of differences in the development of the central complex (Cx), a brain structure mainly controlling spatial orientation and locomotion in insects, which can be traced back to the neuroblast lineages that produce the Cx structure. The lineages are called type-II neuroblast (NB) lineages and assumed to be conserved in insects. While Tribolium castaneum produces a functional larval Cx that only consists of one part of the adult Cx structure, the fan-shaped body, in Drosophila melanogaster a non-functional neuropile primordium is formed by neurons produced by the embryonic type-II NBs which then enter a dormant state and continue development in late larval and pupal stages.

The authors present a meticulous study demonstrating that type-II neuroblast (NB) lineages are indeed present in the developing brain of Tribolium castaneum. In contrast to type-I NB lineages, type-II NBs produce additional intermediate progenitors. The authors generate a fluorescent enhancer trap line called fez/earmuff which prominently labels the mushroom bodies but also the intermediate progenitors (INPs) of the type-II NB lineages. This is convincingly demonstrated by high resolution images that show cellular staining next to large pointed labelled cells, a marker for type-II NBs in Drosophila melanogaster. Using these and other markers (e.g. deadpan, asense), the authors show that the cell type composition and embryonic development of the type-II NB lineages are similar to their counterparts in Drosophila melanogaster. Furthermore, the expression of the Drosophila type-II NB lineage markers six3 and six4 in subsets of the Tribolium type-II NB lineages (anterior 1-4 and 1-6 type-II NB lineages) and the expression of the Cx marker skh in the distal part of most of the lineages provide further evidence that the identified NB lineages are equivalent to the Drosophila lineages that establish the central complex. However, in contrast to Drosophila, there are 9 instead of 8 embryonic type-II NB lineages per brain hemisphere and the lineages contain more progenitor cells compared to the Drosophila lineages. The authors argue that the higher number of dividing progenitor cells supports the earlier development of a functional Cx in Tribolium.

While the manuscript clearly shows that type-II NB lineages similar to Drosophila exist in Tribolium, it does not establish a direct link between the characteristics of these lineages and a functional larval Cx in Tribolium, i.e., it does not identify the cause of the heterochronic development of the Cx in these insects. However, the detailed study lays the foundation for lineage tracing and gene function experiments that will elucidate if the higher number of Tribolium type-II NB lineage progenitors, the additional lineage and the timing of developmental progression of the progenitors can indeed be linked with the earlier function of the Cx and/or if other components are required for establishing the functional larval neural circuits in Tribolium such as e.g. larval born neurons as is the case in Drosophila.

Reviewer #3 (Public review):

Summary:

In this paper, Rethemeier et al capitalize on their previous observation that the beetle central complex develops heterochronically compared to the fly and try to identify the developmental origin of this difference. For this reason, they use a fez enhancer trap line that they generated to study the neuronal stem cells (INPs) that give rise to the central complex. Using this line and staining against Drosophila type-II neuroblast markers, they elegantly dissect the number of developmental progression of the beetle type II neuroblasts. They show that the NBs, INPs, and GMCs have a conserved marker progression by comparing to Drosophila marker genes, although the expression of some of the lineage markers (otd, six3, and six4) is slightly different. Finally, they show that the beetle type II neuroblasts lineages are likely longer than the equivalent ones in Drosophila and argue that this might be the underlying reason for the observed heterochrony.

Strengths:

- Very interesting study system that compares a conserved structure that, however, develops in a heterochronic manner.<br /> - Identification of a conserved molecular signature of type-II neuroblasts between beetles and flies. At the same time, identification of transcription factors expression differences in the neuroblasts, as well as identification of an extra neuroblast.<br /> - Nice detailed experiments to describe the expression of conserved and divergent marker genes, including some lineaging looking into co-expression of progenitor (fez) and neuronal (skh) markers.

Weaknesses:

- The link between size and number of neuroblast lineages and the earlier central complex development in beetles is not examined.

Author response:

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

General Response to Public Reviews

We thank the three reviewers for their positive evaluation of our work, which presents the first molecular characterization of type-II NB lineages in an insect outside the fly Drosophila. They seem convinced of our finding of an additional type-II NB and increased proliferation during embryogenesis in the red flour beetle. The reviewers expressed hesitations on our interpretation that the observed quantitative differences of embryonic lineages can directly be linked to the embryonic development of the central complex in Tribolium. While we still believe that a connection of both observations is a valid and likely hypothesis, we acknowledge that due the lack of functional experiments and lineage tracing a causal link has not directly been shown. We have therefore changed the manuscript to an even more careful wording that on one hand describes the correlation between increased embryonic proliferation with the earlier development of the Cx but on the other hand also stresses the need for additional functional and lineage tracing experiments to test this hypothesis. We have also strengthened the discussion on alternative explanations of the increased lineage size and emphasize the less disputed elements like presence and conservation of type-II NB lineages. 

While our manuscript could in conclusion not directly show that the reason of the heterochronic shift lies in the progenitor behaviour, we still provide a first approach to answering the question of the developmental basis of this shift and testable hypotheses directly emerge from our work. We agree with reviewer#1 that functional work is best suited to test our hypothesis and we are planning to do so. However, we believe that the presented work is already rich in novel data and significantly advances our understanding on the conservation and divergence of type-II NBs in insects. We would also like to stress that most transgenic tools for which genome-wide collections exist for Drosophila have to be created for Tribolium and doing so can be quite time consuming. Conducting RNAi experiments is certainly possible in Tribolium but observing phenotypes in this defined cellular context will need laborious optimization. We have for example tried knocking down Tc-fez/erm but could not see any embryonic phenotype which might be due to an escaper effect in which only mildly affected or wild type-like embryos survive while the others die in early embryogenesis. Due to pleiotropic functions of the involved genes a cell-specific knockdown might be necessary and we are working towards establishing a system to do that in the red flour beetle. For the stated reasons, we see our work as an important basis to inspire future functional studies that build up on the framework that we introduced. 

In response to these common points, we have made the following changes to the manuscript

-        The title has been changed from ‘being associated’ to ‘correlate’

-        The conclusions part of the abstract has been changed

-        We deleted the statement ‘…thus providing the material for the early central complex formation…’

-        Rephrased to saying that the two observations just correlate

-        The part of the discussion ‘Divergent timing of type-II NB activity and heterochronic development of the central complex’ has been extensively rewritten and now discusses several alternative explanations that were suggested by the reviewers. It also stresses the need for further functional work and lineage tracing (line 859-862 (608-611)).

In addition, we have made numerous changes to the manuscript to account for more specific comments of the reviewers and to the recommendations for the authors.

Our responses to the individual comments can be found in the following. 

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Insects inhabit diverse environments and have neuroanatomical structures appropriate to each habitat. Although the molecular mechanism of insect neural development has been mainly studied in Drosophila, the beetle, Tribolium castaneum has been introduced as another model to understand the differences and similarities in the process of insect neural development. In this manuscript, the authors focused on the origin of the central complex. In Drosophila, type II neuroblasts have been known as the origin of the central complex. Then, the authors tried to identify those cells in the beetle brain. They established a Tribolium fez enhancer trap line to visualize putative type II neuroblasts and successfully identified 9 of those cells. In addition, they also examined expression patterns of several genes that are known to be expressed in the type II neuroblasts or their lineage in Drosophila. They concluded that the putative type II neuroblasts they identified were type II neuroblasts because those cells showed characteristics of type II neuroblasts in terms of genetic codes, cell diameter, and cell lineage. 

Strengths: 

The authors established a useful enhancer trap line to visualize type II neuroblasts in Tribolium embryos. Using this tool, they have identified that there are 9 type II neuroblasts in the brain hemisphere during embryonic development. Since the enhancer trap line also visualized the lineage of those cells, the authors found that the lineage size of the type II neuroblasts in the beetle is larger than that in the fly. They also showed that several genetic markers are also expressed in the type II neuroblasts and their lineages as observed in Drosophila. 

Weaknesses: 

I recommend the authors reconstruct the manuscript because several parts of the present version are not logical. For example, the author should first examine the expression of dpn, a well-known marker of neuroblast. Without examining the expression of at least one neuroblast marker, no one can say confidently that it is a neuroblast. The purpose of this study is to understand what makes neuroanatomical differences between insects which is appropriate to their habitats. To obtain clues to the question, I think, functional analyses are necessary as well as descriptive analyses. 

The expression of an exclusive type-II neuroblast marker would indeed have been the most convincing evidence. However, asense is absent from type-II NBs and deadpan is not specific enough as it is expressed in many other cells of the developing protocerebrum. The gene pointed, although also expressed elsewhere, emerged as the the most specific marker. Therefore, we start with pointed and fez/erm to describe the first appearance and developmental progression of the cells and then add further evidence that these cells are indeed type-II neuroblasts. Further evidence is provided in the following chapters.  We have discussed the need for functional work in the general response. 

Reviewer #2 (Public Review): 

The authors address the question of differences in the development of the central complex (Cx), a brain structure mainly controlling spatial orientation and locomotion in insects, which can be traced back to the neuroblast lineages that produce the Cx structure. The lineages are called type-II neuroblast (NB) lineages and are assumed to be conserved in insects. While Tribolium castaneum produces a functional larval Cx that only consists of one part of the adult Cx structure, the fan-shaped body, in Drosophila melanogaster a non-functional neuropile primordium is formed by neurons produced by the embryonic type-II NBs which then enter a dormant state and continue development in late larval and pupal stages. 

The authors present a meticulous study demonstrating that type-II neuroblast (NB) lineages are indeed present in the developing brain of Tribolium castaneum. In contrast to type-I NB lineages, type-II NBs produce additional intermediate progenitors. The authors generate a fluorescent enhancer trap line called fez/earmuff which prominently labels the mushroom bodies but also the intermediate progenitors (INPs) of the type-II NB lineages. This is convincingly demonstrated by high-resolution images that show cellular staining next to large pointed labelled cells, a marker for type-II NBs in Drosophila melanogaster. Using these and other markers (e.g. deadpan, asense), the authors show that the cell type composition and embryonic development of the type-II NB lineages are similar to their counterparts in Drosophila melanogaster. Furthermore, the expression of the Drosophila type-II NB lineage markers six3 and six4 in subsets of the Tribolium type-II NB lineages (anterior 1-4 and 1-6 type-II NB lineages) and the expression of the Cx marker skh in the distal part of most of the lineages provide further evidence that the identified NB lineages are equivalent to the Drosophila lineages that establish the central complex. However, in contrast to Drosophila, there are 9 instead of 8 embryonic type-II NB lineages per brain hemisphere and the lineages contain more progenitor cells compared to the Drosophila lineages. The authors argue that the higher number of dividing progenitor cells supports the earlier development of a functional Cx in Tribolium. 

While the manuscript clearly shows that type-II NB lineages similar to Drosophila exist in Tribolium, it does not considerably advance our understanding of the heterochronic development of the Cx in these insects. First of all, the contribution of these lineages to a functional larval Cx is not clear. For example, how do the described type-II NB lineages relate to the DM1-4 lineages that produce the columnar neurons of the Cx? What is the evidence that the embryonically produced type-II NB lineage neurons contribute to a functional larval Cx? The formation of functional circuits could rely on larval neurons (like in Drosophila) which would make a comparison of embryonic lineages less informative with respect to understanding the underlying variations of the developmental processes. Furthermore, the higher number of progenitors (and consequently neurons) in Tribolium could simply reflect the demand for a higher number of cells required to build the fan-shaped body compared to Drosophila. In addition, the larger lineages in Tribolium, including the higher number of INPs could be due to a greater number of NBs within the individual clusters, rather than a higher rate of proliferation of individual neuroblasts, as suggested. What is the evidence that there is only one NB per cluster? The presented schemes (Fig. 7/12) and description of the marker gene expression and classification of progenitor cells are inconsistent but indicate that NBs and immature INPs cannot be consistently distinguished. 

We thank this reviewer for pointing out the inconsistency in our classification of cells within the lineages as one central part of our manuscript. These were due to a confusion in the used terms (young vs. immature). We have corrected this mistake and have changed the naming of the INP subtypes to immature-I and immature-II. We are confident that based on the analysed markers, type-II NBs and immature INPs can actually be distinguished with confidence.

We agree that a functional link of increased proliferation to heterochronic CX development is not shown although we consider it to be likely. As stated in the general response we have changed the manuscript to saying that the two observations (higher number of progenitors and larger lineages/more INPs) correlate but that a causal link can only be hypothesized for the time being. At the same time, we have strengthened the discussion on alternative explanations.

We would like to remain with our statement of an increased number of embryonic progeny of Tribolium type-II NBs. We counted the total number of progenitor cells emerging from the anterior median cluster and divided this by the number of type II NBs in that cluster. Hence, the shown increased number of cells represents an average per NB but is not influenced by the increased number of NBs. On the same line, we have never seen indication for the presence of additional NBs within any cluster while one type-II NB is what we regularly found. Hence, we are confident that we know the number of respective NBs. The fact that the fly data included also neurons and was counted at a later stage indicates that the observed differences are actually minimum estimates.

We have discussed that based on the position and comparison to the grasshopper we believe that Tribolium type-II NB 1-4 contribute to the x, y, z and w tracts. To confirm this, lineage tracing experiments would be necessary, for which tools remain to be developed. 

We agree that the role of larvally born neurons and the fate of Tribolium neuroblasts through the transition from embryo to larva and pupa need to be further studied.

Available data suggests that the adult fan shaped body in Tribolium does not hugely differ in size from the Drosophila counterpart, although no data in terms of cell number is available. In the larva, however, no fan shaped body or protocerebral bridge can be distinguished in flies while in beetle larvae, these structures are clearly developed. Hence, we think that it is more likely that differences observed in the embryo reflect differences in the larval central complex. We discuss the need for further investigation of larval stages.

The main difference between Tribolium and Drosophila Cx development with regards to the larval functionality might be that Drosophila type-II NB lineage-derived neurons undergo quiescence at the end of embryogenesis so that the development of the Cx is halted, while a developmental arrest does not occur in Tribolium. However, this needs to be confirmed (as the authors rightly observe). 

Indeed, there is evidence that cells contributing to the CX go into quiescence in flies – hence, this certainly is one of the mechanisms. However, based on our data we would suggest that in addition, the balance of embryonic versus larval proliferation of type-II lineages is different between the two insects: The increased embryonic proliferation and development leads to a functional larval CX in beetles while in flies, postembryonic proliferation may be increased in order to catch up.

Reviewer #3 (Public Review):

Summary: 

In this paper, Rethemeier et al capitalize on their previous observation that the beetle central complex develops heterochronically compared to the fly and try to identify the developmental origin of this difference. For this reason, they use a fez enhancer trap line that they generated to study the neuronal stem cells (INPs) that give rise to the central complex. Using this line and staining against Drosophila type-II neuroblast markers, they elegantly dissect the number of developmental progression of the beetle type II neuroblasts. They show that the NBs, INPs, and GMCs have a conserved marker progression by comparing to Drosophila marker genes, although the expression of some of the lineage markers (otd, six3, and six4) is slightly different. Finally, they show that the beetle type II neuroblast lineages are likely longer than the equivalent ones in Drosophila and argue that this might be the underlying reason for the observed heterochrony. 

Strengths: 

- A very interesting study system that compares a conserved structure that, however, develops in a heterochronic manner. 

- Identification of a conserved molecular signature of type-II neuroblasts between beetles and flies. At the same time, identification of transcription factors expression differences in the neuroblasts, as well as identification of an extra neuroblast. 

- Nice detailed experiments to describe the expression of conserved and divergent marker genes, including some lineaging looking into the co-expression of progenitor (fez) and neuronal (skh) markers. 

Weaknesses: 

- Comparing between different species is difficult as one doesn't know what the equivalent developmental stages are. How do the authors know when to compare the sizes of the lineages between Drosophila and Tribolium? Moreover, the fact that the authors recover more INPs and GMCs could also mean that the progenitors divide more slowly and, therefore, there is an accumulation of progenitors who have not undergone their programmed number of divisions. 

We understand the difficulty of comparing stages between species, but we feel that our analysis is on the save side. At stages comparable with respect to overall embryonic development (retracting or retracted germband), the fly numbers are clearly smaller. To account for potential heterochronic shifts in NB activity, we have selected the stages to compare based on the criteria given: In Drosophila the number of INPs goes down after stage 16, meaning that they reach a peak at the selected stages. In Tribolium the chosen stages also reflect the phase when lineage size is larger than in all previous stages. Therefore, we believe that the conclusion that Tribolium has larger lineages and more INPs is well founded. Lineage size in Tribolium might further increase just before hatching (stage 15) but we were for technical reasons not able to look at this. As lineage size goes down in the last stage of Drosophila embryogenesis the number of INPs goes down and type-II NB enter quiescence, we think it is highly unlikely that the ratio between Tribolium and Drosophila INPs reverses at this stage, but a study of the behaviour of type-II NB in Tribolium and whether there is a stage of quiescence is still needed.

- The main conclusion that the earlier central complex development in beetles is due to the enhanced activity of the neuroblasts is very handwavy and is not the only possible conclusion from their data. 

As discussed in the general response we have made several changes to the manuscript to account for this criticism and discuss alternative explanations for the observations.

- The argument for conserved patterns of gene expression between Tribolium and Drosophila type-II NBs, INPs, and GMCs is a bit circular, as the authors use Drosophila markers to identify the Tribolium cells. 

We tested the hypothesis that in Tribolium there are type-II NBs with a molecular signature similar to flies. Our results are in line with that hypothesis. If pointed had not clearly marked cells with NB-morphology or fez/erm had not marked dividing cells adjacent to these NBs, we would have concluded that no such cells/lineages exist in the Tribolium embryo, or that central complex producing lineages exist but express different markers. Therefore, we regard this a valid scientific approach and hence find this argument not problematic.  

An appraisal of whether the authors achieved their aims, and whether the results support their conclusions: Based on the above, I believe that the authors, despite advancing significantly, fall short of identifying the reasons for the divergent timing of central complex development between beetle and fly. 

We agree that based on the available data, we cannot firmly make that link and we have changed the text accordingly.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

In addition to these descriptive analyses, functional analyses can be included. RNAi is highly effective in this beetle. 

We agree that functional analyses of some of the studied genes and possible effects of gene knockdowns on the studied cell lineages and on central complex development could be highly informative. However, when studying specific cell types or organs these experiments are less straight forward than it may seem as knockdowns often lead to pleiotropic effects, sterility or lethality. All the genes involved are expressed in additional cells and may have essential functions there. Given the systemic RNAi of Tribolium, it is challenging to unequivocally assign phenotypes to one of the cell groups. Overcoming these challenges is often possible but needs extensive optimization. Our study, though descriptive is already rich in data and is the first description of NB-II lineages in Tribolium central complex development. We see it as a basis for future studies on central complex development that will include functional experiments.

(1) Introduction 

For these reasons the beetle... 

Could you explain the differences in the habitats between Tribolium and Drosophila? or What is the biggest difference between these two species at the ecological aspect? 

We have added a short characterisation of the main differences.

The insect central complex is an anterior... 

The author should explain why they focus on the structure. 

Added

It is however not known how these temporal... 

If the authors want to get the answer to the question, they need to conduct functional analyses. 

While we agree with the importance of functional work (see above) we believe that detailed descriptions under the inclusion of molecular markers as presented here is very informative by itself for understanding developmental processes and sets the foundation for the analysis of mutant/RNAi- phenotypes in future studies.

CX - Central complex? 

We have opted to not use this abbreviation anymore for clarity.

“because intermediate cycling progenitors have also been...” 

Is the sentence correct? 

We have included ‘INPs’ in the sentence to make clear what the comparison refers to and added a comma

“However, molecular characterization of such lineage in another...” 

The authors should explain why molecular characterization is necessary. 

We have done so

(2) Results 

a) Figure 8. Could you delineate the skh/eGFP expression region? 

We have added brackets to figure 1 panel A to indicate the extent of skh and other gene expressions within the lineages.

b) This section should be reorganized for better logical flow. 

There certainly are different ways to organize this part and we have considered different structures of the results part. We eventually subjectively concluded that the chosen one is the best fit for our data (also see comment below on dpn-expression).

c) For the tables. The authors should mention what statistical analysis they have conducted. 

The tables themselves are just listing the raw numbers. They are the basis for the graph in figure 9. Statistical tests (t-test) are mentioned in the legend of that figure and now also in the Methods sections.

“We also found that the large Tc-pnt...” 

The authors could examine the mitotic index using an anti-pH3 antibody. 

We have used the anti-pH3 antibody to detect mitoses (figure 3C, table 1 and 3) but as data on mitoses based on this antibody is only a snapshot it would require a lot of image data to reliably determine an index in this specific cells. While mitotic activity over time possibly combined with live imaging might be very interesting in this system also with regards to the timing of development, for this basic study we are satisfied with the statement that the type-II NB are indeed dividing at these stages.

“Based on their position by the end of embryogenesis...” 

How can the authors conclude that they are neuroblasts without examining the expression of NB markers? 

Type-II NB do not express asense as the key marker for type I neuroblasts. To corroborate our argument that the cells are neuroblasts we have used several criteria:

- We have used the same markers that are used in Drosophila to label type-II NBs (pnt, dpn, six4). We are not aware of any other marker that would be more specific.

- We have shown that these cells are larger and have larger nuclei than neighbouring cells and they are dividing

- We have shown that these cells through their INP lineages give rise to central complex neuropile

We believe that these features taken together leave little doubt that the described cells are indeed neuroblasts. 

“We found that the cells they had assigned as...” 

How did the authors distinguish that they are really neuroblasts? 

We see the difficulty that we first describe the position and development of these cells (e.g. fig 3) and then add further evidence (cell size, additional marker dpn) that these are neuroblasts (also see above). However, without previous knowledge on position (and on pnt expression as the most specific marker) the type-II NB could not have been distinguished from other NBs based on cell size or expression of other markers.

“Conserved patterns of gene expression...” 

This must be the first (especially dpn). 

Dpn is not specific to type-II NB because it is also expressed in type-1 NBs, mature INPs and possibly other neural cells. It is therefore impossible to identify type-II NBs based on this gene alone. We therefore first used the most specific marker, pnt, in addition to adjacent fez expression to identify candidates for type-II lineages. Then we mapped expression of further genes on these lineages to support the interpretation (and show homology to the Drosophila lineages). Although of course the structure of a paper does not necessarily have to reflect the sequence in which experiments were done we would find putting dpn expression first misleading as it would not be clear why exactly a certain part of the expression should belong to type-II NB. Also, our pnt-fez expression data shows the position of the NB-II in the context of the whole head lobe whereas the other gene expressions are higher magnifications focussing on details. We therefore believe that the structure we chose best fits our data and the other reviewers seemed to find it acceptable as well.  

“As type-II NBs contribute to central...” 

Before the sentence, the author could explain differences in the central complex structure between Tribolium and Drosophila in terms of cell number and tissue size. 

We have added references on the comparisons of tissue sizes, but unfortunately there is no Tribolium data that can be directly compared to available Drosophila resources in terms of cell number.  

“We conclude that the embryonic development of...” 

How did the authors conclude? They must explain their logic. 

Actually, before this sentence, I only found the description of the comparison between Tribolium NBs and Drosophila once. 

We agree that this conclusion is not fully evident from the presented data. We have therefore changed this part to stating that there is a correlation with the earlier central complex development described in Tribolium. See also response to the general reviewer comments.

“Hence, we wondered...” 

The authors need to do a functional assessment of the genes they mentioned. 

We agree that the goals originally stated at the beginning of this paragraph can only be achieved with functional experiments. We have therefore rephrased this part.

(3) Discussion

“A beetle enhancer trap line...” 

This part should be moved elsewhere (it does not seem to be a discussion) 

In accordance with this comment and reviewer#2’s similar comment we have removed this section. We have added a statement on the importance of testing the expression of an enhancer trap line to the results part and an added the use of CRISPR-Cas9 for line generation to the introduction. 

“We have identified a total...” 

The authors emphasized that they discovered 9 type II NBs. The authors should clarify how important this it

We have added some discussion on the importance of this finding.

Dpn is a neural marker - Is this correct? 

According to Bier et al 1992 (now added as reference) dpn is a pan-neural marker. Reviewer#2 also recommended calling dpn a neural marker.

“Previous work described a heterochronic...” - reference? 

Reference have been added

“By contrast, we show that Tribolium...” 

What about the number of neurons in the central complex in Tribolium and Drosophila? 

Does the lineage size of type II NBs reflect the number? 

Unfortunately, we do not have numbers for that.  

Reviewer #2 (Recommendations For The Authors): 

I recommend using page and line numbers to make reviewing and revising less timeconsuming. 

We apologize for this oversight. We include a line numbering system into our resubmission.

(1) Abstract 

"These neural stem cells are believed to be conserved among insects, but their molecular characteristics and their role in brain development in other insect neurogenetics models, such as the beetle Tribolium castaneum have so far not been studied." 

I recommend explaining the importance of studying Tribolium with regard to the evolution of brain centres rather than just stating that data are lacking. 

We have now emphasized the importance of Tribolium as model for the evolution of brain centres.

"Intriguingly, we found 9 type-II neuroblast lineages in the Tribolium embryo while Drosophila produces only 8 per brain hemisphere." 

It should be made clear that the 9 lineages also refer to brain hemispheres. 

We have added this information

(2) Introduction 

I would remove the first paragraph of the introduction; the use of Tribolium as model representative for insects is too general. The authors should focus on the specific question, i.e. the introduction should start with paragraph 2. 

While we can relate to the preference for short and concise writing, we feel that giving some background on Tribolium might be important as we expect that many of our readers might be primarily Drosophila researchers. Keeping this paragraph also seems in line with a recommendation of reviewer#1 to add some additional information on Tribolium ecology.  

"Several NBs of the anterior-most part of the neuroectoderm contribute to the CX and compared…”

The abbreviation has not been introduced. 

For clarity we have now opted to not use this abbreviation but to always spell out central complex.

"Several NBs of the anterior-most part of the neuroectoderm contribute to the CX and compared to the ventral ganglia produced by the trunk segments, it is of distinctively greater complexity..." 

Puzzling statement. Why would you compare a brain center with ventral ganglia? I recommend removing this. 

We have changed this statement to just emphasizing the complexity of the brain structure.

"The dramatically increased number of neural cells that are produced by individual type-II lineages, and the fact that one lineage can produce different types of neurons..."  In my opinion, this statement is too vague and unprofessional in style. Instead of "dramatically increased" use numbers. 

We have removed ‘dramatically increased’ and now give a numeric example.

"The dramatically increased number of neural cells that are produced by individual type-II lineages, and the fact that one lineage can produce different types of neurons, leads to the generation of increased neural complexity within the anterior insect brain when compared to the ventral nerve cord.." 

I assume that this statement relates to the comparison of type I and II nb lineages. However, type I NB lineages also produce different types of neurons due to GMC temporal identity, and neuronal hemi-lineage identity. 

We have rephrased and tried to make clear that the second part of the statement is not specific to type-II NB only. In line with the comment above we have also removed the reference to the ventral nerve cord.

"In addition, in Drosophila brain tumours have been induced from type-II NBs lineages [34], opening up the possibility of modelling tumorigenesis in an invertebrate brain, thus making these lineages one of the most intriguing stem cell models in invertebrates [35,36]." 

This statement is misplaced here; it should be mentioned at the start (if at all). 

We have moved this statement up.

"However, molecular characterisation of such lineages in another insect but the fly and a thorough comparison of type-II NBs lineages and their sub-cell-types between fly and beetle are still lacking" 

The background information should include what is known about type-II NB lineages in Tribolium, including marker gene expression, e.g. Farnworth et al. 

We refer to He et al 2019, Farnworth et al 2020 and Garcia-Perez 2021. All these publications speculate about a contribution of type-II NBs to Tribolium central complex development but do not show evidence of it. As we emphasize throughout the manuscript, the present work is the first description of type-II NB in Tribolium. 

"The ETS-transcription factor pointed (pnt) marks type-II NBs [40,41], which do not express the type-I NB marker asense (ase) but the pro-neural gene deadpan (dpn)"  Deadpan is considered a pan-neural gene. To avoid confusion, I would remove "proneural" throughout.

We have done so throughout the manuscript.

"We further found that, like the type-II NBs itself, the youngest Tc-pnt-positive but fezmm-eGFP-negative INPs neither express Tc-ase (Fig. 5D, pink arrowheads)."  What is the evidence that these are the youngest pnt positive cells? Position? This needs to be explained. 

We have clarified that ‘youngest pnt-positive cells’ refers to the position of these cells close to the type-II NB.

"Therefore these neural markers can be used for a classification of type II NBs (Tc-pnt+, Tcase-), young INPs (Tc-pnt+, Tc-fez/erm-, Tc-ase-), immature INPs (Tc-pnt+, Tcfez/erm+, Tcase+), mature INPs (Tc-dpn+, Tc-ase+, Tc-fez/erm+, Tc-pros+), and GMCs (Tc-ase+, Tcfez/ erm+, Tc-pros+, Tc-dpn). This classification is summarized in Fig. 7 A-B." 

This is not the best classification and not in line with the schemes in Figure 7 - the young INPs are also immature. What is the difference? It needs to be explained what "mature" means (dividing?). 

Thank you for pointing this out. We have corrected the error in this part that confused the two original groups (young and immature). To take the immaturity of both types of INPs into account we have then also changed our naming of INP subtypes into immature-I and immature-II and throughout the manuscript). Figure 7 and figure 12 were also changed accordingly. While our classification if primarily based on gene expression the available data indicates that both types of immature INPs are not dividing, whereas mature INPs are. We have added a statement on that to this part.

"In beetles a single-unit functional central complex develops during embryogenesis while in flies the structure is postembryonic." 

This statement is vague - the authors need to explain what is meant by "single-unit". The phrase "The structure is postembryonic" also needs more explanation. The Drosophila CX neuroblasts lineages originate in the embryo and the neurons form a commissural tract that becomes incorporated into the fan-shaped body of the Cx. 

We have explained single-unit central complex and have improved our summary of known differences in central complex development between fly and beetle.

"To assess the size of the embryonic type-II NBs lineages in beetles we counted the Tc- fez/erm positive (fez-mm-eGFP) cells (INPs and GMCs) associated with a Tc-pntexpressing type-II NBs of the anterior medial group (type-II NBs lineages 1-7).  It is not clear what is meant by "with a Tc-pnt-expressing type-II NBs". Is this a typo?" 

We have removed this bit.

(3) Discussion 

I would remove the first paragraph "A beetle enhancer trap lines reflects Tc-fez/earmuff expression". This is a repetition of the methods rather than a discussion. 

This part has been removed also in line with reviewer#1’s comment.

(4) Figures 

Figure 2 

To which developing structure do the strongly labelled areas in Figure 2D correspond? 

We believe that these areas from the protocerebrum including central complex, mushroom bodies and optic lobe. We have added this to the text and to the figure legend.

Figure 7 

What do A and B represent? Different stages? 

A and B show the same lineage but map the expression of different additional markers for clarity. We have added an explanation of this. 

The classification contradicts the description in the section "Conserved patterns of gene expression mark Tribolium type-II NBs, different stages of INPs and GMCs" (last sentence) where young INPs are first in the sequence and described as pnt+, erm-, ase- and immature INPs as pnt+ erm+ and ase+. 

We have corrected this mistake and changed the names of the subtypes into immatureI and immature-II (see above).

"We conclude that the evolutionary ancient six3 territory gives rise to the neuropile of the z, y, x and w tracts." 

Please clarify if six3 is also expressed in the corresponding grasshopper NB lineages or if your conclusion is based on the comparison of Drosophila and Tribolium and you assume that this is the ancestral condition. 

Six3 expression has not been studied in grasshoppers. Owing to the highly conserved nature of an anterior median six3 domain in arthropods and bilaterian animals in general, we would expect it to be expressed anterior-medially in grasshoppers as well. In Drosophila the gene is expressed in the anterior-medial embryonic region where the type-II NBs are expected to develop, but to our knowledge it has not been specifically studied which type-II NB lineages are located within this domain. We have clarified in our text that we do not claim that the origin of anterior-medial type-II NB 1-4 and the X,Y, Z and W lineages from the six3 territory is highly conserved but only the territory itself. As far as we know our work is the first to analyse the relationship of type-II lineages and the conserved head patterning genes six3 and otd. We have added some clarification of this into this part of the discussion.

(5) Methods 

The methods section should include the methods for cell counting, as well as cell and nuclei size measurements including statistics (e.g. how many embryos, how many NB lineages). The comparison of the Tribolium NB lineage cell numbers to published Drosophila data should include a brief description of the method used in Drosophila (in addition to the method used here in Tribolium) so that the reader can understand how the data compare. 

We have added a separate section on this to the Methods part which also includes the criteria used in Drosophila. We have also included some more information to the results part on the inclusion of neurons in the Drosophila counts that may only be partially included in our numbers. This does however not change the results in terms of larger numbers of progenitor cells in Tribolium.

(6) Typos and minor errors 

Abstract 

“However, little is known on the developmental processes that create this diversity” 

Change to ... little is known about

Changed.

NBs lineages 

Change to NB lineages throughout. 

We have used text search to find and replace all position where this was used erroneously,

Results 

"Schematic drawing of expression different markers in type-II NB lineages.." 

Schematic drawing of expression of different markers 

Corrected

Discussion 

"However, the type-II NB 7, which is we assigned to the anterior medial group but which..." 

.... which we assigned.... 

corrected

"......might be the one that does not have a homologue in the fly embryo The identification of more..."  Full stop missing. 

Added.

"Adult like x, y, and w tracts as well as protocerebral bridge are...." 

Change to "The adult like x, y, and w tracts as well as the protocerebral bridge are.... 

This part has been removed with the rewriting of this paragraph.  

Reviewer #3 (Recommendations For The Authors): 

(1) Suggestions for improved or additional experiments, data, or analyses: 

a) The analysis of nuclear size is wrong. The authors compare the largest cell of a cluster of cells with a number of random cells from the same brain. It is obvious that the largest cell of a cluster will be larger than the average cell of the same brain. A better control would be to compare the largest cell of the pnt+ cluster with the largest cell of a random sample of cells, although this also comes with biases. Personally, I have no doubt that the authors are looking at neuroblasts, based on the markers they are using, so I would recommend completely eliminating Figure 4.

We agree that we produced a somewhat biased and expected result when we select the largest cell of a cluster for size comparison. However, we found it important to show based on a larger sample that these cells are also statistically larger than the average cell of a brain, which we think our assessment shows. We do not claim that type-II NBs are the largest cells of a brain, or that they are larger than type-I NBs, therefore in a random sample there might be cells that are equally big (see also distribution of the control sample shown in figure 4, and we have added a note on this to the text). We are happy to hear that this reviewer has no doubts we are looking at neural stem cells. However, reviewer#1 did express some hesitations and therefore we think it is important to keep the information on cell size as part of our argument that we are indeed looking at type-II NBs (gene expression, cell size, dividing, part of a neural lineage).

b) The comparison of NB, INP, and GMC numbers between Drosophila and Trbolium (section "The Tribolium embryonic lineages of type-II NBs are larger and contain more mature INPs than those of Drosophila") compares an experiment that the authors did with published data. I would suggest that the authors repeat the Drosophila stainings and compare themselves to avoid cases of batch effects, inconsistent counting, etc.

None of the authors is a Drosophila expert or has any experience at working with this model and reassessing the lineage size would require a number of combinatorial staining. Therefore, we feel that using the published data produced by experts and which also includes repeat experiments is for us the more reliable approach.

c) In Figure 10, there are some otd+ GFP+ cells laterally. What are these? 

We believe that these cells contribute to the eye anlagen. We have added this information to the legend.

(2) Minor corrections to the text and figures: 

a) There are some typos in the text: e.g. "pattering" in the abstract. 

We have carefully checked the text for typos and hope that we have found everything.

b) The referencing of figures in the text is inconsistent (eg "Figure 5 panel A" vs "Figure 5D" on page 12). 

We have checked throughout the manuscript and made sure to always refer to a panel correctly.

c) In Figure 3C, the white staining (anti-PH3) is not indicated in the Figure. 

The label has been added in the figure.

d) Moreover, in Figure 3, green is not very visible in the images. 

We have improved the colour intensity where possible.

e) In the figures, it might be better to outline the cells with color-coded dashed circles instead of using arrows. 

We think that this would obscure some details of the stainings and create a rather artificial representation. We also feel that doing this consistently in all our images is an amount of work not justified by the degree of expected improvement to the figures

NOTE: We are submitting a revised version of the supplementary material which only contains two minor changes: a headline was added to Table S4 (Antibodies and staining reagents) and a typo was corrected in line one of table S5 (TC to Tc).

eLife Assessment

This important study employs an optogenetics approach aimed at activating oncogene (KRASG12V) expression in a single somatic cell, with a focus on following the progression of activated cell to examine tumourigenesis probabilities under altered tissue environments. Although the description of the methodologies applied is incomplete, the authors propose a mechanism whereby reactivation of re-programming factors correlates with the increased likelihood of a mutant cell undergoing malignant transformation. This work will be of interest to developmental and cancer biologists, especially in relation to the genetic tools described.

Reviewer #2 (Public review):

Summary:

In the work by Scerbo et al, the authors aim to better understand the open question of what factors constrain cells that are genetically predisposed to form cancer (e.g. those with a potentially cancer-causing mutation like activated Ras) to only infrequently undergo this malignant transformation, with a focus on the influence of embryonic or pluripotency factors (e.g. VENTX/NANOG). Using genetically defined zebrafish models, the authors can inducibly express the KRASG12V oncogene using a combination of Cre/Lox transgenes further controlled by optogenetically inducible Cre-activated (CreER fusion that becomes active with light-induced uncaging of a tamoxifen-analogue in a targeted region of the zebrafish embryo). They further show that transient expression and activation of a pluripotency factor (e.g. Ventx fused to a GR receptor that is activated with addition of dexamethasone) must occur in the model in order for overgrowth of cells to occur. This paper describes a genetically tractable and modifiable system for studying the requirements for inducing cellular hyperplasia in a whole organism by combining overexpression of canonical genetic drivers of cancer (like Ras) with epigenetic modifiers (like specific transcription factors), which could be used to study an array of combinations and temporal relationships of these cancer drivers/modifiers.

Strengths:

The combination of Cre/lox inducible gene expression with potentially localized optogenetic induction (CreER and uncaging of tamoxifen analogues) of recombination as well as inducible activation of a transcription factor expressed via mRNA injection (GR-fusion to the TF and dex induction) offers a flexible system for manipulating cell growth, identity, and transcriptional programs. With this system, the authors establish that Ras activation and at least transient Ventx overexpression are together required to induce a hyperproliferative phenotype in zebrafish tissues.

The ability to live image embryos over the course of days with inducible fluorophores indicating recombination events and transgene overexpression offers a tractable in vivo system for studying hyperplastic cells in the context of a whole organism.

The transplant experiments demonstrate the ability of the induced hyperplastic cells to grow upon transfer to new host.

Weaknesses:

There is minimal quantitation of key aspects of the system, most critically in the efficiency of activation of the Ras-TFP fusion (Fig 1) in, purportedly, a single cell. The authors note "On average the oncogene is then activated in a single cell, identified within ~1h by the blue fluorescence of its nuclear marker) but no additional quantitative information is provided. For a system that is aimed at "a statistically relevant single-cell<br /> tracking and characterization of the early stages of tumorigenesis", such information seems essential.

The authors indicate that a single cell is "initiated" (Fig 2) using the laser optogenetic technique, but without definitive genetic lineage tracing, it is not possible to conclude that cells expressing TFP distant from the target site near the ear are daughter cells of the claimed single "initiated" cell. A plausible alternative explanation is 1) that the optogenetic targeting is more diffuse (i.e. some of the light of the appropriate wavelength hits other cells nearby due to reflection/diffraction), so these adjacent cells are additional independent "initiated" cells or 2) that the uncaged tamoxifen analogue can diffuse to nearby cells and allow for CreER activation and recombination. In Fig 2B, the claim is made that "the activated cell has divided, giving rise to two cells" - unless continuously imaged or genetically traced, this is unproven. In addition, it appears that Figures S3 and S4 are showing that hyperplasica can arise in many different tissues (including intestine, pancreas, and liver, S4C) with broad Ras + Ventx activation (while unclear from the text, it appears these embryos were broadly activated and were not "single cell activated using the set-up in Fig 1E? This should be clarified in the manuscript). In Fig S7 where single cell activation and potential metastasis is discussed, similar gut tissues have TFP+ cells that are called metastatic, but this seems consistent with the possibility that multiple independent sites of initiation are occurring even when focal activation is attempted.

Although the hyperplastic cells are transplantable (Fig 4), the use of the term "cells of origin of cancer" or metastatic cells should be viewed with care in the experiments showing TFP+ cells (Fig 1, 2, 3) in embryos with targeted activation for the reasons noted above.

Comments on latest version:

The authors have clarified and strengthened a number of important conclusions/claims.

In Figure 4, the requirement for both kRas and VentX activation for successful transplant and survival of transplanted activated cells does indeed support the need for both MAPK activation and the reprogramming factor. A limitation remains that, as in a tail vein injection in a mouse model, this may be a better measure of the ability of disbursed cells to survive in the embryo, and not "native" metastatic behavior as cells may just lodge in ectopic sites, and survive, but not exhibit complete metastatic potential. Still, these are interesting and important results about the combination effects of an oncogene and a reprogramming factor.

Further, the addition of Fig 2A and additional explanation in the text on the specificity of the light-induced activation of the Ras and/or VentX supports that transgene induction is indeed limited to one or a few cells. We agree that visual tracking of daughter cells over days is technically challenging and will be a revealing and exciting potential addition in the future.

Reviewer #3 (Public review):

Summary:

This study employs an optogenetics approach aimed at activating oncogene (KRASG12V) expression in a single somatic cell, with a focus on following the progression of activated cell to examine tumourigenesis probabilities under altered tissue environments. The research explores the role of stemness factors (VENTX/NANOG/OCT4) in facilitating oncogenic RAS (KRASG12V)-driven malignant transformations. Although the evidence provided is incomplete, the authors propose an important mechanism whereby reactivation of re-programming factors correlates with the increased likelihood of a mutant cell undergoing malignant transformation.

Strengths:

· Innovative Use of Optogenetics: The application of optogenetics for precise activation of KRAS in a single cell is valuable to the field of cancer biology, offering an opportunity to uncover insight into cellular responses to oncogenic mutations.<br /> · Important Observations: The findings concerning stemness factors' role in promoting oncogenic transformation are important, contributing data to the field of cancer biology.

Weaknesses:

Lack of Methodological Clarity: The manuscript lacks detailed descriptions of methodologies, making it difficult to fully evaluate the experimental design and reproducibility, rendering incomplete evidence to support the conclusion. Improving methodological transparency and data presentation will crucially strengthen the paper's contributions to understanding the complex processes of tumorigenesis.

Sub-optimal Data Presentation and Quality:<br /> The resolution of images through-out the manuscript are too low. Images presented in Figure 2 and Figure 4 are of very low resolution. It is very hard to distinguish individual cells and in which tissue they might reside.<br /> Lack of quantitative data and control condition data obtained from images of higher magnification limits the ability to robustly support the conclusions.

Here are some details:<br /> · Tissue specificity of the cells express KRASG12V oncogene: In this study, the ubiquitin promoter was used to drive oncogenic KRASG12V expression. Despite this, the authors claim to activate KRAS in a single brain cell based on their localized photo-activation strategy. However, upon reviewing the methods section, the description was provided that 'Localized uncaging was performed by illumination for 7 minutes on a Nikon Ti microscope equipped with a light source peaking at 405 nm, Figure 1. The size of the uncaging region was controlled by an iris that defines a circular illumination with a diameter of approximately 80 μm.' It is surprising that an epi-fluorescent microscope with an illumination diameter of around 80μm can induce activation in a single brain cell beneath skin tissue. Additionally, given that the half-life for mTFP maturation is around 60 minutes, it is likely that more cells from a variety of different lineages could be activated, but the fluorescence would not be visible until more than 1-hour post-illumination. Authors might want to provide more evidence to support their claim on the single cell KRAS activation.<br /> · Stability of cCYC: The manuscript does not provide information on the half-life and stability of cCYC. Understanding these properties is crucial for evaluating the system's reliability and the likelihood of leakiness, which could significantly influence the study's outcomes.<br /> · Metastatic Dissemination claim: Typically, metastatic cancer cells migrate to and proliferate within specific niches that are conducive to outgrowth, such as the caudal hematopoietic tissue (CHT) or liver. In Figure 3 A, an image showing the presence of mTFP expressing cells in both the head and tail regions of the larva, with additional positive dots located at the fin fold. This is interpreted as "metastasis" by the authors. However, the absence of supportive cellular compartment within the fin-fold tissue makes the presence of mTFP-positive metastatic cells there particularly puzzling. This distribution raises concerns about the spatial specificity of the optogenetic activation protocol.<br /> The unexpected locations of these signals suggest potential ectopic activation of the KRAS oncogene, which could be occurring alongside or instead of targeted activation. This issue is critical as it could affect the interpretation of whether the observed mTFP signal expansion over time is due to actual cell proliferation and infiltration, or merely a result of ectopic RAS transgene activation.<br /> · Image Resolution Concerns: The cells depicted in Figure 3C β, which appear to be near the surface of the yolk sac and not within the digestive system as suggested in the MS, underscore the necessity for higher-resolution imaging. Without clearer images, it is challenging to ascertain the exact locations and states of these cells, thus complicating the assessment of experimental results.<br /> · The cell transplantation experiment is lacking protocol details: The manuscript does not adequately describe the experimental protocols used for cell transplantation, particularly concerning the origin and selection of cells used for injection into individual larvae. This omission makes it difficult to evaluate the reliability and reproducibility of the results. Such as the source of transplanted cells:<br /> • If the cells are derived from hyperplastic growths in larvae where RAS and VX (presumably VENTX) were locally activated, the manuscript fails to mention any use of fluorescence-activated cell sorting (FACS) to enrich mTFP-positive cells. Such a method would be crucial for ensuring the specificity of the cells being studied and the validity of the results.<br /> • If the cells are obtained from whole larvae with induced RAS + VX expression, it is notable and somewhat surprising that the larvae survived up to six days post-induction (6dpi) before cells were harvested for transplantation. This survival rate and the subsequent ability to obtain single cell suspensions raise questions about the heterogeneity of the RAS + VX expressing cells that transplanted.<br /> · Unclear Experimental Conditions in Figure S3B: The images in Figure S3B lack crucial details about the experimental conditions. It is not specified whether the activation of KRAS was targeted to specific cells or involved whole-body exposure. This information is essential for interpreting the scope and implications of the results accurately.<br /> · Contrasting Data in Figure S3C compared to literatures: The graph in Figure S3C indicates that KRAS or KRAS + DEX induction did not result in any form of hyperplastic growth. This observation starkly contrasts with previous literature where oncogenic KRAS expression in zebrafish led to significant hyper-proliferation and abnormal growth, as evidenced by studies such as those published in and Neoplasia (2018), DOI: 10.1016/j.neo.2018.10.002; Molecular Cancer (2015), DOI: 10.1186/s12943-015-0288-2; Disease Models & Mechanisms (2014) DOI: 10.1242/dmm.007831. The lack of expected hyperplasia raises questions about the experimental setup or the specific conditions under which KRAS was expressed. The authors should provide detailed descriptions of the conditions under which the experiments were conducted in Figure S3B and clarifying the reasons for the discrepancies observed in Figure S3C are crucial. The authors should discuss potential reasons for the deviation from previous reports.<br /> Further comments:<br /> Throughout the study, KRAS-activated cell expansion and metastasis are two key phenotypes discussed that Ventx is promoting. However, the authors did not perform any experiments to directly show that KRAS+ cells proliferate only in Ventx-activated conditions. The authors also did not show any morphological features or time-lapse videos demonstrating that KRAS+ cells are motile, even though zebrafish is an excellent model for in vivo live imaging. This seems to be a missed opportunity for providing convincing evidence to support the authors' conclusions.<br /> There were minimal experimental details provided for the qPCR data presented in the supplementary figures S5 and S6, therefore, it is hard to evaluate results obtained.

Author response:

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

First, we thank the reviewers for a thorough reading of our paper and some useful comments. A recurrent remark of the reviewers concerns the appearance of kRas-expressing cells (labelled by a nuclear blue fluorescent marker) which we attribute to the progeny of the initially induced cell. The reviewers suggest that these cells may have been obtained through activation of the Cre-recombinase in other cells by cyclofen released from light scattering, via diffusion, leakiness, etc. These remarks are perfectly reasonable from people not familiar with the cyclofen uncaging approach that we are using, but are unwarranted as we shall show below. 

We have been using cyclofen uncaging with subsequent activation of a Cre-recombinase (or some other proteins) since 2010 (see ref.34, Sinha et al., Zebrafish 7, 199-204 (2010) and our 2018 review (ref.35, Zhang et al., ChemBioChem 19,1-8 (2018)). In our experiments, the embryos are incubated in the dark in 6µM caged cyclofen (cCyc) and washed in E3 medium (and transferred to a new medium with no cCyc). In these conditions, over many years we never observed activation of the recombinase, i.e. the appearance of the associated fluorescent label in cells of embryos grown in E3 medium. Hence leakiness can be ruled out (in presence of cCyc or in its absence).

Following transfer of the embryos to new E3 medium we illuminate the embryos locally with light at 405nm. In these conditions, cCyc is only partially uncaged and results in activation of Cre-recombinase in only a few cells (1,2, 3, …) within the illuminated region only, namely in the appearance of the kRas-associated nuclear blue fluorescent label in usually one cell (and sometimes in a few more). Data and statistics are now incorporated in the revised manuscript, see Fig.2A and S7. In absence of activation of a reprogramming factor these fluorescently labelled cells disappear within a few days (either via shut-down of their promotor, apoptosis or some other mechanism). The crucial point here is that we see less and not more kRas expressing cells (i.e. with nuclear blue fluorescence) in absence of VentX activation. This observation rules out activation of Cre-recombinase in other cells days after illumination due to leakiness, cyclofen released by light or diffusing from the illumination spot.

To observe many more fluorescent cells days after activation of the initial cell, one needs to transiently activate VentX-GR by overnight incubation in dexamethasone (DEX). Injecting the embryos at 1-cell stage with VentX-GR only or incubating them in DEX (without injection of VentX-GR) does not result in the appearance of more blue fluorescent cells.  Following activation of VentX-GR, the fluorescent cells observed a couple of days after initiation are visualized in E3 medium (i.e. in absence of cyclofen) and are localized to the vicinity of the otic vesicle (the region where the initial cell was activated). In the revised manuscript we show images of these fluorescent cells taken a few days apart in the same embryo in which a single cell was initially activated (Fig.S8). Hence, we attribute these cells to the progeny of the activated cell. Obviously, single cell tracking via time-lapse microscopy would definitely nail down this issue and provide fascinating insight into the initial stages of tumor growth. Unfortunately, immobilization of embryos in the usual medium (e.g. MS222, tricaine) over 5-6 days to track the division and motion of single cells is not possible. We are considering some other possibilities (immobilization in bungarotoxin or via photo-activation of anionic channels), but these challenging experiments are for a future paper.

Reviewer #1 (Public Review): 

The authors then performed allotransplantations of allegedly single fluorescent TICs in recipient larvae and found a large number of fluorescent cells in distant locations, claiming that these cells have all originated from the single transplanted TIC and migrated away. The number of fluorescent cells showed in the recipient larve just after two days is not compatible with a normal cell cycle length and more likely represents the progeny of more than one transplanted cell.  

As mentioned in the manuscript, we measure the density of cells/nl and inject in the yolk of 2dpf Nacre embryos a volume equivalent to about 1 cell, following published protocols (S.Nicoli and M.Presta, Nat.Prot. 2,2918 (2007)). We further image the injected cell(s) by fluorescence microscopy immediately following injection, as shown in Fig.4A and Fig.S8B. We might miss a few cells but not many. With a typical cell cycle of ~10h the images of tumors in larvae at 3dpt (and not 2dpt) correspond to  ~100 cells. In any case the purpose of this experiment was to show that the progeny of the initial induced cell is capable of developing into a tumor in a naïve fish, which is the operational definition of cancer that we adopted here. 

The ability to migrate from the injection site should be documented by time-lapse microscopy. 

As stated above our purpose here is not to study tumor formation from transplanted cell(s)  but to use that assay as an operational test of cancer. Besides as mentioned earlier single cell tracking in larvea over 3-4dpt is not a trivial task.

Then, the authors conclude that "By allowing for specific and reproducible single cell malignant transformation in vivo, their optogenetic approach opens the way for a quantitative study of the initial stages of cancer at the single cell level". However, the evidence for these claims are weak and further characterization should be performed to: 

(1) Show that they are actually activating the oncogene in a single cell (the magnification is too low and it is difficult to distinguish a single nucleus, labelling of the cell membrane may help to demonstrate that they are effectively activating the oncogene in, or transplanting, a single cell)  

In the revised manuscript we provide larger magnification of the initial induced cell and show examples of oncogene activation in more than one cell. 

(2) The expression of the genes used as markers of tumorigenesis is performed in whole larvae, with only a few transformed cells in them. Changes should be confirmed in FACS sorted fluorescent cells  

When the oncogene is activated in a whole larvae all cells are fluorescent and thus FACS  is of no use for cell sorting. Sorting could be done in larvae where single cells are activated , but then the efficiency of FACS is not good enough to isolate the few fluorescent cells among the many more non-fluorescent ones. We agree that the expression change of the genes used as markers of tumorigenesis is an underestimate of their true change, but our goal at this time is not to precisely measure the change in expression level, but to show that the pattern of change was different from the controls and corresponded to what is expected in tumorigenesis.

(3) The histology of the so called "tumor masses" is not showing malignant transformation, but at the most just hyperplasia. 

The histology of the hyperplasic tissues show cellular proliferation with a higher density of nuclear material which is characteristic of tumors, Fig.S4C. Besides the increased expression of pERK in these tissues, Fig.S4A,B is also a hallmark of cancer. 

In the brain, the sections are not perfectly symmetrical and the increase of cellularity on one side of the optic tectum is compatible with this asymmetry. 

The expected T-shape formed by the sections of the tegmentum and hypothalamus are compatible with the symmetric sections shown in Fg.2D. The asymmetry in the optic tectum is a result of the hyperplasic growth.

(4) The number of fluorescent cells found dispersed in the larvae transplanted with one single TIC after 48 hours will require a very fast cell cycle to generate over 50 cells. Do we have an idea of the cell cycle features of the transplanted TICs? 

As answered above, the transplanted larvae are shown at 3dpt. With a cell cycle of about 10h, a single cell can give rise to about 100 cells in that time lapse.  

Reviewer #2 (Public Review): 

Summary: 

This paper describes a genetically tractable and modifiable system …which could be used to study an array of combinations and temporal relationships of these cancer drivers/modifiers. 

We thank this referee for its positive comments. We would also like to point out that our approach provides for the first quantitative means to estimate the probability of tumorigenesis from a single cell, an estimate which is crucial in any assessment of cancer malignancy and the effectiveness of prophylactics. 

Weaknesses: 

There is minimal quantitation of … the efficiency of activation of the Ras-TFP fusion (Fig 1) in, purportedly, a single cell. …, such information seems essential.  

We have added more images of induction of a single (or a few cells) and a plot where the probability of RAS activation in one or a few cells is specified. 

The authors indicate that a single cell is "initiated" (Fig 2) using the laser optogenetic technique, but without definitive genetic lineage tracing, it is not possible to conclude that cells expressing TFP distant from the target site near the ear are daughter cells of the claimed single "initiated" cell. A plausible alternative explanation is 1) that the optogenetic targeting is more diffuse (i.e. some of the light of the appropriate wavelength hits other cells nearby due to reflection/diffraction), so these adjacent cells are additional independent "initiated" cells or 2) that the uncaged tamoxifen analogue can diffuse to nearby cells and allow for CreER activation and recombination.  

We have addressed this point in our general comments to the reviewers’ remarks. The possibilities mentioned by this reviewer would result in cells expressing TFP in absence of VentX activation, which is NOT the case. Cells expressing TFP away from the initial site are observed DAYS after activation of the oncogene (and TFP) in a single cell and ONLY upon activation of VentX.

In Fig 2B, the claim is made that "the activated cell has divided, giving rise to two cells" - unless continuously imaged or genetically traced, this is unproven. 

We have addressed this remark previously. Tracking of larvae over many days is not possible with the usual protocol using tricaine to immobilize the larvae. Nonetheless, in the revised version we present images of an embryo imaged at various times post activation (1hpi, 3dpi, 7dpi) where proliferation and metastasis of the cells can be observed. We are pursuing other alternatives for time-lapse microscopy over many days, since besides convincing the sceptics, a single cell tracking experiment (possibly coupled with in-situ spatial transcriptomics) will shed a new and fascinating light on the initial stages of tumor growth. 

In addition, it appears that Figures S3 and S4 are showing that hyperplasia can arise in many different tissues (including intestine, pancreas, and liver, S4C) with broad Ras + Ventx activation …. This should be clarified in the manuscript). 

This is true and has been clarified in the new version. 

In Fig S7 where single cell activation and potential metastasis is discussed, similar gut tissues have TFP+ cells that are called metastatic, but this seems consistent with the possibility that multiple independent sites of initiation are occurring even when focal activation is attempted. 

As mentioned previously this is ruled out by the fact that these cells are observed days after cyclofen uncaging (and TFP activation) and IF AND ONLY IF VentX was activated during the first dpi.

Although the hyperplastic cells are transplantable (Fig 4), the use of the term "cells of origin of cancer" or metastatic cells should be viewed with care in the experiments showing TFP+ cells (Fig 1, 2, 3) in embryos with targeted activation for the reasons noted above.  

The purpose of this transplantation experiment was to show that cell in which both kRas and VentX have been activated possess the capacity to metastasize and develop a tumor mass when transplanted in a naïve zebrafish. This -  to the best of our knowledge  - is the operational definition of a malignant tumor. Notice also that transplantation of kRAS only activated cells (i.e. without subsequent activation of VentX) does NOT yield tumors, rather the transplanted cell disappears after a few days, see Fig.S10. 

Reviewer #3 (Public Review): 

Summary: 

This study employs an optogenetics approach … to examine tumorigenesis probabilities under altered tissue environments.  

We thank this reviewer for this remark, since we believe that the probability to assess the probability of tumorigenesis from a single cell is probably the most significant contribution of this work.

Weaknesses: 

Lack of Methodological Clarity: The manuscript lacks detailed descriptions of methodologies, 

We have included additional detail of our methodology and statistical analyses in the revised manuscript.

Sub-optimal Data Presentation and Quality:  

Lack of quantitative data and control condition data obtained from images of higher magnification limits the ability to robustly support the conclusions.  

We have included more images at higher magnification and quantitative data to support the main report of targeted single cell induction. 

Here are some details:  

Authors might want to provide more evidence to support their claim on the single cell KRAS activation.  

More images and a data on activation of single or few cells in the illumination field are provided as well as statistical analysis of  cell induction.  

Stability of cCYC: The manuscript does not provide information on the half-life and stability of cCYC. Understanding these properties is crucial for evaluating the system's reliability and the likelihood of leakiness, which could significantly influence the study's outcomes. 

We have been using the cCyc system for about 14 years. We refer the reader to our previous papers and reviews on this methodology. Briefly, cCyc is stable when not illuminated with light around 375nm. Typically, we incubate our embryos in the dark for about 1h before washing, transferring them into E3 medium and illuminating them. Assessing the leakiness of the system is easy as expression of a fluorescent marker is permanently turned on. We have observed none in the conditions of our experiment or in previous works.

Metastatic Dissemination claim: However, the absence of a supportive cellular compartment within the fin-fold tissue makes the presence of mTFP-positive metastatic cells there particularly puzzling. This distribution raises concerns about the spatial specificity of the optogenetic activation protocol … The unexpected locations of these signals suggest potential ectopic activation of the KRAS oncogene, 

We have addressed this remark in the introduction and above. Specifically, metastatic and proliferative mTFP-positive cells are observed IF AND ONLY IF VentX is also activated concomitant with activation of kRAS in a single cell. No proliferative cells are observed in absence of VentX activation, or in presence of VentX or Dex alone, or if kRAS has not been activated by cyclofen uncaging. 

Image Resolution Concerns: The cells depicted in Figure 3C β, which appear to be near the surface of the yolk sac and not within the digestive system as suggested in the MS, underscore the necessity for higher-resolution imaging. Without clearer images, it is challenging to ascertain the exact locations and states of these cells, thus complicating the assessment of experimental results. 

Better images are provided in the revised version.

The cell transplantation experiment is lacking protocol details:

Details are provided. We have followed regular protocols for transplantation:  S.Nicoli and M.Presta, Nat.Prot. 2,2918 (2007). 

If the cells are obtained from whole larvae with induced RAS + VX expression, it is notable and somewhat surprising that the larvae survived up to six days post-induction (6dpi) before cells were harvested for transplantation. This survival rate and the subsequent ability to obtain single cell suspensions raise questions about the heterogeneity of the RAS + VX expressing cells that transplanted. 

From Fig.S4D, about 50% of the embryos survive at 6dpi. Though an interesting question by itself we have not (yet) addressed the important issue of the heterogeneity of the outgrowth obtained from a single cell. Our purpose here was just to show that cells in which both kRAS and VentX have been activated possess the capacity to metastasize and develop a tumor mass when transplanted in a naïve zebrafish. This -  to the best of our knowledge  - is the operational definition of a malignant tumor.

Unclear Experimental Conditions in Figure S3B: …It is not specified whether the activation of KRAS was targeted to specific cells or involved whole-body exposure. 

This was whole body (global) illumination and is specified in the revised version.

Contrasting Data in Figure S3C compared to literature: The graph in Figure S3C indicates that KRAS or KRAS + DEX induction did not result in any form of hyperplastic growth. The authors should provide detailed descriptions of the conditions under which the experiments were conducted in Figure S3B and clarifying the reasons for the discrepancies observed in Figure S3C are crucial. The authors should discuss potential reasons for the deviation from previous reports. 

This discrepancy is discussed in the revised version. First the previous reports consider the development of tumors within 3-4 weeks which we have not studied in detail. Second, the expression of the oncogene in these reports might be stronger than in ours. Third, the stochastic and random appearance of tumors in these reports suggest that some other mechanism (transient stress-induced reprogramming?) might have activated the oncogene in the initial cell. 

Further comments: 

Throughout the study, KRAS-activated cell expansion and metastasis are two key phenotypes discussed that Ventx is promoting. However, the authors did not perform any experiments to directly show that KRAS+ cells proliferate only in Ventx-activated conditions.  

Yes, we did. See Fig. S1 and compare with Fig.S3B, or Fig.S10A in comparison with Fig.2A,B.

The authors also did not show any morphological features or time-lapse videos demonstrating that KRAS+ cells are motile, even though zebrafish is an excellent model for in vivo live imaging. This seems to be a missed opportunity for providing convincing evidence to support the authors' conclusions.  

Performing time-lapse microscopy on larvae over many (4-5) days is not possible with the regular tricaine protocol for immobilization. We are definitely planning such experiments, but they will require some other protocol, perhaps using bungarotoxin or some optogenetic inhibitory channels.

There were minimal experimental details provided for the qPCR data presented in the supplementary figures S5 and S6, therefore, it is hard to evaluate result obtained. 

More details are given in the revised version.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Abstract: what is the definition of tumors that they are using? I never heard of a full-blown tumor that develops in less than 6 days from a single cell!  

This is indeed surprising! We are using an operational definition of a tumor: if cells from an hyperplasic tissue can metastasize and outgrow when transplanted in a naïve zebrafish, then it is a tumor. 

Introduction: The claim that this is the first report of the induction of oncogene expression in a single cell in zebrafish is wrong as there are other reports (PMID: 27810924, PMID: 30061297) 

These other approaches are invasive (electroporation and transplantation). We have added non-invasive in the revised version. 

Figure 2: The quality of these images is too low to visualize the infiltration that they talk about, the sections are not perfectly coronal and the asymmetric distribution of cells may be confused with an infiltration. 

We have addressed this question above. 

Results, page 5: how do we know that these are metastatic cells? there could have been spurious activation in other locations, you need to prove that these cells moved from one place to the other and that they are of the same cell type as the primary tumor  

We have addressed this question extensively in the introduction and in our answers to the reviewers. We have also added a figure showing cell proliferation in the same embryos at various time post induction. Time-lapse microscopy studies of tumor initiation and growth over many days are planned, but will be the subject of an other paper.

Figure 3: not clear why they did not use anaesthetic or mounting media to take pictures of the transplanted fish  

We tried to minimally stress the larvae that are already in a perilous condition…

Results, page 6: Not clear why the authors used KRAS v12 as an oncogene and uncaged its expression in the brain, as KRAS is not a common oncogene for brain tumors. 

There are reports of kRASG12V tumors in zebrafish brain (doi: 10.1186/s12943-015-0288-2)

It is not clear what is the mechanism of Ventx -driven oncogenesis? What changes in gene expression, cell function etc are induced by Ventx in the cells that express KRASv12? The qPCR analysis performed is done on whole larvae and an analysis on single TICs and their progeny should be done following FACS sorting of fluorescent cells.  

FACS sorting of a single TIC (and its progeny) among many thousand cells in the embryo is not possible. The analysis on whole larvae provides an underestimate of the changes in gene expression following activation of kRAS and VentX.  We are looking for spatial transcriptomics as a better approach of the changes in gene expression induced in single TICs and their progeny, but that is beyond the scope of this paper. 

Nuclear staining is necessary to make sure that only 1 cell was transplanted. How is it possible that we get more than 50 cells from a single transplanted cell in less than 48 hours? What is the length of the cell cycle of these transformed cells? 

Nuclear staining is not necessary as the transplanted cell is fluorescent. Thus we can see how many cells are transplanted. With a cell-cycle of about 10h in 3dpt, a single cell will have generated as many as 100 cells. 

Reviewer #2 (Recommendations For The Authors): 

Minor grammatical change - hyperplasic more commonly called hyperplastic. 

Reviewer #3 (Recommendations For The Authors): 

Provide Detailed Methodologies: Clearly describe all experimental protocols used, particularly those for cell transplantation and photo-activation techniques. Detailed protocols will aid in replicating your findings and enhancing the manuscript's credibility.  

Done.

Provide High-Resolution Imaging data: To substantiate the claims about cell location and behaviour, provide high-resolution images where individual cells and their specific tissue contexts are clearly visible. 

Greater magnification images provided.

Quantitative Data: Incorporate quantitative analyses to strengthen the findings, particularly in experiments where cell proliferation and activation are key outcomes. 

Done.

Verify Single Cell Activation: Offer additional evidence or experimental validation to support the claim that KRASG12V activation is confined to single cells, considering the limitations mentioned about the photo-activation setup. 

Discussion, figures and statistical analysis added in manuscript.

Discuss Stability and Leakage of cCYC: Provide data on the stability and half-life of cCYC to assess the likelihood of system leakiness, which could influence the interpretation of your results.  

Reference to our previous papers and reviews added.

Clarify Metastatic Claims: Discuss the unexpected presence of mTFP-positive cells in nontraditional metastatic sites, like the fin fold, and consider additional experiments to verify whether these are cases of ectopic activation or true metastasis.

Discussion added in manuscript

Utilize time-lapse live imaging to visually document the motility and behaviour of KRAS+ cells over time, leveraging the strengths of the zebrafish model. 

Definitely interesting, but non trivial to conduct over many days and subject for a future paper.

Address Discrepancies in KRAS Activation Effects from literature: Specifically, discuss why your findings on KRAS-induced hyperplasia differ from existing literature. Consider whether experimental conditions or KRAS expression levels might have contributed to these differences.  

Discussion added in revised version

eLife Assessment

This study makes the important finding that pleiotropy is positively associated with parallelism of evolutionary responses in gene expression. This finding, if true, runs counter to current expectations in the field. The analysis uses state-of-the art experimental evolution approach to study the genetic basis of adaptation of Drosophila simulans to a hot environment. Although the experimental results are convincing, the theoretical model is incomplete, due to several unusual assumptions. It remains to be seen whether the main conclusion can be replicated in other contexts.

Reviewer #1 (Public review):

When different groups (populations, species) are presented with similar environmental pressures, how similar are the ultimate targets (genes, pathways)? This study sought to illuminate this broader question via experimental evolution in D. simulans and quantifying gene-expression changes, specifically in the context of standing genetic variation (and not de novo mutation). Ultimately, the authors showed pleiotropy and standing-genetic variation play a significant role in the "predictability" of evolution.

The results of this manuscript look at the interplay between pleiotropy, standing genetic variation and parallelism (i.e. predictability of evolution) in gene expression. Ultimately, their results suggest that (a) pleiotropic genes typically have a smaller range in variation/expression, and (b) adaptation to similar environments tends to favor changes in pleiotropic genes, which leads to parallelism in mechanisms (though not dramatically). However, it is still uncertain how much parallelism is directly due to pleiotropy, instead of a complex interplay between them and ancestral variation.

Reviewer #2 (Public review):

Summary:

Lai and collaborators use a previously published RNAseq dataset derived from an experimental evolution set up to compare the pleiotropic properties of genes which expression evolved in response to fluctuating temperature for over 100 generations. The authors correlate gene pleiotropy with the degree of parallelisms in the experimental evolution set up to ask: are genes that evolved in multiple replicates more or less pleiotropic?

They find that, maybe counter to expectation, highly pleiotropic genes show more replicated evolution. And such effect seems to be driven by direct effects (which the authors can only speculate on) and indirect effect through low variance in pleiotropic genes (which the authors indirectly link to genetic variation underlying gene expression variance).

Weaknesses:

The results offer new insights into the evolution of gene expression and into the parameters that constrain such evolution, i.e., pleiotropy. Although the conclusions are supported by the data, I find the interpretation of the results a little bit complicated.

Major comment:

The major point I ask the authors to address is whether the connection between polygenic adaptation and parallelism can indeed be used to interpret gene expression parallelism. If the answer is not, please rephrase the introduction and discussion, if the answer is yes, please make it explicit in the text why it is so.

The authors argument: parallelism in gene expression is the same as parallelism in SNP allele frequency (AFC) (see L389-383 here they don't mention that this explanation is derived from SNP parallelism and not trait parallelism, and see Fig1 b). In previous publications the authors have explained the low level of AFC parallelism using a polygenic argument. Polygenic traits can reach a new trait optimum via multiple SNPs and therefore although the trait is parallel across replicates, the SNPs are not necessarily so.

In the current paper, they seem to be exchanging SNP AFC by gene expression, and to me, those are two levels that cannot be interchanged. Gene expression is a trait, not a SNP, and therefore the fact that a gene expression doesn't replicate cannot be explained by polygenic basis, because again the trait is gene expression itself. And, actually the results of the simulations show that high polygenicity = less trait parallelism (Fig4).

Now, if the authors focus on high parallel genes (present in e.g. 7 or more replicates) and they show that the eQTLs for those genes are many (highly polygenic) and the AFC of those eQTL are not parallel, then I would agree with the interpretation. But, given that here they just assess gene expression and not eQTL AFC, I do not think they can use the 'highly polygenic = low parallelism' explanation.

The interpretation of the results to me, should be limited to: genes with low variance and high pleiotropy tend to be more parallel, and the explanation might be synergistic pleiotropy.

Comments on revisions: The authors didn't really address any of the comments made by any of the reviewers - basically nothing was changed in the main text. Therefore, I leave my original review unchanged.

Reviewer #3 (Public review):

The authors aim to understand how gene pleiotropy affects parallel evolutionary changes among independent replicates of adaptation to a new hot environment of a set of experimental lines of Drosophila simulans using experimental evolution. The flies were RNAsequenced after more than 100 generations of lab adaptation and the changes in average gene expression were obtained relative to ancestral expression levels from reconstructed ancestral lines. Parallelism of gene expression change among lines is evaluated as variance in differential gene expression among lines relative to error variance. Similarly, the authors ask how the standing variation in gene expression estimated from a handful of flies from a reconstructed outbred line affects parallelism. The main findings are that parallelism in gene expression responses is positively associated with pleiotropy and negatively associated with expression variation. Those results are in contradiction with theoretical predictions and empirical findings. To explain those seemingly contradictory results the authors invoke the role of synergistic pleiotropy and correlated selection, although they do not attempt to measure either.

Strengths:

The study uses highly replicated outbred laboratory lines of Drosophila simulans evolved in the lab under constant hot regime for over 100 generations. This allows for robust comparisons of evolutionary responses among lines.

The manuscript is well written and the hypotheses are clearly delineated at the onset.

The authors have run a causal analysis to understand the causal dependencies between pleiotropy and expression variation on parallelism.

The use of whole-body RNA extraction to study gene expression variation is well justified.

Weaknesses:

The accuracy of the estimate of ancestral phenotypic variation in gene expression is likely low because estimated from a small sample of 20 males from a reconstructed outbred line. It might not constitute a robust estimate of the genetic variation of the evolved lines under study.

There are no estimates of the standing genetic variation of expression levels of the genes under study, only estimates of their phenotypic variation. I wished the authors had been clear about that limitation and had refrained from equating phenotypic variation in expression level with standing genetic variation.

Moreover, since the phenotype studied is gene expression, its genetic basis extends beyond expressed sequences. The phenotypic variation of a gene's expression may thus likely misrepresent the genetic variation available for its evolution. The authors do not present evidence that sequence variation correlates with expression variation.

The authors have not attempted to estimate synergistic pleiotropy among genes, nor how selection acts on gene expression modules. It makes their conclusion regarding the role of synergistic pleiotropy rather speculative.

Author response:

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

Reviewer #1 (Public review):

When different groups (populations, species) are presented with similar environmental pressures, how similar are the ultimate targets (genes, pathways)? This study sought to illuminate this broader question via experimental evolution in D. simulans and quantifying gene-expression changes, specifically in the context of standing genetic variation (and not de novo mutation). Ultimately, the authors showed pleiotropy and standing-genetic variation play a significant role in the "predictability" of evolution.

The results of this manuscript look at the interplay between pleiotropy, standing genetic variation and parallelism (i.e. predictability of evolution) in gene expression. Ultimately, their results suggest that (a) pleiotropic genes typically have a smaller range in variation/expression, and (b) adaptation to similar environments tends to favor changes in pleiotropic genes, which leads to parallelism in mechanisms (though not dramatically). However, it is still uncertain how much parallelism is directly due to pleiotropy, instead of a complex interplay between them and ancestral variation.

Yes, the reviewer is correct that our results for the direct effects of pleiotropy were not consistent for both measures of pleiotropy. We highlight this in the discussion:” Only tissue specificity had a significant direct effect, which was even larger than the indirect effect (Table 2). No significant direct effect was found for network connectivity. The discrepancy between the two measures of pleiotropy is particularly interesting given their significant correlation (Supplementary Figure 1). This suggests that both measures capture aspects of pleiotropy that differ in their biological implications.”

Reviewer #2 (Public review):

Summary:

Lai and collaborators use a previously published RNAseq dataset derived from an experimental evolution set up to compare the pleiotropic properties of genes which expression evolved in response to fluctuating temperature for over 100 generations. The authors correlate gene pleiotropy with the degree of parallelisms in the experimental evolution set up to ask: are genes that evolved in multiple replicates more or less pleiotropic?

They find that, maybe counter to expectation, highly pleiotropic genes show more replicated evolution. And such effect seems to be driven by direct effects (which the authors can only speculate on) and indirect effect through low variance in pleiotropic genes (which the authors indirectly link to genetic variation underlying gene expression variance).

Weaknesses:

The results offer new insights into the evolution of gene expression and into the parameters that constrain such evolution, i.e., pleiotropy. Although the conclusions are supported by the data, I find the interpretation of the results a little bit complicated.

We are very happy to read that the reviewer finds our conclusions to be supported by the data.

Major comment:

The major point I ask the authors to address is whether the connection between polygenic adaptation and parallelism can indeed be used to interpret gene expression parallelism. If the answer is not, please rephrase the introduction and discussion, if the answer is yes, please make it explicit in the text why it is so.

Yes, we think that gene expression parallelism can be explained by polygenic adaptation.

The authors argument: parallelism in gene expression is the same as parallelism in SNP allele frequency (AFC) (see L389-383 here they don't mention that this explanation is derived from SNP parallelism and not trait parallelism, and see Fig1 b). In previous publications the authors have explained the low level of AFC parallelism using a polygenic argument. Polygenic traits can reach a new trait optimum via multiple SNPs and therefore although the trait is parallel across replicates, the SNPs are not necessarily so.

In the current paper, they seem to be exchanging SNP AFC by gene expression, and to me, those are two levels that cannot be interchanged. Gene expression is a trait, not a SNP, and therefore the fact that a gene expression doesn't replicate cannot be explained by polygenic basis, because again the trait is gene expression itself. And, actually the results of the simulations show that high polygenicity = less trait parallelism (Fig4).

We agree with the reviewer that it is important to consider different hierarchies when talking about the implications of polygenic adaptation. The lowest hierarchical level is SNP variation and the highest level is fitness. In-between these extreme hierarchical levels is gene expression. While gene expression is a trait itself, as correctly pointed out by the reviewer, it is possible that selection is not favoring a specific trait value, because selection targets a trait on a higher hierarchical level. This implies that not only SNPs, but also intermediate traits such as gene expression can exhibit redundancy. Considering a simple example of one selected trait (e.g. body size), which is affected by the expression level of two genes A and B, each regulated by SNP A1, A2 and B1, B2. It is now possible to modulate the focal trait by allele frequency changes of A1, which in turn will only affect gene A. Alternatively, SNP B2 may change, modifying the expression of gene B, leading to the same change in body size. Hence, we could have redundancy both at the SNP level as well as on the gene expression level (although higher redundancy is expected on the SNP level). Most importantly, this redundancy at intermediate hierarchical levels is not pure theory, but it is supported by empirical evidence. We have shown that redundancy exists not only for gene expression (10.1111/mec.16274) but also for metabolite concentrations (10.1093/gbe/evad098).

Now, if the authors focus on high parallel genes (present in e.g. 7 or more replicates) and they show that the eQTLs for those genes are many (highly polygenic) and the AFC of those eQTL are not parallel, then I would agree with the interpretation. But, given that here they just assess gene expression and not eQTL AFC, I do not think they can use the 'highly polygenic = low parallelism' explanation.

This is clearly an interesting proposed research project, but we doubt that it would result in the expected outcome. Since most of the adaptive gene expression changes are not having a simple genetic basis (10.1093/gbe/evae077) and most expression variation is determined by trans-regulatory effects (10.1038/s41576-020-00304-w), eQTL mapping will most likely not identify all contributing loci. Large effect loci are more easily identified, but they are also expected to be more parallel.

The interpretation of the results to me, should be limited to: genes with low variance and high pleiotropy tend to be more parallel, and the explanation might be synergistic pleiotropy.

We thank the reviewer for the suggestion, but prefer to stick to our interpretation of the data.

Comments on revisions: The authors didn't really address any of the comments made by any of the reviewers - basically nothing was changed in the main text. Therefore, I leave my original review unchanged.

We modestly disagree, in our point to point reply, we respond to all reviewers’ comments. Since, we did not identify any major problem in our manuscript, we only modified the wording in some parts where we felt that a clarification could resolve the misunderstanding of the reviewers. In response to the reviewers’ comments, we added a new paragraph in the discussion and generated a new figure.

Reviewer #3 (Public review):

The authors aim to understand how gene pleiotropy affects parallel evolutionary changes among independent replicates of adaptation to a new hot environment of a set of experimental lines of Drosophila simulans using experimental evolution. The flies were RNAsequenced after more than 100 generations of lab adaptation and the changes in average gene expression were obtained relative to ancestral expression levels from reconstructed ancestral lines. Parallelism of gene expression change among lines is evaluated as variance in differential gene expression among lines relative to error variance. Similarly, the authors ask how the standing variation in gene expression estimated from a handful of flies from a reconstructed outbred line affects parallelism. The main findings are that parallelism in gene expression responses is positively associated with pleiotropy and negatively associated with expression variation. Those results are in contradiction with theoretical predictions and empirical findings. To explain those seemingly contradictory results the authors invoke the role of synergistic pleiotropy and correlated selection, although they do not attempt to measure either.

Strengths:

The study uses highly replicated outbred laboratory lines of Drosophila simulans evolved in the lab under constant hot regime for over 100 generations. This allows for robust comparisons of evolutionary responses among lines.

The manuscript is well written and the hypotheses are clearly delineated at the onset.

The authors have run a causal analysis to understand the causal dependencies between pleiotropy and expression variation on parallelism.

The use of whole-body RNA extraction to study gene expression variation is well justified.

Weaknesses:

The accuracy of the estimate of ancestral phenotypic variation in gene expression is likely low because estimated from a small sample of 20 males from a reconstructed outbred line. It might not constitute a robust estimate of the genetic variation of the evolved lines under study.

We agree with the reviewer that variation estimates based on 20 samples are not very precise. Nevertheless, we demonstrated that the estimated variance in gene expression was highly correlated between two independent samples from the same ancestral population. Furthermore, we identified a significant correlation of expression variance with evolutionary parallelism. In other words, the biological signal has been sufficiently strong despite the variance estimate has been noisy.

There are no estimates of the standing genetic variation of expression levels of the genes under study, only estimates of their phenotypic variation. I wished the authors had been clear about that limitation and had refrained from equating phenotypic variation in expression level with standing genetic variation.

The reviewer is right that we did not estimate genetic variation of gene expression, but use expression variation as a proxy for the standing genetic variation. There are two potential problems with this approach. First, a large expression variation could be caused by a single large effect variant segregating at intermediate frequency. Such large effect variants will exhibit a highly parallel selection response-contrary to our empirical results. Since we have shown previously (10.1093/gbe/evae077) that adaptive gene expression changes are mostly polygenic we do not consider this extreme scenario to be very relevant in our study. Rather, we would like to emphasize that neither a SNP analysis of the 5’ region nor an eQTL study will provide an unbiased estimator of genetic variation of gene expression. The second problem arises if gene expression noise differs among genes, hence more noisy genes will appear to have more standing genetic variation than genes with less noise. Since, we average across many different cells and cell types, gene expression noise is expected to be levelled out- this aspect is discussed in detail in the manuscript.

In other words, despite these two potential limitations, we consider our approach superior to alternative approaches of estimating genetic variation in gene expression.

Moreover, since the phenotype studied is gene expression, its genetic basis extends beyond expressed sequences. The phenotypic variation of a gene's expression may thus likely misrepresent the genetic variation available for its evolution. The authors do not present evidence that sequence variation correlates with expression variation.

Gene expression is determined by the joint effects of cis-regulatory and trans-regulatory variation. Hence, recombination can create more extreme phenotypes than the one of the parental lines (in quantitative genetics this is called transgressive segregation). It is unclear to what extent this constitutes a problem for our analyses. Nevertheless, we would like to point out that eQTL mapping will miss many trans-acting variants and therefore we doubt that the requested empirical evidence for correlation between genetic variation (estimated by eQTL mapping) and observed expression variation is as straight forward as suggested by the reviewer.

Nevertheless, we reference an empirical study, which showed a positive correlation between expression variation and cis-regulatory variation.

The authors have not attempted to estimate synergistic pleiotropy among genes, nor how selection acts on gene expression modules. It makes their conclusion regarding the role of synergistic pleiotropy rather speculative.

The reviewer is correct that we did not demonstrate synergistic pleiotropy, but we discuss this as a possible explanation for the observed direct effects of pleiotropy.

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

Reviewer #1 (Public review):

The results of this manuscript look at the interplay between pleiotropy, standing genetic variation, and parallelism (i.e. predictability of evolution) in gene expression. Ultimately, their results suggest that (a) pleiotropic genes typically have a smaller range in variation/expression, and (b) adaptation to similar environments tends to favor changes in pleiotropic genes, which leads to parallelism in mechanisms (though not dramatically). However, it is still uncertain how much parallelism is directly due to pleiotropy, instead of a complex interplay between them and ancestral variation.

I have a few things that I was uncertain about. It may be these things are easily answered but require more discussion or clarity in the manuscript.

(1) The variation being talked about in this manuscript is expression levels, and not SNPs within coding regions (or elsewhere). The cause of any specific gene having a change in expression can obviously be varied - transcription factors, repressors, promoter region variation, etc. Is this taken into account within the "network connectivity" measurement? I understand the network connectivity is a proxy for pleiotropy - what I'm asking is, conceptually, what can be said about how/why those highly pleiotropic genes have a change (or not) in expression. This might be a question for another project/paper, but it feels like a next step worth mentioning somewhere.

In current study, we are only able to detect significant and repeatable expression changes but unable to identify the underlying causal variants. An eQTL study in the founder population in combination with genomic resequencing for both evolved and ancestral populations would be required to address this question.

(2) The authors do have a passing statement in line 361 about cis-regulatory regions. Is the assumption that genetic variation in promoter regions is the ultimate "mechanism" driving any change in expression? In the same vein, the authors bring up a potential confounding factor, though they dismiss it based on a specific citation (lines 476-481; citation 65). I'm of the mindset that in order to more confidently disregard this "issue" based on previous evidence, it requires more than one citation. Especially since the one citation is a plant. That specific point jumps out to me as needing a more careful rebuttal.

It was not our intention to claim that the expression changes in our experiment are caused by cis-regulatory variation only. We believe that the observed expression variation has both cis- and trans-genetic components, where as some studies tend to estimate much higher cisvariation for gene expression in Drosophila populations (e.g. [1, 2]). We mentioned the positive correlation between cis-regulatory polymorphism and expression variation to (1) highlight the genetic control of gene expression and (2) make the connection between polygenic adaptation and gene expression evolutionary parallelism.

(3) I feel like there isn't enough exploration of tissue specificity versus network connectivity. Tissue specificity was best explained by a model in which pleiotropy had both direct and indirect effects on parallelism; while network connectivity was best explained (by a small margin) via the model which was mostly pleiotropy having a direct effect on ancestral variation, that then had a direct effect on parallelism. When the strengths of either direct/indirect effects were quantified, tissue specificity showed a stronger direct effect, while network connectivity had none (i.e. not significant). My confusion is with the last point - if network connectivity is explained by a direct effect in the best-supported model, how does this work, since the direct effect isn't significant? Perhaps I am misunderstanding something.

To clarify, for network connectivity, there’s a significant “indirect” effect on parallelism (i.e. network connectivity affect ancestral gene expression and ancestral gene expression affect parallelism). Hence, in table 2, the direct effect of network connectivity on parallelism is weak and not significant while the indirect effect via ancestral variation is significant.

Also, network connectivity might favor the most pleiotropic genes being transcription factor hubs (or master regulators for various homeostasis pathways); while the tissue specificity metric perhaps is a kind of a space/time element. I get that a gene having expression across multiple tissues does fit the definition of pleiotropy in the broad sense, but I'm wondering if some important details are getting lost - I'm just thinking about the relative importance of what tissue specificity measurements say versus the network connectivity measurement.

We examined the statistical relationship between the two measures and found a moderate positive correlation on the basis of which we argued that the two measures may capture different aspects of pleiotropy. We appreciate the reviewer’s suggestions about the biological basis of the two estimates of pleiotropy, but we think that without further experimental insights, an extended discussion of this topic is too premature to provide meaningful insights to the readership.

Reviewer #2 (Public review):

Summary:

Lai and collaborators use a previously published RNAseq dataset derived from an experimental evolution set up to compare the pleiotropic properties of genes whose expression evolved in response to fluctuating temperature for over 100 generations. The authors correlate gene pleiotropy with the degree of parallelisms in the experimental evolution set up to ask: are genes that evolved in multiple replicates more or less pleiotropic?

They find that, maybe counter to expectation, highly pleiotropic genes show more replicated evolution. Such an effect seems to be driven by direct effects (which the authors can only speculate on) and indirect effects through low variance in pleiotropic genes (which the authors indirectly link to genetic variation underlying gene expression variance).

Weaknesses:

The results offer new insights into the evolution of gene expression and into the parameters that constrain such evolution, i.e., pleiotropy. Although the conclusions are supported by the data, I find the interpretation of the results a little bit complicated.

Major comment:

The major point I ask the authors to address is whether the connection between polygenic adaptation and parallelism can indeed be used to interpret gene expression parallelism. If the answer is not, please rephrase the introduction and discussion, if the answer is yes, please make it explicit in the text why it is so.

Our answer is yes, we interpreted gene expression parallelism (high ancestral variance -> less parallelism) using the same framework that links polygenic adaptation and parallelism (high polygenicity = less trait parallelism). We believe that our response covers several of the reviewer’s concerns.

The authors' argument: parallelism in gene expression is the same as parallelism in SNP allele frequency (AFC) (see L389-383 here they don't mention that this explanation is derived from SNP parallelism and not trait parallelism, and see Figure 1 b). In previous publications, the authors have explained the low level of AFC parallelism using a polygenic argument. Polygenic traits can reach a new trait optimum via multiple SNPs and therefore although the trait is parallel across replicates, the SNPs are not necessarily so.

Importantly, our rationale is based on the idea that gene expression is rarely the direct target of selection, but rather an intermediate trait [3]. Recently, we have specifically tested this assumption for gene expression and metabolite concentrations and our analysis showed that both traits were are redundant [4], as previously shown for DNA sequences [5]. The important implication for this manuscript is that gene expression is also redundant, so that adaptation can be achieved by distinct changes in gene expression in replicate populations adapting to the same selection pressure. This implies that we can use the same simulation framework for gene expression as for sequencing data. In our case different SNP frequencies correspond to different expression levels (averaged across individuals from a population), which in turn increases fitness by modifying the selected trait. Importantly, the selected trait in our simulations is not gene expression, but a not defined high level phenotype. A key insight from our simulations is that with increasing polygenicity the expression of a gene is more variable in the ancestral population.

In the current paper, they seem to be exchanging SNP AFC by gene expression, and to me, those are two levels that cannot be interchanged. Gene expression is a trait, not an SNP, and therefore the fact that a gene expression doesn't replicate cannot be explained by a polygenic basis, because again the trait is gene expression itself. And, actually, the results of the simulations show that high polygenicity = less trait parallelism (Figure 4).

As detailed above, because adaptation can be reached by changes in gene expression at different sets of genes, redundancy is also operating on the expression level not just on the level of SNPs. To clarify, the x-axis of Fig. 4 is the expression variation in the ancestral population.

Now, if the authors focus on high parallel genes (present in e.g. 7 or more replicates) and they show that the eQTLs for those genes are many (highly polygenic) and the AFC of those eQTLs are not parallel, then I would agree with the interpretation. But, given that here they just assess gene expression and not eQTL AFC, I do not think they can use the 'highly polygenic = low parallelism' explanation.

The interpretation of the results to me, should be limited to: genes with low variance and high pleiotropy tend to be more parallel, and the explanation might be synergistic pleiotropy.

While we understand the desire to model the full hierarchy from eQTLs to gene expression and adaptive traits, we raise caution that this would be a very challenging task. eQTLs very often underestimate the contribution of trans-acting factors, hence the understanding of gene expression evolution based on eQTLs is very likely incomplete and cannot explain the redundancy of gene expression during adaptation. Hence, we think that the focus on redundant gene expression is conceptually simpler and thus allows us to address the question of pleiotropy without the incorporation of allele frequency changes.  

Reviewer #3 (Public review):

The authors aim to understand how gene pleiotropy affects parallel evolutionary changes among independent replicates of adaptation to a new hot environment of a set of experimental lines of Drosophila simulans using experimental evolution. The flies were RNAsequenced after more than 100 generations of lab adaptation and the changes in average gene expression were obtained relative to ancestral expression levels from reconstructed ancestral lines. Parallelism of gene expression change among lines is evaluated as variance in differential gene expression among lines relative to error variance. Similarly, the authors ask how the standing variation in gene expression estimated from a handful of flies from a reconstructed outbred line affects parallelism. The main findings are that parallelism in gene expression responses is positively associated with pleiotropy and negatively associated with expression variation. Those results are in contradiction with theoretical predictions and empirical findings. To explain those seemingly contradictory results the authors invoke the role of synergistic pleiotropy and correlated selection, although they do not attempt to measure either.

Strengths:

(1) The study uses highly replicated outbred laboratory lines of Drosophila simulans evolved in the lab under a constant hot regime for over 100 generations. This allows for robust comparisons of evolutionary responses among lines.

(2) The manuscript is well written and the hypotheses are clearly delineated at the onset.

(3) The authors have run a causal analysis to understand the causal dependencies between pleiotropy and expression variation on parallelism.

(4) The use of whole-body RNA extraction to study gene expression variation is well justified.

Weaknesses:

(1) It is unclear how well phenotypic variation in gene expression of the evolved lines has been estimated by the sample of 20 males from a reconstructed outbred line not directly linked to the evolved lines under study. I see this as a general weakness of the experimental design.

Our intention was not to measure the phenotypic variance of the evolved lines, but rather to estimate the phenotypic variance at the beginning of the experiment. Hence, we measured and investigated the variation of gene expression in the ancestral population since this was the beginning of the replicated experimental evolution. Furthermore, since the ancestral population represents the natural population in Florida, the gene expression variation reflects the history of selection history acting on it.

(2) There are no estimates of standing genetic variation of expression levels of the genes under study, only phenotypic variation. I wished the authors had been clear about that limitation and had discussed the consequences of the analysis. This also constitutes a weakness of the study.

The reviewer is correct that we do not aim to estimate the standing genetic variation, which is responsible for differences in gene expression. While we agree that it could be an interesting research question to use eQTL mapping to identify the genetic basis of gene expression, we caution that trans-effects are difficult to estimate and therefore an important component of gene expression evolution will be difficult to estimate. Hence, we consider that our focus on variation in gene expression without explicit information about the genetic basis is simpler and sufficient to address the question about the role of pleiotropy.

(3) Moreover, since the phenotype studied is gene expression, its genetic basis extends beyond expressed sequences. The phenotypic variation of a gene's expression may thus likely misrepresent the genetic variation available for its evolution. The genetic variation of gene expression phenotypes could be estimated from a cross or pedigree information but since individuals were pool-sequenced (by batches of 50 males), this type of analysis is not possible in this study.

We agree with the reviewer that gene expression variation may also have a non-genetic basis, we discuss this in depth in the discussion of the manuscript.  

(4) The authors have not attempted to estimate synergistic pleiotropy among genes, nor how selection acts on gene expression modules. It makes any conclusion regarding the role of synergistic pleiotropy highly speculative.

We mentioned synergistic pleiotropy as a possible explanation for our results. A positive correlation between the fitness effect of gene expression variation would predict more replicable evolutionary changes. A similar argument has been made by [6]. 

I don't understand the reason why the analysis would be restricted to significantly differentially expressed genes only. It is then unclear whether pleiotropy, parallelism, and expression variation do play a role in adaptation because the two groups of adaptive and non-adaptive genes have not been compared. I recommend performing those comparisons to help us better understand how "adaptive" genes differentially contribute to adaptation relative to "nonadaptive" genes relative to their difference in population and genetic properties.

We agree with the reviewer that the comparison between the pleiotropy of adaptive and nonadaptive genes is interesting. We performed the analysis but omitted from the current manuscript for simplicity. Similar to the results in [6], non-adaptive genes are more pleiotropic than the adaptive genes. For adaptive genes we find a positive correlation between the level of pleiotropy and evolutionary parallelism. Thus, high pleiotropy limits the evolvability of a gene, but moderate and potentially synergistic pleiotropy increases the repeatability of adaptive evolution. We included this result in the revised manuscript and discuss it.

There is a lack of theoretical groundings on the role of so-called synergistic pleiotropy for parallel genetic evolution. The Discussion does not address this particular prediction. It could be removed from the Introduction.

We modestly disagree with the reviewer, synergistic pleiotropy is covered by theory and empirical results also support the importance of synergistic pleiotropy. 

References

(1) Genissel A, McIntyre LM, Wayne ML, Nuzhdin SV. Cis and trans regulatory effects contribute to natural variation in transcriptome of Drosophila melanogaster. Molecular biology and evolution. 2008;25(1):101-10. Epub 20071112. doi: 10.1093/molbev/msm247. PubMed PMID: 17998255.

(2) Osada N, Miyagi R, Takahashi A. Cis- and Trans-regulatory Effects on Gene Expression in a Natural Population of Drosophila melanogaster. Genetics. 2017;206(4):2139-48. Epub 20170614. doi: 10.1534/genetics.117.201459. PubMed PMID: 28615283; PubMed Central PMCID: PMCPMC5560811.

(3) Barghi N, Hermisson J, Schlötterer C. Polygenic adaptation: a unifying framework to understand positive selection. Nature reviews Genetics. 2020;21(12):769-81. Epub 2020/07/01. doi: 10.1038/s41576-020-0250-z. PubMed PMID: 32601318.

(4) Lai WY, Otte KA, Schlötterer C. Evolution of Metabolome and Transcriptome Supports a Hierarchical Organization of Adaptive Traits. Genome biology and evolution. 2023;15(6). Epub 2023/05/26. doi: 10.1093/gbe/evad098. PubMed PMID: 37232360; PubMed Central PMCID: PMCPMC10246829.

(5) Barghi N, Tobler R, Nolte V, Jaksic AM, Mallard F, Otte KA, et al. Genetic redundancy fuels polygenic adaptation in Drosophila. PLoS biology. 2019;17(2):e3000128. Epub 2019/02/05. doi: 10.1371/journal.pbio.3000128. PubMed PMID: 30716062.

(6) Rennison DJ, Peichel CL. Pleiotropy facilitates parallel adaptation in sticklebacks. Molecular ecology. 2022;31(5):1476-86. Epub 2022/01/09. doi: 10.1111/mec.16335. PubMed PMID: 34997980; PubMed Central PMCID: PMCPMC9306781.

eLife Assessment

This study provides important findings that during credit assignment, the lateral orbitofrontal cortex (lOFC) and hippocampus (HC) encode causal choice representations, while the frontopolar cortex (FPl) mediates HC -lOFC interactions when the causality needs to be maintained over longer distractions. This research offers compelling evidence and employs sophisticated multivariate pattern analysis. However, while the task design captures the delayed component, it lacks the full complexity and ambiguity of the credit assignment process observed in real-world scenarios. Moreover, the data indicated that other frontal regions beyond just lOFC were involved in delayed credit assignment. This work will be of interest to cognitive and computational neuroscientists who work on value-based decision-making and fronto-hippocampal circuits.

Reviewer #1 (Public review):

Summary

The authors conducted a study on one of the fundamental research topics in neuroscience: neural mechanisms of credit assignment. Building on the original studies of Walton and his colleagues and subsequent studies on the same topic, the authors extended the research into the delayed credit assignment problem with clever task design, which compared the non-delayed (direct) and delayed (indirect) credit assignment processes. Their primary goal was to elucidate the neural basis of these processes in humans, advancing our understanding beyond previous studies.

Major Strengths and Considerations

Strengths:

(1) Innovative task design distinguishing between direct and indirect credit assignment.<br /> (2) Use of sophisticated multivariate pattern analysis to identify neural correlates of pending representations.<br /> (3) Well-executed study with clear presentation of results.<br /> (4) Extension of previous research to human subjects, providing valuable comparative insights.

Considerations for Future Research:

(1) The task design, while clear and effective, might be further developed to capture more real-world complexity in credit assignment.<br /> (2) There's potential for deeper exploration of the role of task structure understanding in credit assignment processes.<br /> (3) The interpretation of lateral orbitofrontal cortex (lOFC) involvement could be expanded to consider its role in both credit assignment and task structure representation.

Achievement of Aims and Support of Conclusions

The authors successfully achieved their aim of investigating direct and indirect credit assignment processes in humans. Their results provide valuable insights into the neural representations involved in these processes. The study's conclusions are generally well-supported by the data, particularly in identifying neural correlates of pending representations crucial for delayed credit assignment.

Impact on the Field and Utility of Methods

This study makes a significant contribution to the field of credit assignment research by bridging animal and human studies. The methods, particularly the multivariate pattern analysis approach, provide a robust template for future investigations in this area. The data generated offers valuable insights for researchers comparing human and animal models of credit assignment, as well as those studying the neural basis of decision-making and learning.

The study's focus on the lOFC and its role in credit assignment adds to our understanding of this brain region's function

Additional Context and Future Directions

(1) Temporal ambiguity in credit assignment: While the current design provides clear task conditions, future studies could explore more ambiguous scenarios to further reflect real-world complexity.

(2) Role of task structure understanding: The difference in task comprehension between human subjects in this study and animal subjects in previous studies offers an interesting point of comparison.

(3) The authors used a sophisticated method of multivariate pattern analysis to find the neural correlate of the pending representation of the previous choice, which will be used for credit assignment process in the later trials. The authors tend to use expressions that these representations are maintained throughout this intervening period. However the analysis period is specifically at the feedback period, which is irrelevant for the credit assignment of the immediately preceding choice. This task period can interfere with the interference of ongoing credit assignment process. Thus, rather than the passive process of maintaining the information of the previous choice, the activity of this specific period can mean the active process of protecting the information from interfering and irrelevant information. It would be great if the authors could comment on this important interpretational issue.

(4) Broader neural involvement: While the focus on specific regions of interest (ROIs) provided clear results, future studies could benefit from a whole-brain analysis approach to provide a more comprehensive understanding of the neural networks involved in credit assignment.

Comments after the revision:

The authors have adequately addressed the majority of concerns raised in my previous review. The manuscript has demonstrably improved as a result of these revisions and represents a valuable contribution to the literature on credit assignment.

However, some limitations persist that, while not readily resolvable within the scope of the current study, warrant attention. Specifically, the investigation focuses primarily on the temporal dimension of credit assignment. In real-world scenarios, the complexity of credit assignment extends beyond temporal distance to encompass the inherent ambiguity of causal attribution arising from the presence of multiple potential causal events. Resolving this ambiguity necessitates a form of structural understanding of the environment, a capacity presumably possessed by humans and animals. While the experimental design of this study provides explicit cues regarding the structure of the environment, deciphering such structure in natural settings is a crucial component of the credit assignment process.<br /> Future research should prioritize the investigation of credit assignment within more ecologically valid contexts, focusing on the role of structural understanding in navigating the causal ambiguity inherent in real-world environments. Addressing this aspect will be crucial for developing a more complete and nuanced understanding of credit assignment mechanisms.

In addition, the newly added whole-brain searchlight decoding analysis provides an important nuance regarding the neural substrates of credit assignment (Figure S7). The results reveal not only activity in the lateral orbitofrontal cortex (lOFC), but also, and more robustly, in the medial orbitofrontal cortex/ventromedial prefrontal cortex (mOFC/vmPFC) specifically during the "indirect transition condition" and not the "direct transition condition." This finding suggests a potentially more significant role for mOFC/vmPFC in processing complex, non-immediate credit assignment scenarios. This nuance should be explicitly noted to appreciate the complexity of the neural mechanisms at play.

Reviewer #2 (Public review):

Summary:

The present manuscript addresses a longstanding challenge in neuroscience: how the brain assigns credit for delayed outcomes, especially in real-world learning scenarios where decisions and outcomes are separated by time. The authors focus on the lateral orbitofrontal cortex and hippocampus, key regions involved in contingent learning. By integrating fMRI data and behavioral tasks, the authors examined how neural circuits maintain a causal link between past decisions and delayed outcomes. Their findings offer insights into mechanisms that could have critical implications for understanding human decision-making.

Strengths:

- The experimental designs were extremely well thought-out. The authors successfully coupled behavioral data and neural measures (through fMRI) to explore the neural mechanisms of contingent learning. This integration adds robustness to the findings and strengthens their relevance.<br /> - The emphasis on the interaction between the lateral orbitofrontal cortex (lOFC) and hippocampus (HC) in this study is very well-targeted. The reported findings regarding their dynamic interactions provide valuable insights into contingent learning in humans.<br /> - The use of advanced modeling framework and analytical techniques allowed the authors to uncover new mechanistic insights regarding a complex case of decision-making process. The methods developed will also benefit analyses of future neuroimaging data on a range of decision-making tasks as well.

Weaknesses:

- Given the limited temporal resolution of fMRI and that the measured signal is an indirect measure of neural activity, it is unclear the extent to which the reported causality reflects the true relationship/interactions between neurons in different regions. That said, I believe this concern is minimized by a series of well-thought-out and robust analyses which consistently point to compelling results.

Comments on revisions:

Thank you for your thorough point-by-point responses to my comments and questions. After carefully reviewing the responses and additional analyses/results provided, I do not have further comments. Importantly, I believe the authors have done a great job addressing inevitable limitations that are inherent to fMRI signals. The thoughtful analyses used in the study combined with the timely questions the manuscript is able to address make the study an important contribution to the field.

Reviewer #3 (Public review):

The authors apply multivoxel decoding analyses from fMRI during reward feedback about the cues previously chosen that led to that feedback. They compare two versions of the task - one in which the feedback is provided about the current trial, and one in which the feedback is provided about the previous trial. Reward probability changes slowly over time, so subjects need to identify which cues are leading to reward at a given time. They find that evidence for recall of the cue in lateral orbitofrontal cortex (lOFC) and hippocampus (HC). They also find that in the second condition, where feedback is for the one-back trial, this representation is mediated by the lateral frontal pole (FPl).

Overall, the analyses are clean and elegant and seem to be complete. I have only a few comments, all of which can be public.

(1) They do find (not surprisingly) that the one-back task is harder. It would be good to ensure that the reason that they had more trouble detecting direct HC & lOFC effects on the harder task was not because the task is harder and thus that there are more learning failures on the harder one-back task. (I suspect their explanation that it is mediated by FPl is likely to be correct. But it would be nice to do some subsampling of the zero-back task [matched to the success rate of the one-back task] to ensure that they still see the direct HC and lOFC there.)

(2) The evidence that they present in the main text (Figure 3) that the HC and lOFC are mediated by FPl is a correlation. I found the evidence presented in Supplemental Figure 7 to be much more convincing. As I understand it, what they are showing in SF7 is that when FPl decodes the cue, then (and only then) HC and lOFC decode the cue. If my understanding is correct, then this is a much cleaner explanation for what is going on than the secondary correlation analysis. If my understanding here is incorrect, then they should provide a better explanation of what is going on so as to not confuse the reader.

(3) I like the idea of "credit spreading" across trials (Figure 1E). I think that credit spreading in each direction (into the past [lower left] and into the future [upper right]) is not equivalent. This can be seen in Figure 1D, where the two tasks show credit spreading differently. I think a lot more could be studied here. Does credit spreading in each of these directions decode in interesting ways in different places in the brain?

Comments on revisions:

After revision, I have no additional comments.

Author response:

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

Reviewer 1:

Point 1 of public reviews and point 2 of recommendations to authors. 

Temporal ambiguity in credit assignment: While the current design provides clear task conditions, future studies could explore more ambiguous scenarios to further reflect real-world complexity…. The role of ambiguity is very important for the credit assignment process. However, in the current task design, the instruction of the task design almost eliminates the ambiguity of which the trial's choice should be assigned credit to. The authors claim the realworld complexity of credit assignment in this task design. However, the real-world complexity of this type of temporal credit assignment involves this type of temporal ambiguity of responsibility as causal events. I am curious about the consequence of increasing the complexity of the credit assignment process, which is closer to the complexity in the real world.

We agree that the structure of causal relationships can be more ambiguous in real-world contexts. However, we also believe that there are multiple ways in which a task might approach “real-world complexity”. One way is by increasing the ambiguity in the relationships between choices and outcomes (as done by Jocham et al., 2016). Another is by adding interim decisions that must be completed between viewing the outcome of a first choice, which mimics task structures such as the cooking tasks described in the introduction. In such tasks, the temporal structure of the actions maybe irrelevant, but the relationship between choice identities and the actions is critical to be effective in the task (e.g., it doesn’t matter whether I add spice before or after the salt, all I need to know that adding spice will result in spicy soup).  While ambiguity about either form of causal relation is clearly an important part of real-world complexity, and would make credit assignment harder, our study focuses on how links between outcomes and specific past choice identities are created at the neural level when they are known to be causal. 

We consequently felt it necessary to resolve temporal ambiguity for participants. Instructing participants on the structure of the task allowed us to make assumptions about how credit assignment for choice identities should proceed (assign credit to the choice made N trials back) and allowed us make positive predictions about the content of representations in OFC when viewing an outcome. This gave the highest power to detect multivariate information about the causal choice and the highest interpretability of such findings. 

In contrast, if we had not resolved this ambiguity, it would be difficult to tell if incorrect decoding from the classifier resulted from noise in the neural signal, or if on that trial participants were assigning credit to non-causal choices that they erroneously believed to have caused the outcome due to the perceived temporal structure. We believe this would have ultimately decreased our power to determine whether representations of the causal choice were present at the time of outcome because we would have to make assumptions about what counts as a “true” causal representation. 

We have commented on this in the discussions (p.13): 

“While our study was designed to focus on the complexity of assigning credit in tasks with different known causal structures, another important component of real-world credit assignment is temporal ambiguity. To isolate the mechanisms which create associations between specific choices and specific outcomes, we instructed participants on the causal structure of each task, removing temporal ambiguity about the causal choice.  However, our results are largely congruent with previously reported results in tasks that dissolved the typical experimental trial structure, producing temporal ambiguity, and which observed more pronounced spreading of effect, in addition to appropriate credit assignment (Jocham et al, 2016).  Namely, this study found that activation in the lOFC increased only when participants received rewards contingent on a previous action, an effect that was more pronounced in subjects whose behavior reflected more accurate credit assignment. This suggests a shared lOFC mechanism for credit assignment in different types of complex environments. Whether these mechanisms extend to situations where the temporal causal structure is completely unknown remains an important question.”

Point 2 of public reviews and point 1 of recommendations to authors

Role of task structure understanding: The difference in task comprehension between human subjects in this study and animal subjects in previous studies offers an interesting point of comparison…. The credit assignment involves the resolution of the ambiguity in which the causal responsibility of an outcome event is assigned to one of the preceding events. In the original study of Walton and his colleagues, the monkey subjects could not be instructed on the task structure defining the causal relationships of the events. Then, the authors of the original study observed the spreading of the credit assignments to the "irrelevant" events, which did not occur in the same trial of the outcome event but to the events (choices) in neighbouring trials. This aberrant pattern of the credit assignment can be due to the malfunctions of the credit assignment per se or the general confusion of the task structure on the part of the monkey subjects. In the current study design, the subjects are humans and they are not confused about the task structure. Consistently, it is well known that human subjects rarely show the same patterns of the "spreading of credit assignment". So the implicit mechanism of the credit assignment process involves the understanding of the task structure. In the current study, there are clearly demarked task conditions that almost resolve the ambiguity inherent in the credit assignment process. Yet, the focus of the current analysis stops short of elucidating the role of understanding the task structure. It would be great if the authors could comment on the general difference in the process between the conditions, whether it is behavioral or neural.

We would like to thank the reviewer for making this important point. We believe that understanding the structure of the credit-assignment problem above is quite important, at least for the type of credit assignment described here. That is, because participants know that the outcome viewed is caused by the choice they made, 0 or 1 trials into the past, they can flexibly link choice identities to the newly observed outcomes as the probabilities change. Note, however, that this is already very challenging in the 1-back condition because participants need to track the two independently changing probabilities. We believe this is critical to address the questions we aimed to answer with this experiment, as described above. 

We agree that this might be quite different from previous studies done with non-human primates, which also included many more training trials and lesions to the lOFC. Both of these aspects could manifest as difference in task performance and processing at behavioural and neural levels, respectively. Consistent with this possibility, in our task, we found no differences in credit spreading between conditions, suggesting that humans were quite precise in both, despite causal relationships being harder to track in the “indirect transition condition”. This lack of credit spreading could be because humans better understood the task-structure compared to macaques or be due to differences in functioning of the OFC and other regions. Because all participants were trained to understand, and were cued with explicit knowledge of, the task structure, it is difficult to isolate its role as we would need another condition in which they were not instructed about the task structure. This would also be an interesting study, and we leave it to future research to parse the contributions of task-structure ambiguity to credit assignment. 

Point 3 of public reviews. 

The authors used a sophisticated method of multivariate pattern analysis to find the neural correlate of the pending representation of the previous choice, which will be used for the credit assignment process in the later trials. The authors tend to use expressions that these representations are maintained throughout this intervening period. However, the analysis period is specifically at the feedback period, which is irrelevant to the credit assignment of the immediately preceding choice. This task period can interfere with the ongoing credit assignment process. Thus, rather than the passive process of maintaining the information of the previous choice, the activity of this specific period can mean the active process of protecting the information from interfering and irrelevant information. It would be great if the authors could comment on this important interpretational issue.

We agree that lFPC is likely actively protecting the pending choice representation from interference with the most recent choice for future credit assignment. This interpretation is largely congruent with the idea of “prospective memory” (e.g., Burgess, Gonen-Yaacovi, Volle, 2011), in which the lFPC can be thought of as protecting information that will be needed in the future but is not currently needed for ongoing behavior. That said, from our study alone it is difficult to make claims about whether the information maintained in frontal pole is actively protecting this information because of potentially interfering processes. Our “indirect transition condition” only contains trials where there is incoming, potentially interfering information about new outcomes, but no trials that might avoid interference (e.g., an interim choice made but there is nothing to be learned from it). We comment on this important future direction on page 14:  

“One interpretation of these results is that the lFPC actively protects information about causal choices when potentially interfering information must be processed. Future studies will be needed to determine if the lFPC’s contributions are specific to these instances of potential interference, and whether this is a passive or active process”

Point 3 of recommendation to authors 

A slightly minor, but still important issue is the interpretation of the role of lOFC. The authors compared the observed patterns of the credit assignment to the ideal patterns of credit assignment. Then, the similarity between these two matrices is used to find the associated brain region. In the assumption that lOFC is involved in the optimal credit assignment, the result seems reasonable. But as mentioned above, the current design involves the heavy role of understanding the task structure, it is debatable whether the lOFC is just involved in the credit assignment process or a more general role of representing the task structure.

We agree that this is an important distinction to make, and it is very likely that multiple regions of the OFC carry information about the task structure, and the extent to which participants understood this structure may be reflected in behavioral estimates of credit assignment or the overall patterns of the matrices (though all participants verbalized the correct structure prior to the task). However, we believe that in our task the lOFC is specifically involved in credit-assignment because of the content of the information we decoded. We demonstrated that the lOFC and HPC carry information about the causal choice during the outcome. These results cannot be explained by differences in understanding of the task structure because that understanding would have been consistent across trials where participants choose either shape identity. Thus, a classifier could not use this to separate these types of trials and would reflect chance decoding.   

One interpretation of the lOFC’s role in credit assignment is that it is particularly important when a model of the task structure has to be used to assign credit appropriately. Here, we show lOFC the reinstates specific causal representations precisely at the time credit needs to be assigned, which are appropriate to participants’ knowledge of the task structure.  These representations may exist alongside representations of the task structure, in the lOFC and other regions of the brain (Park et al., 2020; Boorman et al., 2021; Seo and Lee, 2010; Schuck et al., 2016). We have added the following sentences to clarify our perspective on this point in the discussion (p. 13):

“Our results from the “indirect transition” condition show that these patterns are not merely representations of the most recent choice but are representations of the causal choice given the current task structure, and may exist alongside representations of the task structure, in the lOFC and elsewhere (Boorman et al., 2021; Park et al., 2020; Schuck et al., 2016; Seo & Lee, 2010).”

Point 4 of public reviews and point 4 of recommendation to authors

Broader neural involvement: While the focus on specific regions of interest (ROIs) provided clear results, future studies could benefit from a whole-brain analysis approach to provide a more comprehensive understanding of the neural networks involved in credit assignment… Also, given the ROI constraint of the analysis, the other neural structure may be involved in representing the task structure but not detected in the current analysis

Given our strong a priori hypotheses about regions of interest (ROIs) in this study, we focused on these specific areas. This choice was based on theoretical and empirical grounds that guided our investigation. However, we thank the reviewer for pointing this out and agree that there could be other unexplored areas that are critical to credit-assignment which we did not examine. 

We conducted the same searchlight decoding procedure on a whole brain map and corrected for multiple comparisons using TFCE. We found no significant regions of the brain in the “direct transition condition” but did find other significant regions in our information connectivity analysis of the “indirect transition condition”. In addition to replicating the effects in lOFC and HPC, we also found a region of mOFC which showed a strong correlation with pending choice in lFPC. It’s difficult to say whether this region is involved in credit assignment per se, because we did not see this region in the “direct transition condition” and so we cannot say that it is consistently related to this process. However, the mOFC is thought to be critical to representing the current task state (Schuck et al., 2016), and the task structure (Park et al., 2020). In our task, it could be a critical region for communicating how to assign credit given the more complex task structure of the “indirect transition condition” but more evidence would be needed to support this interpretation. 

For now, we have added the results of this whole brain analysis to a new supplementary figure S7 (page 41), and all unthresholded maps have been deposited in a Neurovault repository, which is linked in the paper, for interested readers to assess.  

Minor points:

There are some missing and confusing details in the Figure reference in the main text. For example, references to Figure 3 are almost missing in the section "Pending item representations in FPl during indirect transitions predict credit assignment in lOFC". For readability, the authors should improve this point in this section and other sections.

Thank you to the reviewer for pointing this out. We have now added references to Figure 3 on page 8:

“Our analysis revealed a cluster of voxels specifically within the right lFPC ([x,y,z] = [28, 54, 8], t(19) = 3.74, pTFCE <0.05 ROI-corrected; left hemisphere all pTFCE > 0.1, Fig. 3A)”

And on page 10: 

Specifically, we found significant correlations in decoding distance between lFPC and bilateral lOFC ([x,y,z] = [-32,24, -22], t(19) = 3.81, [x,y,z] = [20, 38, -14], t(19) = 3.87, pTFCE <0.05 ROI corrected]) and bilateral HC ([x,y,z] = [-28, -10, -24], t(19) = 3.41, [x,y,z] = [22, -10, -24], t(19) = 4.21, pTFCE <0.05 ROI corrected]), Fig. 3C).

Task instructions for the two conditions (direct and indirect) play important roles in the study. If possible, please include the following parts in the figures and descriptions in the introduction and/or results sections.

We have now included a short description of the condition instructions beginning on page 5: 

“Participants were instructed about which condition they were in with a screen displaying “Your latest choice” in the direct transition condition, and “Your previous choice” in the indirect condition.”

And have modified Figure 1 to include the instructions in the title of each condition. We thought this to be the most parsimonious solution so that the choice options in the examples were not occluded. 

The subject sample size might be slightly too small in the current standards. Please give some justifications.

We originally selected the sample size for this study to be commensurate with previous studies that looked for similar behavioral and neural effects (see Boorman et al., 2016; Howard et al., 2015; Jocham et al., 2016). This has been mentioned in the “methods” section on page 24.  

However, to be thorough, we performed a power analysis of this sample size using simulations based on an independently collected, unpublished data set. In this data set, 28 participants competed an associative learning task similar to the task in the current manuscript. We trained a classifier to decode causal choice option at the time of feedback, using the same searchlight and cross-validation procedures described in the current manuscript, for the same lateral OFC ROI. We calculated power for various sample sizes by drawing N participants with replacement 1000 times, for values of N ranging from 15 to 25. After sampling the participants, we tested for significant decoding for the causal choice within the subset of data, using smallvolume TFCE correction to correct for multiple comparisons. Finally, we calculated the proportion of these samples that were significant at a level of pTFCE <.05.  

The results of this procedure show that an N of 20 would result in 84.2% power, which is slightly above the typically acceptable level of 80%. We have added the following sentences to the methods section on page 25: 

“Using an independent, unpublished data set, we conducted a power analysis for the desire neural effect in lOFC. We found that this number of participants had 84% power to detect this effect (Fig. S8).” 

We also added the following figure to the supplemental figures page (42):

Reviewer 2:

I have several concerns regarding the causality analyses in this study. While Multivariate analyses of information connectivity between regions are interesting and appear rigorous, they make some assumptions about the nature of the input data. It is unclear if fMRI with its poor temporal resolution (in addition to possible region-specific heterogeneity in the readouts), can be coupled with these casual analysis methods to meaningfully study dynamics on a decision task where temporal dynamics is a core component (i.e., delay). It would be helpful to include more information/justification on the methods for inferring relationships across regions from fMRI data. Along this line, discussing the reported findings in light of these limitations would be essential.

We agree that fMRI is limited for capturing fast neural dynamics, and that it can be difficult to separate events that occur within a few seconds. However, we designed the information connectivity analysis to maximally separate the events in question – the representations of the causal choice being held in a pending state, and the representation of the causal choice during credit assignment. These events were separated by at least 10 seconds and by 15 seconds on average, which is commensurate with recommended intervals for disentangling information in such analysis (Mumford et al., 2012, 2014, also see van Loon et al., 2018, eLife; as example of fluctuations in decodability over time). This feature of our task design may not have been clear because information connectivity analyses are typically performed in the same task period. We clarify this point on page 32:

“Note that the decoding fidelity metric at each time point represents the decodability of the same choice at different phases of the task. These phases were separated by at least 10 seconds and 15 seconds on average, which can be sufficient for disentangling unique activity (Mumford et al., 2012, 2014).”

However, we agree with the reviewer that the limitations of fMRI make it difficult to precisely determine how roles of the OFC and lFPC might change over time, and whether other regions may contribute to information transfer at times scales which cannot be detected by fMRI. Further, we do not wish to imply causality between lFPC and lOFC (something we believe we do not claim in the paper), only that information strength in lFPC predicts subsequent strength of the same information in the OFC and HC. We have clarified this limitation on page 14:

“Although we show evidence that lFPC is involved in maintaining specific content about causal choices during interim choices, the limited temporal resolution of fMRI makes it difficult to tell if other regions may be supporting the learning processes at timescales not detectable in the BOLD response. Thus, it is possible that the network of regions supporting credit assignment in complex tasks may be much larger. Our results provide a critical first stem in discerning the nature of interactions between cognitive subsystems that make different contributions to the learning process in these complex tasks.”

Reviewer 3:  

Point 1 of public reviews:

They do find (not surprisingly) that the one-back task is harder. It would be good to ensure that the reason that they had more trouble detecting direct HC & lOFC effects on the harder task was not because the task is harder and thus that there are more learning failures on the harder oneback task. (I suspect their explanation that it is mediated by FPl is likely to be correct. But it would be nice to do some subsampling of the zero-back task [matched to the success rate of the one-back task] to ensure that they still see the direct HC and lOFC there).

We would like to thank the reviewer for this comment and agree that the “indirect transition condition” is more difficult than the direct transition condition. However, in this task it is difficult to have an explicit measure of learning failures per se because the “correctness” of a choice is to some extent subjective (i.e., based on the gift card preference and the computational model). We could infer when learning failures occur through the computational model by looking at trials in which participants made choices that the model would consider improbable, (i.e., non-reward maximizing) while accounting for outcome preference. However, there are also a myriad of other possible explanations for these choices, such as exploratory/confirmatory strategies, lapses in attention etc. Thus, we could not guarantee that the two conditions would be uniquely matched in difficulty with specific regard to learning even if we subsampled these trials. We feel it would be better left to future experiments which can specifically compare learning failures to tackle this issue. We have now addressed this point when discussing the model on page 31:  

“Note that learning failures are not trivial to identify in our paradigm and model, because every choice is based on a participant’s preference between gift card outcomes, and the ability of the computational model to accurately estimate participants’ beliefs in the stimulus-outcome transition probabilities.”

Point 2 of public reviews:

The evidence that they present in the main text (Figure 3) that the HC and lOFC are mediated by FPl is a correlation. I found the evidence presented in Supplemental Figure 7 to be much more convincing. As I understand it, what they are showing in SF7 is that when FPl decodes the cue, then (and only then) HC and lOFC decode the cue. If my understanding is correct, then this is a much cleaner explanation for what is going on than the secondary correlation analysis. If my understanding here is incorrect, then they should provide a better explanation of what is going on so as to not confuse the reader.

SF7 (now Figures 3C and 3D) does show that positive decoding in the HC and lOFC are more likely to occur when there is positive decoding in lFPC. However, the analysis shown in these figures are only meant to be control analysis to further characterise what is being captured, but not necessarily implied, by the information connectivity analysis. For example, in principle the classifier might never correctly decode a choice label in the lOFC or HC while still getting closer to the hyperplane when the lFPC patterns are correctly decoded. This would lead to a positive correlation, but a difficult to interpret result since patterns in lOFC and HPC are incorrect. Figure SF7A (now Fig. 3C) shows that this is not the case. Lateral OFC and HC have higher than chance positive decoding when lFPC has positive decoding. Figure SF7B (now Fig. 3D) shows that we can decode that information even if a new hyperplane is constructed. However, both cases have less information about the relationship between these regions because they do not include the trials where lOFC/HC and lFPC classifiers were incorrect at the same time. The correlation in Figure 3B includes these failures, giving a more wholistic picture of the data. We therefore try to concisely clarify this point on page 10:

“These signed distances allow us to relate both success in decoding information, as well as failures, between regions.”

And here on page 10: 

“Subsequent analyses confirmed that this effect was due to these regions showing a significant increase in positive (correct) decoding in trials where pending information could be positively (correctly) decoded in lFPC, and not simply due to a reduction in incorrect information fidelity (see Fig. 3C & 3D).”

And have integrated these figures on page 9:

Point 3 of public reviews:

I like the idea of "credit spreading" across trials (Figure 1E). I think that credit spreading in each direction (into the past [lower left] and into the future [upper right]) is not equivalent. This can be seen in Figure 1D, where the two tasks show credit spreading differently. I think a lot more could be studied here. Does credit spreading in each of these directions decode in interesting ways in different places in the brain?

We agree that this an interesting question because each component of the off diagonal (upper and lower triangles) may reflect qualitatively different processes of credit spreading. However, we believe this analysis is difficult to carry out with the current dataset for two reasons. First, we designed this study to ask specifically about the information represented in key credit assignment regions during precise credit assignment, meaning we did not optimize the task to induce credit spreading at any point. Indeed, our efforts to train participants on the task were to ensure they would correctly assign credit as much as possible. Figure 1F shows that the regression coefficients representing credit spreading in each condition are near zero (in the negative direction), with little individual differences compared to the credit assignment coefficients. Thus, any analysis aiming to test for credit spreading would unfortunately be poorly powered. Studies such as Jocham et al. (2016), with more variability in causal structures, or studies with ambiguity about the causal structure by dissolving the typical trial structure would be better suited to address this interesting question. The second reason why such an analysis would be challenging is that due to our design, it is difficult to intuitively determine what kind of information should be coded by neural regions when credit spreads to the upper diagonal, since these cells reflect current outcomes that are being linked to future choices. 

Replace all the FPl with LFPC (lateral frontal polar cortex)

We have no replace “FPl” with “LFPC” throughout the text and figures

eLife Assessment

This work attempts to demonstrate an ATP-independent non-canonical role of proteasomal component PA28y in the promotion of oral squamous cell carcinoma growth, migration, and invasion. Although the authors have addressed some concerns, uncertainties regarding the PA28g-C1QBP direct interaction still exist. The overall findings of the manuscript are useful, but the validation evidence is incomplete.

Reviewer #2 (Public review):

This manuscript determines how PA28g, a proteasome regulator that is overexpressed in tumors, and C1QBP, a mitochondrial protein for maintaining oxidative phosphorylation that plays a role in tumor progression, interact in tumor cells to promote their growth, migration and invasion. Evidence for the interaction and its impact on mitochondrial form and function was provided although it is not particularly strong.

The revised manuscript corrected mislabeled data in figures and provides more details in figure legends. Misleading sentences and typos were corrected. However, key experiments that were suggested in previous reviews were not done, such as making point mutations to disrupt the protein interactions and assess the consequence on protein stability and function. Results from these experiments are critical to determine whether the major conclusions are fully supported by the data.

The second revision of the manuscript included the proximity ligation data to support the PA28g-C1QBP interaction in cells. However, the method and data were not described in sufficient detail for readers to understand. The revision also includes the structural models of the PA28g-C1QBP complex predicted by AlphaFold. However, the method and data were not described with details for readers to understand how this structural modeling was done, what is the quality of the resulting models, and the physical nature of the protein-protein interaction such as what kind of the non-covalent interactions exist in the interface of the protein complexes. Furthermore, while the interactions mediated by the protein fragments were tested by pull-down experiments, the interactions mediated by the three residues were not tested by mutagenesis and pull-down experiments. In summary, the revision was improved, but further improvement is needed

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Comment of Review of Revised Version:

Although the authors have partly corrected the manuscript by removing the mislabeling in their Co-IP experiments, my primary concern on the actual functional connotations and direct interaction between PA28y and C1QBP still remains unaddressed. As already mentioned in my previous review, since the core idea of the work is PA28y's direct interaction with C1QBP, stabilizing it, the same should be demonstrated in a more convincing manner.

My other observation on the detection of C1QBP as a doublet has been addressed by usage of anti-C1QBP Monoclonal antibody against the polyclonal one used before. C1QBP doublets have not been observed in the present case.

The authors have also worked on the presentation of the background by suitably modifying the statements and incorporating appropriate citations.

However, the authors are requested to follow the recommendations provided to them by the reviewers to address the major concerns.

Thank you very much for your comments. We appreciate your concerns regarding the need for more direct evidence to support the stabilizing interaction between PA28γ and C1QBP. In response to your feedback, we have taken additional steps to provide more convincing evidence of this interaction.

To complement our existing pull-down and Co-IP experiments, we utilized AlphaFold 3 to predict the three-dimensional structure of the PA28γ-C1QBP complex. The predicted model reveals specific residues and interfaces that are likely involved in the direct interaction between PA28γ and C1QBP. Our analysis indicates that this interaction may depend on amino acids 1-167 and 1-213 of C1QBP (Revised Appendix Figure 1E-H). Furthermore, aspartate (ASP), as the 177th amino acids of PA28γ, was predicted to interact with the 76th amino acid threonine (THR) and the 78th amino acid glycine (GLY) of C1QBP (Revised Appendix Figure 1I). This structural insight was further validated by our immunoprecipitation experiments (Revised Figure 1J). These findings provide a molecular basis for the observed stabilizing effect and suggest potential mechanisms by which PA28γ influences C1QBP stability. Specifically, the identified interaction sites offer clues into how PA28γ may stabilize C1QBP at the molecular level.

Furthermore, we performed proximity ligation assays (PLA) to detect in situ interactions between PA28γ and C1QBP at the single-cell level. PLA results clearly demonstrate the presence of PA28γ-C1QBP complexes within cells, providing direct evidence of their physical interaction (Revised Figure 1D). This approach overcomes some of the limitations associated with traditional IP experiments and confirms the direct nature of the interaction.

In summary, the integration of AlphaFold 3 predictions, PLA data, and our previous Pull-down and Co-IP experiments provides robust and direct evidence for a stable interaction between PA28γ and C1QBP. We believe that these additional findings significantly reinforce our conclusions and effectively address the concerns raised by the reviewers. Once again, thank you for your valuable feedback, which has been instrumental in refining and enhancing our study.

Reviewer #2 (Public review):

Comment of Review of Revised Version:

Weaknesses:

Many data sets are shown in figures that cannot be understood without more descriptions either in the text or the legend, e.g., Fig. 1A. Similarly, many abbreviations are not defined.

The revision addressed these issues.

Some of the pull-down and coimmunoprecipitation data do not support the conclusion about the PA28g-C1QBP interaction. For example, in Appendix Fig. 1B the Flag-C1QBP was detected in the Myc beads pull-down when the protein was expressed in the 293T cells without the Myc-PA28g, suggesting that the pull-down was not due to the interaction of the C1QBP and PA28g proteins. In Appendix Fig. 1C, assume the SFB stands for a biotin tag, then the SFB-PA28g should be detected in the cells expressing this protein after pull-down by streptavidin; however, it was not. The Western blot data in Fig. 1E and many other figures must be quantified before any conclusions about the levels of proteins can be drawn.

The revision addressed these problems.

The immunoprecipitation method is flawed as it is described. The antigen (PA28g or C1QBP) should bind to the respective antibody that in turn should binds to Protein G beads. The resulting immunocomplex should end up in the pellet fraction after centrifugation, and analyzed further by Western blot for coprecipitates. However, the method in the Appendix states that the supernatant was used for the Western blot.

The revision corrected this method.

To conclude that PA28g stabilizes C1QBP through their physical interaction in the cells, one must show whether a protease inhibitor can substitute PA28q and prevent C1QBP degradation, and also show whether a mutation that disrupt the PA28g-C1QBP interaction can reduce the stability of C1QBP. In Fig. 1F, all cells expressed Myc-PA28g. Therefore, the conclusion that PA28g prevented C1QBP degradation cannot be reached. Instead, since more Myc-PA28g was detected in the cells expressing Flag-C1QBP compared to the cells not expressing this protein, a conclusion would be that the C1QBP stabilized the PA28g. Fig. 1G is a quantification of a Western blot data that should be shown.

The binding site for PA28g in C1QBP was mapped to the N-terminal 167 residues using truncated proteins. One caveat would be that some truncated proteins did not fold correctly in the absence of the sequence that was removed. Thus, the C-terminal region of the C1QBP with residues 168-283 may still bind to the PA29g in the context of full-length protein. In Fig. 1I, more Flag-C1QBP 1-167 was pull-down by Myc-PA28g than the full-length protein or the Flag-C1QBP 1-213. Why?

The interaction site in PA28g for C1QBP was not mapped, which prevents further analysis of the interaction. Also, if the interaction domain can be determined, structural modeling of the complex would be feasible using AlphaFold2 or other programs. Then, it is possible to test point mutations that may disrupt the interaction and if so, the functional effect.

The revision added AlphaFold models for the protein interaction. However, the models were not analyzed and potential mutations that would disrupt the interact were not predicted, made and tested. The revision did not addressed the request for the protease inhibitor.

Thank you for your insightful comments regarding the binding site of PA28γ in C1QBP. We appreciate your concern about the potential misfolding of truncated proteins and the possible interaction between the C-terminal region (residues 168-283) of C1QBP and PA28γ in the context of full-length protein.

To address these concerns, we have conducted additional analyses and experiments to provide a more comprehensive understanding of the interaction between PA28γ and C1QBP. Using AlphaFold 3, we predicted the three-dimensional structure of the PA28γ-C1QBP complex. The model reveals specific residues and interfaces that are likely involved in the direct interaction between PA28γ and C1QBP. Notably, our structural analysis indicates that the interaction may primarily depend on amino acids 1-167 and 1-213 of C1QBP (Revised Appendix Figure 1E-H). Furthermore, aspartate (ASP), as the 177th amino acids of PA28γ, was predicted to interact with the 76th amino acid threonine (THR) and the 78th amino acid glycine (GLY) of C1QBP (Revised Appendix Figure 1I). This prediction supports the idea that the N-terminal region of C1QBP is crucial for its interaction with PA28γ. Regarding the observation in old Figure 1I (Revised Figure 1J), where more Flag-C1QBP 1-167 was pulled down by Myc-PA28γ compared to the full-length protein or Flag-C1QBP 1-213, we believe this can be explained by several factors:

A. The truncation of C1QBP to residues 1-167 may expose key interaction sites that are partially obscured in the full-length protein. This enhanced accessibility could lead to stronger binding affinity and higher pull-down efficiency.

B. While it is possible that some truncated proteins do not fold correctly, our data suggest that the N-terminal fragment (1-167) retains sufficient structural integrity to interact effectively with PA28γ. The increased pull-down of this fragment suggests that it captures the essential elements required for binding.

C. The C-terminal region (168-283) might exert steric hindrance or allosteric effects on the N-terminal binding site in the context of the full-length protein. This interference could reduce the overall binding efficiency, leading to less pull-down of full-length C1QBP compared to the truncated version.

Compared with the control group, the presence of Myc-PA28γ significantly increased the expression level of Flag-C1QBP (r Revised Figure 1G). Gray value analysis showed that in cells transfected with Myc-PA28γ, the decay rate of Flag-C1QBP was significantly slower than that of the control group (Revised Figure 1H), suggesting that PA28γ can delay the protein degradation of C1QBP and stabilize its protein level. This indicates that an increase in the level of PA28γ protein can significantly enhance the expression level of C1QBP protein, while PA28γ can slow down the degradation rate of C1QBP and improve its stability. In addition, our western blot analysis also proved that PA28γ could still prevent the degradation of C1QBP under the action of proteasome inhibitor MG-132 (Revised Appendix Figure 1D). Moreover, PA28γ could not stabilize the mutation of C-terminus of C1QBP (amino acids 94-282), which was not the interaction domain of PA28γ-C1QBP (Revised Figure 1K).

eLife Assessment

This valuable study leverages innovative high-dimensional imaging strategies to interrogate pancreatic immune cell profiles and distributions throughout stages of type 1 diabetes (T1D). Despite a notable limitation in the number of donor samples analyzed, the authors identify a series of intriguing "immune signatures" and histopathological features that collectively constitute a solid foundation for future investigations into immunological processes underpinning the pathogenesis of T1D. Accordingly, the work will be of considerable interest to the community of T1D researchers and clinicians.

Reviewer #1 (Public review):

Summary:

Barlow and coauthors utilized the high-parameter imaging platform of CODEX to characterize the cellular composition of immune cells in situ from tissues obtained from organ donors with type 1 diabetes, subjects presented with autoantibodies who are at elevated risk, or non-diabetic organ donor controls. The panels used in this important study were based up prior publications using this technology, as well a priori and domain specific knowledge of the field by the investigators. Thus, there was some bias in the markers selected for analysis. The authors acknowledge that these types of experiments may be complemented moving forward with the inclusion of unbiased tissue analysis platforms that are emerging that can conduct a more comprehensive analysis of pathological signatures employing emerging technologies for both high-parameter protein imaging and spatial transcriptomics.

Strengths:

In terms of major findings, the authors provide important confirmatory observations regarding a number of autoimmune-associated signatures reported previously. The high parameter staining now increases the resolution for linking these features with specific cellular subsets using machine learning algorithms. These signatures include a robust signature indicative of IFN-driven responses that would be expected to induce a cytotoxic T cell mediated immune response within the pancreas. Notable findings include the upregulation of indolamine 2,3-dioxygenase-1 in the islet microvasculature. Furthermore, the authors provide key insights as to the cell:cell interactions within organ donors, again supporting a previously reported interaction between presumably autoreactive T and B cells.

Weaknesses:

These studies also highlight a number of molecular pathways that will require additional validation studies to more completely understand whether they are potentially causal for pathology, or rather, epiphenomenon associated with increased innate inflammation within the pancreas of T1D subjects. Given the limitations noted above, the study does present a rich and integrated dataset for analysis of enriched immune markers that can be segmented and annotated within distinct cellular networks. This enabled the authors to analyze distinct cellular subsets and phenotypes in situ, including within islets that peri-islet infiltration and/or intra-islet insulitis.

Despite the many technical challenges and unique organ donor cohort utilized, the data are still limited in terms of subject numbers - a challenge in a disease characterized by extensive heterogeneity in terms of age of onset and clinical and histopathological presentation. Therefore, these studies cannot adequately account for all of the potential covariates that may drive variability and alterations in the histopathologies observed (such as age of onset, background genetics, and organ donor conditions). In this study, the manuscript and figures could be improved in terms of clarifying how variable the observed signatures were across each individual donor, with the clear notion that non-diabetic donors will present with some similar challenges and variability.

Reviewer #2 (Public review):

Summary:

The authors aimed to characterize the cellular phenotype and spatial relationship of cell types infiltrating the islets of Langerhans in human T1D using CODEX, a multiplexed examination of cellular markers

Strengths:

Major strengths of this study are the use of pancreas tissue from well-characterized tissue donors, the use of CODEX, a state-of-the-art detection technique of extensive characterization and spatial characterization of cell types and cellular interactions. The authors have achieved their aims with the identification of the heterogeneity of the CD8+ T cell populations in insulitis, the identification of a vasculature phenotype and other markers that may mark insulitis-prone islets, and characterization of tertiary lymphoid structures in the acinar tissue of the pancreas. These findings are very likely to have a positive impact on our understanding (conceptual advance) of the cellular factors involved in T1D pathogenesis which the field requires to make progress in therapeutics.

Weaknesses:

A major limitation of the study is the cohort size, which the authors directly state. However, this study provides avenues of inquiry for researchers to gain further understanding of the pathological process in human T1D.

Comments on revisions:

The authors have responded well to the 3 critiques. They have addressed my specific comments in their revised text.<br /> I have no further comments.

Reviewer #3 (Public review):

Summary:

The authors applied an innovative approach (CO-Detection by indEXing - CODEX) together with sophisticated computational analyses to image pancreas tissues from rare organ donors with type 1 diabetes. They aimed to assess key features of inflammation in both islet and extra-islet tissue areas; they report that the extra-islet space of lobules with extensive islet infiltration differs from the extra-islet space of less infiltrated areas within the same tissue section. The study also identifies four sub-states of inflamed islets characterized by the activation profiles of CD8+T cells enriched in islets relative to the surrounding tissue. Lymphoid structures are identified in the pancreas tissue away from islets, and these were enriched in CD45RA+ T cells - a population also enriched in one of the inflamed islet sub-states. Together, these data help define the coordination between islets and the extra-islet pancreas in the pathogenesis of human T1D.

Strengths:

The analysis of tissue from well-characterized organ donors, provided by the Network for the Pancreatic Organ Donor with Diabetes, adds strength to the validity of the findings.

By using their innovative imaging/computation approaches, key known features of islet autoimmunity were confirmed, providing validation of the methodology.

The detection of IDO+ vasculature in inflamed islets - but not in normal islets or islets that have lost insulin-expression links this expression to the islet inflammation, and it is a novel observation. IDO expression in the vasculature may be induced by inflammation and may lost as disease progresses, and it may provide a potential therapeutic avenue.

The high-dimensional spatial phenotyping of CD8+T cells in T1D islets confirmed that most T cells were antigen experienced. Some additional subsets were noted: a small population of T cells expressing CD45RA and CD69, possibly naive or TEMRA cells, and cells expressing Lag-3, Granzyme-B, and ICOS.

While much attention has been devoted to the study of the insulitis lesion in T1D, our current knowledge is quite limited; the description of four sub-clusters characterized by the<br /> activation profile of the islet-infiltrating CD8+T cells is novel. Their presence in all T1D donors, indicates that the disease process is asynchronous and is not at the same stage across all islets. Although this concept is not novel, this appears to be the most advanced characterization of insulitis stages.

When examining together both the exocrine and islet areas, which is rarely done, authors report that pancreatic lobules affected by insulitis are characterized by distinct tissue markers. Their data support the concept that disease progression may require crosstalk between cells in the islet and extra-islet compartments. Lobules enriched in β-cell-depleted islets were also enriched in nerves, vasculature, and Granzyme-B+/CD3- cells, which may be natural killer cells.

Lastly, authors report that immature tertiary lymphoid structures (TLS) exist both near and away from islets, where CD45RA+ CD8+T cells aggregate, and also observed an inflamed islet-subcluster characterized by an abundance of CD45RA+/CD8+ T cells. These TLS may represent a point of entry for T cells and this study further supports their role in islet autoimmunity.

Weaknesses:

As the author themselves acknowledge, the major limitation is that the number of donors examined is limited as those satisfying study criteria are rare. Thus, it is not possible to examine disease heterogeneity, and the impact of age at diagnosis. Of 8 T1D donors examined, 4 would be considered newly diagnosed (less than 3 months from onset) and 4 had longer disease durations (2, 2, 5 and 6 years). It was unclear if disease duration impacted the results in this small cohort. In the introduction, the authors discuss that most of the pancreata from nPOD donors with T1D lack insulitis. This is correct, yet it is a function of time from diagnosis. Donors with shorter duration will be more likely to have insulitis. A related point is that the proportion of islets with insulitis is low even near diagnosis, Finally, only one donor was examined that while not diagnosed with T1D, was likely in the preclinical disease stage and had autoantibodies and insulitis. This is a critically important disease stage where the methodology developed by the investigators could be applied in future efforts.

While this was not the focus of this investigation, it appears that the approach was very much immune-focused and there could be value in examining islet cells in greater depth using the methodology the authors developed.

Additional comments

Overall, the authors were able to study pancreas tissues from T1D donors and perform sophisticated imaging and computational analysis that reproduce and importantly extend our understanding of inflammation in T1D. Despite the limitations associated with the small sample size, the results appear robust, and the claims are well supported.

The study expands the conceptual framework of inflammation and islet autoimmunity, especially by the definition of different clusters (stages) of insulitis and by the characterization of immune cells in and outside the islets.

Comments on revisions:

I have not felt the need to update the initial review.

However, I note that the paragraph describing the nPOD repository (lines 154-158) can be misinterpreted that insulitis is infrequent in T1D (17 of 200 donors had it) without the clarification that insulitis is present around the time of diagnosis in most patients and it subsides over time. Thus, authors are urged to clarify that the presence of insulitis and its severity are impacted by the disease stage and disease duration.

The last sentence of this paragraph, lines 164-165, although linked to the previous sentence about the cause of death in the donors, may be misconstrued in the context of this paragraph, and it is unclear what data support this statement. Please delete this sentence.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Barlow and coauthors utilized the high-parameter imaging platform of CODEX to characterize the cellular composition of immune cells in situ from tissues obtained from organ donors with type 1 diabetes, subjects presented with autoantibodies who are at elevated risk, or non-diabetic organ donor controls. The panels used in this important study were based on prior publications using this technology, as well as a priori and domain-specific knowledge of the field by the investigators. Thus, there was some bias in the markers selected for analysis. The authors acknowledge that these types of experiments may be complemented moving forward with the inclusion of unbiased tissue analysis platforms that are emerging that can conduct a more comprehensive analysis of pathological signatures employing emerging technologies for both high-parameter protein imaging and spatial transcriptomics.

Strengths:

In terms of major findings, the authors provide important confirmatory observations regarding a number of autoimmune-associated signatures reported previously. The high parameter staining now increases the resolution for linking these features with specific cellular subsets using machine learning algorithms. These signatures include a robust signature indicative of IFN-driven responses that would be expected to induce a cytotoxic T-cell-mediated immune response within the pancreas. Notable findings include the upregulation of indolamine 2,3-dioxygenase-1 in the islet microvasculature. Furthermore, the authors provide key insights as to the cell:cell interactions within organ donors, again supporting a previously reported interaction between presumably autoreactive T and B cells.

Weaknesses:

These studies also highlight a number of molecular pathways that will require additional validation studies to more completely understand whether they are potentially causal for pathology, or rather, epiphenomenon associated with increased innate inflammation within the pancreas of T1D subjects. Given the limitations noted above, the study does present a rich and integrated dataset for analysis of enriched immune markers that can be segmented and annotated within distinct cellular networks. This enabled the authors to analyze distinct cellular subsets and phenotypes in situ, including within islets that peri-islet infiltration and/or intra-islet insulitis.

Despite the many technical challenges and unique organ donor cohort utilized, the data are still limited in terms of subject numbers - a challenge in a disease characterized by extensive heterogeneity in terms of age of onset and clinical and histopathological presentation. Therefore, these studies cannot adequately account for all of the potential covariates that may drive variability and alterations in the histopathologies observed (such as age of onset, background genetics, and organ donor conditions). In this study, the manuscript and figures could be improved in terms of clarifying how variable the observed signatures were across each individual donor, with the clear notion that non-diabetic donors will present with some similar challenges and variability.

Thank you to all reviewers and editors for their thoughtful and constructive engagement with our manuscript. We agree that patient heterogeneity and the sample size limited the impact of this study. In the future, more cases with insulitis will become available and spatial technologies will become more scalable.

Given these constraints, we have made a significant effort to illustrate the individual heterogeneity of the disease by using the same color for each nPOD case ID throughout the manuscript and showing individual donors whenever feasible (e.g. Figures 1D-E, 2C, 2I, 3E, 3G, 4B-C, 5C, and 5F). For figures related to insulitis, we do not typically include non-T1D controls since they did not have any insulitis (Figure 2C). We also explicitly discuss the differences in the two autoantibody-positive, non-T1D cases: one closely resembled the T1D cases with respect to multiple features and the other more closely resembled the non-T1D, autoantibody-negative controls.

Reviewer #2 (Public review):

Summary:

The authors aimed to characterize the cellular phenotype and spatial relationship of cell types infiltrating the islets of Langerhans in human T1D using CODEX, a multiplexed examination of cellular markers

Strengths:

Major strengths of this study are the use of pancreas tissue from well-characterized tissue donors, and the use of CODEX, a state-of-the-art detection technique of extensive characterization and spatial characterization of cell types and cellular interactions. The authors have achieved their aims with the identification of the heterogeneity of the CD8+ T cell populations in insulitis, the identification of a vasculature phenotype and other markers that may mark insulitis-prone islets, and the characterization of tertiary lymphoid structures in the acinar tissue of the pancreas. These findings are very likely to have a positive impact on our understanding (conceptual advance) of the cellular factors involved in T1D pathogenesis which the field requires to make progress in therapeutics.

Weaknesses:

A major limitation of the study is the cohort size, which the authors directly state. However, this study provides avenues of inquiry for researchers to gain further understanding of the pathological process in human T1D.

Thank you for your analysis. We point the reader to our above description of our efforts to faithfully report the patient variability despite the small sample size.

Reviewer #3 (Public review):

Summary:

The authors applied an innovative approach (CO-Detection by indEXing - CODEX) together with sophisticated computational analyses to image pancreas tissues from rare organ donors with type 1 diabetes. They aimed to assess key features of inflammation in both islet and extra-islet tissue areas; they reported that the extra-islet space of lobules with extensive islet infiltration differs from the extra-islet space of less infiltrated areas within the same tissue section. The study also identifies four sub-states of inflamed islets characterized by the activation profiles of CD8+T cells enriched in islets relative to the surrounding tissue. Lymphoid structures are identified in the pancreas tissue away from islets, and these were enriched in CD45RA+ T cells - a population also enriched in one of the inflamed islet sub-states. Together, these data help define the coordination between islets and the extra-islet pancreas in the pathogenesis of human T1D.

Strengths:

The analysis of tissue from well-characterized organ donors, provided by the Network for the Pancreatic Organ Donor with Diabetes, adds strength to the validity of the findings.

By using their innovative imaging/computation approaches, key known features of islet autoimmunity were confirmed, providing validation of the methodology.

The detection of IDO+ vasculature in inflamed islets - but not in normal islets or islets that have lost insulin-expression links this expression to the islet inflammation, and it is a novel observation. IDO expression in the vasculature may be induced by inflammation and may be lost as disease progresses, and it may provide a potential therapeutic avenue.

The high-dimensional spatial phenotyping of CD8+T cells in T1D islets confirmed that most T cells were antigen-experienced. Some additional subsets were noted: a small population of T cells expressing CD45RA and CD69, possibly naive or TEMRA cells, and cells expressing Lag-3, Granzyme-B, and ICOS.

While much attention has been devoted to the study of the insulitis lesion in T1D, our current knowledge is quite limited; the description of four sub-clusters characterized by the activation profile of the islet-infiltrating CD8+T cells is novel. Their presence in all T1D donors indicates that the disease process is asynchronous and is not at the same stage across all islets. Although this concept is not novel, this appears to be the most advanced characterization of insulitis stages.

When examining together both the exocrine and islet areas, which is rarely done, authors report that pancreatic lobules affected by insulitis are characterized by distinct tissue markers. Their data support the concept that disease progression may require crosstalk between cells in the islet and extra-islet compartments. Lobules enriched in β-cell-depleted islets were also enriched in nerves, vasculature, and Granzyme-B+/CD3- cells, which may be natural killer cells.

Lastly, authors report that immature tertiary lymphoid structures (TLS) exist both near and away from islets, where CD45RA+ CD8+T cells aggregate, and also observed an inflamed islet-subcluster characterized by an abundance of CD45RA+/CD8+ T cells. These TLS may represent a point of entry for T cells and this study further supports their role in islet autoimmunity.

Weaknesses:

As the authors themselves acknowledge, the major limitation is that the number of donors examined is limited as those satisfying study criteria are rare. Thus, it is not possible to examine disease heterogeneity and the impact of age at diagnosis. Of 8 T1D donors examined, 4 would be considered newly diagnosed (less than 3 months from onset) and 4 had longer disease durations (2, 2, 5, and 6 years). It was unclear if disease duration impacted the results in this small cohort. In the introduction, the authors discuss that most of the pancreata from nPOD donors with T1D lack insulitis. This is correct, yet it is a function of time from diagnosis. Donors with shorter duration will be more likely to have insulitis. A related point is that the proportion of islets with insulitis is low even near diagnosis, Finally, only one donor was examined that while not diagnosed with T1D, was likely in the preclinical disease stage and had autoantibodies and insulitis. This is a critically important disease stage where the methodology developed by the investigators could be applied in future efforts.

While this was not the focus of this investigation, it appears that the approach was very much immune-focused and there could be value in examining islet cells in greater depth using the methodology the authors developed.

Additional comments:

Overall, the authors were able to study pancreas tissues from T1D donors and perform sophisticated imaging and computational analysis that reproduce and importantly extend our understanding of inflammation in T1D. Despite the limitations associated with the small sample size, the results appear robust, and the claims well-supported.

The study expands the conceptual framework of inflammation and islet autoimmunity, especially by the definition of different clusters (stages) of insulitis and by the characterization of immune cells in and outside the islets.

Thank you for your feedback. We agree that it would be very informative to expand on our analysis of autoantibody-positive cases and look at additional non-immune features. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Do any of the observed cellular or structural features correlate with age of onset or disease duration? While numbers of subjects are low, considering these as continuous variables may clarify some of the findings.

Thank you for the suggestion. In Supplemental Figure 5B-C, we plotted the key immune signatures from the manuscript against the diabetes duration and age of onset.

(2) The IDO is an interesting observation and has prior support in the literature. The authors speculate this may be induced as a feature of IFNg expressed by lymphocytes in the local microenvironment. Can any of these concepts be further validated by staining for transcription factors or surrogate downstream markers associated with Th1 skewing (e.g., Tbet, CXCR3, etc)?

The only other interferon-stimulated gene in our panel is HLA-ABC. We updated Supplemental Figure 2F to include HLA-ABC expression in IDO- and IDO+ islets (within the “Inflamed” group). Consistent with the hypothesis that IDO is stimulated by interferon, HLA-ABC is also significantly higher in IDO+ islets than IDO- islets. PDL1, another interferon-stimulated gene. was included in the panel but we did not detect any signal. This antibody was very weak during testing in the tonsil, so we couldn’t confidently claim that PDL1 was not expressed.

(3) The authors discuss the potential that CD45RA may be expressed in Temra populations. This could use additional clarification and a distinction from Tscm if possible.

Unfortunately, we did not have the appropriate markers to distinguish naïve, TEMRA, or Tscm cells from each other. We updated the text in the discussion to include this consideration (Line 432).

(4) Supplemental Figure 5 is not informative in the current display.

Thank you, we replotted these data.

(5) Supplemental Table 1 could be expanded with additional metadata of interest, including the genetic features of the donors (e.g, class II diplotype and GRS2 values) that are published and available in the nPOD program.

Some genetic data are only available to nPOD investigators. We think it is more appropriate to request the data directly from them.

Reviewer #2 (Recommendations for the authors):

(1) I had only a few specific comments. I think the statement in Lines 317 and 318 is too strong. It implies that each lobe is always homogeneous for having all islets with insulitis or not having insulitis. Some lobes are certainly enriched for islets with insulitis but insulin+ islets without insulitis in some lobes in some T1D donors are seen. Please soften that statement.

We apologize for our lack of clarity. We have edited the text (line 305-309) to better articulate that organ donors fall on a spectrum. Thank you for raising this point as we think the motivation for our analysis is much clearer after these revisions.

(2) Please cite and discuss In't Veld Diabetes 20210 PMID: 20413508. While the main point of the paper is that there is beta cell replication after prolonged life support, another observation is that there is a correlation between prolonged life support and CD45+ cells in the pancreas parenchyma. This might indicate that not all immune cells in the parenchyma are T1D associated in donors with T1D.

Thank you, we have added this citation to our discussion of the importance of duration of stay in the ICU (Line 471).

(3) Can you rule out that CD46RA+/CD69+ CD8+ T cells in the islets are not TSCM?

(See above)

Reviewer #3 (Recommendations for the authors):

Similar studies in experimental models may afford increased opportunity to evaluate the significance of these findings and model their potential relevance for disease staging and therapeutic targeting.

We agree that the lack of experimental data limits the ability to interpret and validate the significance of our findings. We hope that our study motivates and helps inform such experiments.

eLife Assessment

The authors demonstrate the valuable discovery that human CD29+/CD56+ myogenic progenitors can differentiate into tendon through the TGFβ pathway, addressing mouse and human interspecies differences in regard to the potential of muscle stem cells. The in vivo transplantation experiments provide convincing evidence for the conclusion, as human CD29+/CD56+ myogenic progenitors contribute to tendon regeneration, resulting in functional recovery in mouse model. The authors' approach can be used for the development of cell therapy for tendon-injured patients.

Reviewer #3 (Public review):

Summary:

The authors have thoroughly addressed all my concerns. The revised version of the current manuscript is solid now. It's very interesting that there is bi-potential ability of human CD29/CD56+ myogenic progenitors. The current study substantiates the medical translational potential for human CD29/CD56+ myogenic progenitors in promoting tendon regeneration.

Strengths:

CD29+/CD56+ stem/progenitor cells were transplanted into immunodeficient mice with a tendon injury, and human cells expressing tenogenic markers contributed to the repair of the injured tendon. Furthermore, the authors also show better tendon biomechanical properties and plantarflexion force after transplantation.

Weaknesses:

None. The authors have thoroughly addressed all my concerns.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

For the colony analysis, it is unclear from the methods and main text whether the initial individual sorted colonies were split and subject to different conditions to support the claim of bi-potency. The finding that 40% of colonies displayed tenogenic differentiation, may instead suggest heterogeneity of the sorted progenitor population. The methods as currently described, suggest that two different plates were subject to different induction conditions. It is therefore difficult to assess the strength of the claim of bi-potency.

Thanks for your valuable comment. We are sorry for the confusing illustration of colony assay. In fact, we first obtained CD29+/CD56+ myogenic progenitors by FACs. Then these freshly isolated cells were randomly seeded to 96-well plate with density of 1 cell/well. Subsequently, the single cell in each plate was cultured with growth medium to form colonies for ten days. Then myogenic induction was performed in three 96-well plates and tenogenic induction was performed in another three 96-well plates for subsequent analyses. We agree with your point that the sorted cell population could be heterogeneous myogenic progenitors. The result showed over 95% colonies successfully differentiated into myotubes, while 40% of colonies displayed tenogenic differentiation (Fig. 2g). Since the freshly obtained CD29+/CD56+ myogenic progenitors were randomly seeded for tenogenic induction or myogenic induction, the undifferentiated cells in each group were considered as the same sample. Furthermore, the optimal tenogenic differentiation condition for these cells was still waiting for investigation. Thus, we believe the colony analysis combined with the data in Figure 1 and Figure 2 could indicate the bi-potency for human CD29+/CD56+ myogenic progenitors.

This group uses the well-established CD56+/CD29+ sorting strategy to isolate muscle progenitor cells, however recent work has identified transcriptional heterogeneity within these human satellite cells (ie Barruet et al, eLife 2020). Given that they identify a tenocyte population in their human muscle biopsy in Figure 1a, it is critical to understand the heterogeneity contained within the population of human progenitors captured by the authors' FACS strategy and whether tenocytes contained within the muscle biopsy are also CD56+/CD29+.

Thanks for your constructive suggestion. We have included more samples to perform scRNA-seq and reanalyzed the data. The scRNA-seq data revealed that all the CD29+/CD56+ cells were myogenic progenitors, which occupied 19.3% of all the myogenic progenitors (Fig. 1e). However, there existed no tenocytes with CD29+/CD56+ (Fig. 1d), and tenocytes made up only a small percentage (0.06%) of all the mononuclear cells. Thus, human CD29+/CD56+ cells are myogenic progenitors, and tenocytes contained within the muscle biopsy are not CD56+/CD29+. In addition, both published research and our results indicated the heterogeneity of CD29+/CD56+ myogenic progenitors. Since the main purpose of current study was to investigate the tenogenic differentiation potential of CD29+/CD56+ myogenic progenitors, the heterogeneity in CD29+/CD56+ myogenic progenitors should be investigated in the further study.

The bulk RNA sequencing data presented in Figure 3 to contrast the expression of progenitor cells under different differentiation conditions are not sufficiently convincing. In particular, it is unclear whether more than one sample was used for the RNAseq analyses shown in Figure 3. The volcano plots have many genes aligned on distinct curves suggesting that there are few replicates or low expression. There is also a concern that the sorted cells may contain tenocytes as tendon genes SCX, MKX, and THBS4 were among the genes upregulated in the myogenic differentiation conditions (shown in Figure 3b).

Thanks for your comment. Each group consisted of three samples for RNAseq analyses. We are sorry there existed a minor analysis mistake in Fig. 3b and Fig. 3c, which have been reanalyzed in the revised version. There was no significantly difference of tendon related marker genes after myogenic differentiation (Fig. 3b), while these tenogenic genes were significantly up-regulated after tenogenic induction (Fig. 3c). As for contamination of tenocytes, scRNA-seq data showed there were no tenocytes with both CD29 and CD56 positive (please see response to Comment 2). And almost all the obtained cells highly expressed myogenic progenitors markers PAX7/MYOD1/MYF5 (Fig. 1f-g). Low expression levels of tendon markers were identified in these cells (Fig. 2a-c). Furthermore, although tendon genes slightly upregulated in myogenic differentiation conditions, these markers dramatically upregulated in tenogenic differentiation conditions (Fig. 2c). Thus, we believe the bulk RNA sequencing data could add the evidence of tenogenic differentiation ability of human CD29+/CD56+ myogenic progenitors.

Reviewer #2 (Public Review):

scRNAseq assay using total mononuclear cell population did not provide meaningful insight that enriched knowledge on CD56+/CD29+ cell population. CD56+/CD29+ cells information may have been lost due to the minority identity of these cells in the total skeletal muscle mononuclear population, especially given the total cell number used for scRNAseq was very low and no information on participant number and repeat sample number used for this assay. Using this data to claim a stem cell lineage relationship for MuSCs and tenocytes may not convincing, as seeing both cell types in the total muscle mononuclear population does not establish a lineage connection between them.

Thanks for your constructive suggestion. We have included more samples to perform scRNA-seq and reanalyzed the data. Three samples with a total of 57,193 cells were included for analysis. As you can see in Fig. 1d and 1e, the joint expression analysis revealed that all the CD29+/CD56+ cells were myogenic progenitors, which occupied 19.3% of all the myogenic progenitors.  In addition, we agree with your comment that the pseudotime analysis could be a bit misleading as the nature of computational biology with pseudotime plots, so we deleted this assay.

The TGF-b pathway assay uses a small molecular inhibitor of TGF-b to probe Smad2/3. The assay conclusion regarding Smad2/3 pathway responsible for tenocyte differentiation may be overinterpretation without Smad2/3 specific inhibitors being applied in the experiments.

Thanks for your comment. We agree with your comment and we have revised it in the revision version (Figure 7, Line 306-326).

Reviewer #3 (Public Review):

This dual differentiation capability was not observed in mouse muscle stem cells.

Thanks for your comment. We have explored the tenogenic differentiation potential of mouse MuSCs both in vivo and in vitro. However, low tenogenic differentiation ability was revealed (Figure 4), which might be due to species diversity. Maybe it is more demanding for humans to maintain the homeostasis of the locomotion system and the whole organism locomotion ability in much longer life span and bigger body size. Thus, the current study also indicated that anima studies may not clinically relevant when investigating human diseases.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

The methods section contained insufficient details for sample tissue for many methods, including the single cell analysis, RNA FISH, and for in vivo cardiotoxin treatment. ie. how were the samples subclustered for the monocle pseudotime analysis; how many cells were counted in the FISH shown in Fig 1e/f, does the n=5 refer to tissue sections or biological replicates?; for the double injury, what was the cardiotoxin dose?

Thanks for your comment. Three samples and a total 57,193 cells were analyzed in single cell analysis (Line 464). We deleted RNA FISH assay data because it provided limited information to prove bipotential ability of human CD29+/CD56+ myogenic progenitors. In addition, since the pseudotime analysis could be a bit misleading as the nature of computational biology with pseudotime plots, we also deleted this assay. For the double injury, 15μl of 10μM cardiotoxin was used for lineage tracing (Line 533).

Additionally, the RNA sequencing datasets are not currently publicly available under the accession numbers provided.

The raw data of RNA sequencing has been uploaded in NCBI (accession number: PRJNA1178160, PRJNA1012476 and PRJNA1012828), and these data will be released immediately after publication.

The poor resolution of 1d makes it impossible to read any of the gene names or interpret the expression profiles of their proposed trajectories.

Since the pseudotime analysis could be a bit misleading as the nature of computational biology with pseudotime plots, we deleted this assay.

What does the color key for 3a refer to? It is not indicated in the figure or legend.

Thanks for your comment. The color key for 3a refer to “Scaled expression values”, which has been added in the revised version.

scRNAseq of the sorted CD29/56+ population could help uncover possible cell heterogeneity within these muscle progenitors and which sub-populations of myogenic progenitor cells have tenogenic potential.

Thanks for your valuable suggestion. We included more cells from three biological repetitions to perform scRNA-seq and found that CD29/CD56+ cells were absolutely from myogenic progenitors (Fig. 1d and 1e). We agree with you that additional scRNAseq will be helpful to clarify the possible cell heterogeneity within these muscle progenitors. Since the main scope of current study is to investigate the biopotential of CD29/CD56+ myogenic progenitors, analysis of scRNAseq of the sorted CD29/56+ population would be performed in the further study for further exploration.

Typos: Line 459 sored cells... preparasion with Chromium Single Cell 3' Reagent Kits (10X genomics, cat# 1000121-1000157). Figure 4E - typo in the word tamoxifen.

Thanks for your valuable suggestion. We are sorry for the typos and have revised these typos (Line 459 and Fig. 4e).

Reviewer #2 (Recommendations For The Authors):

(1) scRNAseq is performed in total mononuclear cells isolated from human skeletal muscle. The cell number (around 15000 cells) seems very low for this assay, given the CD56+/CD29+ cells are a minority population in this sequencing, the data does not seem to provide meaningful insight into the MuSC cell identities. No information on sample numbers and number of patient participants can be found in the paper.

Thanks for your comment. We added more cells to reanalyze the data in the revised manuscript. Three samples with a total of 57,193 cells were analyzed (Line 464). The joint expression analysis revealed that all the CD29+/CD56+ cells were myogenic progenitors, which occupied 19.3% of all the myogenic progenitors (Fig. 1d and 1e). These scRNA-seq data combined with functional experiment confirmed the MuSC cell identity of CD29+/CD56+ cells from mononuclear cells.

In this regard, the paragraph starts with "To confirm the single cell analysis results, we first isolated myogenic progenitor cells from human muscle biopsy using FACS as described previously" which is misleading as the seRNAseq is not the result of the sorted cells. Please reword this paragraph to clarify.

The related paragraph has been reworded (Line 84-95).

Similarly, the existence of myocytes and tenocytes in scRNAseq does not necessarily prove a stem cell and mature cell lineage relationship. Please edit the wording to avoid overinterpretation.

Thanks for your reminding. Since the pseudotime analysis could be a bit misleading as the nature of computational biology with pseudotime plots, we deleted this assay.

(2) The in vitro differentiation assays are well performed, which included bulk culture and clonal culture. The efficiencies of those two assays seem to have discrepancies which may need clarification. Again, no sample numbers and repeats have been informed.

Since the tendon differentiation period for bulk culture was 12 days, those myotubes fused by CD29+/CD56+ myogenic progenitors with only myogenic differentiation potential will be no longer alive. Thus, the efficiency of bulk culture seemed higher than that in clonal culture. As stated in statistical analysis, at least three biological replicates and technical repeats were performed in each experimental group (Line 577).

In these paragraphs, terminologies including MuSCs, myogenic progenitors, CD56+/CD29+, and Pax7+ are interchangeably used, which generates confusion while reading. It is probably best to consistently use the cell sorting markers markers to address this cell population, throughout the paper.

Thanks for your constructive suggestion. The cell population was consistently named as CD29+/CD56+ myogenic progenitors throughout the paper.

Information on the proliferation rate and expansion of the MuSCs would be useful but not provided.

Thanks for your comment. The analysis of cell proliferation was added in Figure 1 (Fig. 1h).

The murine cell differentiation assays are not as convincing as the human study. The assay regarding "mouse muscle CD29+/CD56+ cells were isolated for tenogenic induction. However, very few mouse muscle CD29+/CD56+ cells expressed myogenic progenitor cell marker Pax7, MyoD1 and Vcam1" does not add any value to the work as those markers are not mouse MuSC markers to start with.

Thanks for your comment. The experiments concerning mouse muscle CD29+/CD56+ cells have been deleted to avoid misleading.

The Pax7-cre-TdTomato assay was also not convincing, as a negative finding may not be the best proof of absence.

Thanks for your comment. Pax7 positive cells could consistently express TdTomato for lineage tracing. In current study, large amount of tdTomato+ myofibers were observed after muscle injury (SFig. 2c-d), suggesting that the tracing system works well. However, less than 0.2% tendon cells originated from TdTomato+ MuSCs were observed even four months after tendon removal (Fig. 4f-g). When comparing in vivo data between murine MuSCs and human CD29+/CD56+ myogenic progenitors, we believe these data could indicate the poor tendon differentiation abilities of murine MuSCs.

(5) TGFb as a pathway of smad2/3 mediated tenocyte differentiation assays were well done albeit not novel. Using TGFb universal inhibitor may not accurately state the pathways were due to SMAD2/3 inhibition either.

We agree with your comment and the conclusion concerning SMAD2/3 has been deleted throughout the manuscript.

The paper also needs thorough proofreading. Currently, typographic, grammatical, and logical sequences of writing do not lend the paper to easy reading.

(1) Figure 1K and 1I have similar legends but presumably K is referring to MuSC and I is referring to differentiated cells.

(2) Tenogenic and myogenic induction should be changed to tenogenic/myogenic differentiation as they are the cells at the end of differentiation.

(3) Figure 6, it is not clear how the "human cells" are calculated in this assay.

Thanks for your constructive comment. (1) The figure legends in Figure1 have been revised (Line 797-804).  (2) Tenogenic and myogenic induction have been changed to tenogenic/myogenic differentiation manuscript when they are referring to cells at the end of differentiation (Fig.1, Fig.2, Fig.3, Fig.4, Fig.7 and SFig.1). (3) In Figure 6, “human cells” is referring to those injured tendons with transplantation of human CD29+/CD56+ myogenic progenitors. To evaluate the function of human CD29+/CD56+ myogenic progenitors, PBS group was set as negative control and uninjured group was set as normal control.

Reviewer #3 (Recommendations For The Authors):

(1) The full extent of the differentiation potential of CD29+/CD56+ stem/progenitor cells has not been thoroughly evaluated. There can also exist heterotopic ossification in injured tendon sites. Thus, it remains unclear whether these cells are truly bipotent as the authors claim, or can they differentiate into chondrocytes and osteoblasts.

Thanks for your comment. The current study focused on the tenogenic differentiation potential of CD29+/CD56+ myogenic progenitors, so the research priority was the bipotential ability of CD29+/CD56+ myogenic progenitors. We agree with you that chondrogenic and osteogenic ability of CD29+/CD56+ myogenic progenitors is also important and would investigate it in the further study.

(2) In Figure 3, the GO analysis also shows increased enrichment of muscle-related terms including muscle contraction and filament. Please clarify it.

The tenogenic differentiation efficiency of CD29+/CD56+ myogenic progenitors was about 40% in clonal assay. Some cells would myogenically differentiated under this tenogenic induction system. Thus, the GO analysis could also enrich muscle related terms including muscle contraction and filament.

(3) The authors use TNC staining to evaluate cell transplantation. My concern is whether the TNC expression is specific to the tendon site, or do engrafted human cells also express TNC in other sites such as muscle?

TNC is one of a well-known tendon-related markers. As you can see in Figure 6b and Figure 6c, although some human cells (labeled by Lamin A/C) were engrafted in muscle tissue area (labeled by MyHC), these engrafted human cells didn’t express TNC in muscle. In addition, we also used tendon related markers SCX and TNMD to confirm the tenogenic differentiation ability of engrafted human cells in vivo (SFig. 3a and 3b).

(4) The authors demonstrate that CD29+/CD56+ human stem/progenitor cells could efficiently transplant and contribute to myofiber regeneration in vivo. However, why were only a few transplanted human cells differentiating into myofiber (labeled by MyHC) in the tenon injury model even with CTX injection?

Thanks for your comment. Since skeletal muscle is able to regenerate with in situ muscle progenitor cells, regeneration of injured muscle by CTX injection was dependent on not only CD29+/CD56+ myogenic progenitors, but also native murine MuSCs. Thus, it is reasonable that there were only a few transplanted human cells differentiating into myofiber (labeled by MyHC) in the tenon injury model even with CTX injection.

(5) Figure 7 shows the crucial role of TGFB/SMAD signaling for the tenogenesis of human CD29+/CD56+ stem/progenitor cells. However, can TGFB/SMAD signaling activation facilitate the tenogenic differentiation of mouse MuSCs? This point is crucial to clarify the difference of MuSCs between different species.

Thanks for your valuable suggestion. We did a series of pilot assays to investigate the effect of TGFβ signaling activation to facilitate tenogenic differentiation of mouse MuSCs (Author response image 1). As you can see, activating TGFβ by SRI-011381 could slightly increase the expression of tenogenic markers of murine MuSCs. It’s an interesting topic and we would investigate it in the further study.

Author response image 1.

TGFβ signaling pathway slightly elevated tenogenic differentiation ability of murine MuSCs (a) Immunofluorescence staining of tendon marker Scx and Tnc in murine MuSCs induced for tenogenic differentiation with or without TGFβ signaling pathway agonist SRI-011381, respectively. Scale bars, 50 µm. (b) Quantification of Scx and Tnc fluorescent intensity in murine MuSCs undergone tenogenic induction with or without TGFβ signaling pathway agonist SRI-011381, respectively. Error bars indicated standard deviation (n=5). (c) Protein levels of Tnc and Scx. Murine MuSCs were induced towards tenogenic differentiation with or without TGFβ signaling pathway agonist SRI-011381. Total protein was extracted from cells before and after differentiation and subjected for Tnc and Scx immunoblotting. GAPDH was served as loading control.

(6) Please quantify the WB blot data throughout the manuscript.

Thanks for your comment. The WB blot data has been quantified throughout the manuscript.

(7) The data of RT-qPCR should indicate what the fold changes in relative to throughout the manuscript.

Thanks for your comment. The sentence “GAPDH was served as reference gene” was added in the figure legends to illustrate RT-qPCR results.

eLife Assessment

This study presents a useful theoretical model of molecular evolution of multi-copy gene systems by extending the classic Haldane model and applies the model to explain the surprisingly rapid evolution of rRNA genes. Although the conceptual model is intuitive and provides a new perspective for contextualizing this problem, the model presented does not adequately consider plausible biological constraints on the molecular and genetic processes. The lack of such constraints in the model, along with technical issues in the data analysis, provide incomplete support for the conclusion that the genetic variation patterns of rRNA genes in mouse is compatible with neutral evolution.

Reviewer #1 (Public review):

The fundamental claim of the manuscript is that rRNA genes experience substitutions much too quickly, given that they are a multi-copy gene system. As clarified by the authors in their response, and as I think is relatively clear in the manuscript, they are collapsing all copies of the rRNA array down. They first quantify polymorphism (in this expanded definition, where polymorphism means variable at a given site across any copy). The authors find elevated levels of heterozygosity in rRNA genes compared to single copy genes, which isn't surprising, given that there is a substantially higher target size; that being said, the increase in polymorphism is smaller than the increase in target size. They then look at substitutions between mouse species and also between human and chimp, and argue that the substitution rate is too fast compared to single copy genes in many cases.

[Editors' note: we invite readers to consult the review in full from the previous version of the submission: https://doi.org/10.7554/eLife.99992.2.sa1]

Reviewer #2 (Public review):

This revision has further improved the clarity of the paper, better articulating assumptions of the model and data analysis. I particularly appreciate the authors' thorough response to eLife assessment. However, the authors did not provide point-by-point response to the specific comments I had from last round of review and didn't revise the manuscript accordingly, so my major concerns remain.

At conceptual level, my biggest concern with the model is the lack of constraint on V*(K), which makes the null neutral model too "liberal". On the one hand, the number of descendants of each gene copy must be non-negative; on the other hand, even homogenizing process within an individual is extremely strong, it cannot "spread" gene copies across individuals, so the maximum number of descendants of one gene copy cannot exceed the number of offspring that individual has times C. For these reasons, I believe there must be a theoretical upper bound of the value of V*(K), and the actual V*(K) is likely much smaller under realistic strength of the homogenizing process. When I asked about modeling of the underlying homogenizing process, I did not mean the authors need to include specific molecular process in the model; instead, I am asking the authors to provide some realistic scenarios that can give rise to very large V*(K) values. As a result of the very "liberal" neutral model, although I do agree that rejection of null provides stronger evidence for selection in human, it is unclear whether there is no evidence of selection in mouse. Please see below for my specific comments regarding the definition and assumptions of V*(K) (copied from last review).

Regarding the data analysis, although I understand the authors' methodology and rationale behind, I am not convinced that high sequence similarity between rDNA copies guarantees no biases in alignment and variant calling. Furthermore, given divergence between species, I am particularly concerned about the practice of aligning reads of different species to human and mus musculus reference sequences. A separate issue is the calculation of divergence level. Instead of using Fst>0.8 as the criterion of calling fixed sites, the authors could calculate the pairwise average divergence between a random copy from one species and a random copy from another species. Mathematically, this could be calculated as p1(1-p2)+p2(1-p1). The observation that the estimated substitution rates for rDNA with and without CpG sites are so close seems to be an indication of technical error. Please also see below for my specific questions about data analysis (copied from last round of review).

Specific comments from last round of review:

Questions regarding V*(K)<br /> (1) Another key parameter V*(K) was still not defined within the paper. In response 9, the authors explained that V*(K) refers to "the number of progeny to whom the gene copy of interest is transmitted (K) over a specific time interval". However, the meaning of "progeny" remains unclear. Are the authors referring to the descendent copies of a gene copy, or the offspring individuals (i.e., the living organisms)? For example, if a variant spreads horizontally through homogenizing processes and transmits vertically to multiple offspring individuals, the number of descent gene copies could differ substantially from the number of descendent individuals to whom a gene copy is transmitted to. This distinction needs to be clarified and clearly stated in the paper.

(2) The authors state that V*(K)>=1 for rDNA genes because of the homogenizing processes (lines 139-141) without providing justification. It is unclear, at least to me, whether homogenizing processes are expected increase or decrease the variance in "reproductive success" across gene copies. Moreover, the authors claim that V*(K) "can potentially reach values in the hundreds and may even exceed C, resulting in C*=C/V*(K)<1" (Response 7). This claim is unlikely to be true, as the minimum value of K is bounded by zero and E(K) is assumed to be 1. Even in the extreme case that 1% gene copies leave large numbers of descends while the others leave none, V*(K) would still be less than 100. Such extreme case seems highly improbable, given realistic rates of the homogenizing processes.

(3) Regardless of how the authors define V*(K), it is not immediately clear why Equation 1 (N*=NC/V*(K)) holds. Both sides of the equation have their independent meanings, so the authors need to provide a step-by-step derivation demonstrating that they are equal. Only by doing this will the implicit underlying assumptions become clearer. I also strongly recommend that the authors conduct forward-in-time simulations with fixed N, C, V*(K) (however they define it) and μ to confirm that the right side of Equation 1 actually predicts the N* as calculated from the polymorphism level using the equation in line 165.

Questions about Ne* for multi-copy system

(1) While Ne is clearly defined in the standard single-copy gene model as the reciprocal of genetic drift (i.e., the decay in heterozygosity), its meaning for multiple-copy genes is unclear. Based on the context, it appears that the authors define Ne as the parameter that fits the population polymorphism level (Hs) using the equation in line 165. This definition is reasonable, but it should be explicitly clarified in the text."

(2) Without providing justification, the authors assumed that a certain number N* exists for rRNA such that it fits both the polymorphism level (line 156) in recent timescales and divergence level in longer timescales (i.e., in the comparison between Tf and Td). However, if N, C or any other relevant parameters have varied substantially throughout evolution, N* is expected to vary with time, and the same value may not fit both polymorphism and divergence data simultaneously.

Questions about data analysis

(1) A significant issue with aligning reads to a single reference genome is reference bias, referring to the phenomenon that reads carrying the reference alleles tend to align more easily than those with one or more non-reference alleles, thus creating a bias in genotype calling or variant allele frequency quantification. As a result, there may be an underrepresentation of non-reference alleles in called variants or an underestimate of non-reference allele frequency, particularly in regions with high genetic diversity. Simply focusing on bi-allelic SNVs is insufficient to minimize reference bias. Given the fourfold increase in diversity within rDNA, the authors must either provide evidence that reference bias is not a significant concern or adopt graph-based reference genomes or more sophisticated alignment algorithms to address this issue.

(2) The potential for reference bias also renders the analysis of divergence sites unreliable, as aligning reads from one species (e.g. chimpanzee) to the reference of another species (e.g., human) is likely to introduce biases in variant calling between the two. One commonly adopted approach to address this imbalance is to align reads from both species to a third reference genome that is expected to be equidistantly related to both.

(3) Although it is somewhat reassuring that the estimated divergence rate of rDNA between human and macaque is comparable to that of the rest of the genome, there still remains concern of a under-estimation of divergence in rDNA regions due to reference bias issue. Note that while the "third genome" approach reduces imbalance between two genomes in comparison, it may still under-estimate overall divergence level due to under-calling of non-reference variants.<br /> (4) In response to my question about the similarity in rDNA substitution rates estimated with or without CpG sites, the authors suggest that this "may be due to strong homogenizing forces, which can rapidly fix or eliminate variants" (response17). However, this explanation is insufficient, because the observed substitution rate depends on the mutation rate multiplied by the fixation probability, and accelerated fixation or loss does not alter either. Unless the authors can provide more convincing explanation, technical errors in calling of fixed sites still remain a concern.

Minor points:

Line 157: The statement "where μ is the mutation rate of the entire gene" must be wrong, as the heterozygosity calculated with such μ would correspond to the chance of seeing two different haplotypes at gene level, which is incompatible with the empirical calculation specified in Equation 2. Instead, μ must represent the mutation rate per site averaged over the entire gene.

In response 22, the authors explained that the allele frequency spectrum shown in Fig 3 is folded, because the ancestral allele was not determined. However, this is inconsistent with x-axis Fig 3 ranging between 0 and 1. I suspect the x-axis represents the frequency of the alternative (i.e., non-reference) allele. If so, the reported correlation is inflated, as the reference allele is somewhat random, and a variant at joint ALT allele frequencies of (0.9, 0.9) is no different from a variant at (0.1, 0.1). The proper way of calculate this correlation is to first determine the minor allele frequency across individuals and then calculate the correlation between minor allele frequencies.

Similarly, in response 14, it is unclear what the x-axis represents. Is it the ALT allele frequency or derived allele frequency? If the former, why are only variants with AF>0.8 defined as fixed variants, while those with AF<0.2 excluded? If it is the latter, please describe how ancestral state is determined.

Author response:

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

eLife Assessment<br /> …. While intuitive, the model's underlying issue is grouping many factors under "variance in reproductive success" without explicitly modeling the molecular processes. This limitation, …, provides incomplete support for the authors' claim that the observed paradoxical patterns in rRNA genes can largely be explained by homogenizing processes, such as gene conversion, unequal crossover and replication slippage.

This second paper addresses the genetic drift in multi-copy gene systems using rRNA genes as an example. Note that genetic drift happens in two stages here – within individuals and between individuals while the drift mechanisms are very different between the two stages. We now reply to the editors’ decision that it would be more rigorous to model each molecular process, than to lump all stochastic forces into V(K).  We respond to this criticism on three fronts.

First, for molecular evolutionists, there is NO NEED to model the detailed molecular processes.  This is because we are only interested in knowing the totality of the stochastic variations.  Interesting biological forces such as selection and meiotic drive are masked by such random forces. Our objective is precisely to lump all noises into a quantity that can be estimated.

Second, the homogenization process is the bulk, if not the totality of the within-individual random forces (i.e,, genetic drift). The criticism of incomplete support for drift as a sufficient account of the observations is curious because we did conclude that genetic drift is an insufficient explanation of the human data.  Since drift only influences fixation time, which can have a significant effect in short-term evolution (as shown in Fig 2), but it does not affect fixation rate itself. In contrast, selection influences the both. Thus, we can define the limitation of drift in evolutionary process. Even if the speed of drift-driven fixation is only a few generations, it is still too little for the human-chimpanzee divergence comparisons. In contrast, the speed of genetic drift in mice, as extrapolated from the polymorphism data, is sufficient to drive the divergence between M. m. domesticus and Mus spretus. The criticism appears to be that unbiased gene conversion, unequal crossover and replication slippage together may be insufficient to account for the observations. Since the contribution of each of these three forces is not central to our goal of filtering out the total contributions, we only conclude that the totality of within-individual drift in mice is sufficient to explain the data.

Third, even if we really want to dissect the molecular processes, previous attempts by prominent theorists like Tom Nagylaki and Tomoko Ohta could only model a small subset of such processes.  In fact, Ohta often lumps a few of these forces into one process. More importantly, if we want to tackle other systems like viruses and mitochondria, we will have to develop a new set of theories for each molecular process.  V(K) can take care of all such diverse systemes.  In short, genetic drift is just noises and our goal is to quantify them in total across diverse systmes.  By filtering out noises, we will be able to move on to something more important.

We now briefly comment on the WF models in relation to multi-gene systems. For example, in the case SARS-CoV-2, there are millions of virions in each patient among millions of patients. It is not possible to know what Ne acaully means in the WF modesl. Also, the rDNA population in each individual is not the sub-populations of the WF models.  After all, the mechanisms of genetic drift within individuals by the homogenization processes are entirely different from the genetic drift between individuals.  For a comparison, we published several papers (cited in #2) using the Haldane model to estimate the strength of genetic drift. It is also important to note that the parameters and assumptions of WF model cannot fully capture the evolutionary dynamics of the multi-copy genes.

… ., along with insufficient consideration of technical challenges in alignment and variants calling, provides incomplete support for the authors' claim …

Before delving into the technical details, we would like to summarize our defense. First, all rRNA gene copies belong in a pseudo-population, due to the homogenization process. The concept of specific locus with specific variants does not apply. Second, the levels of within-individual and within-species variation is so low that sequence alignment is not a problem at all. Third, thanks to the large number of sequence reads, occasional sequence errors (rarely encountered) should have minimal effects on the analyses.  Now the technical details:

Regarding the concerns about the alignment and variant calling, we would like to clarify our methodology. While we acknowledge the technical challenges inherent in alignment and variant calling, particularly with respect to orthologous alignments to distinguish different copies, it is important to note that rDNA copies are subject to homogenization processes, meaning that there is no orthology among rDNA copies. Due to the high sequence similarity and frequent genetic exchange among rDNA units within species, we used the species-specific rDNA reference sequence for variant calling. We directly utilized the raw read depth from all rDNA copies within individuals to calculate the site frequency. For each site, we focused on the frequency of the major allele to calculate nucleotide diversity using the 2p(1-p), where p represents the frequency of the major allele. This approach helps capture genetic variation while minimizing the impact of alignment or variant calling errors, which primarily affect low-frequency variants (e.g., 0.800A, 0.199T, 0.001C, with A being the major allele). As for the divergence sites between species, we defined  FST = 0.8 as a cutoff (roughly, when a mutant is > 0.95 in frequency in one species and < 0.05 in the other, FST would be > 0.80.),  which is less likely to be influenced by low-frequency polymorphic sites within species.We believe this method is more appropriate for estimating genetic diversity at rDNA than traditional variant calling pipelines designed to detect homozygotes and heterozygotes.

eLife Assessment

This study presents a useful model of genetic drift by incorporating variance in reproductive success, aiming to address several apparent paradoxes in molecular evolution. However, some of the apparent paradoxes only arise in the most basic version of standard models and have been reconciled in more advanced models. Nonetheless, this paper offers intuitive explanations for these apparent paradoxes, by adopting a new perspective and solid modeling and analysis. More broadly, the proposed model provides an alternative framework to address puzzling observations in molecular evolution, which will be of interest to evolutionary and population geneticists.

Reviewer #1 (Public review):

The revision by Ruan et al clarifies several aspects of the original manuscript that were difficult to understand, and I think it presents some useful and interesting ideas. I understand that the authors are distinguishing their model from the standard Wright-Fisher model in that the population size is not imposed externally, but is instead a consequence of the stochastic reproduction scheme. Here, the authors chose a branching process but in principle any Markov chain can probably be used. Within this framework, the authors are particularly interested in cases where the variance in reproductive success changes through time, as explored by the DDH model, for example. They argue with some experimental results that there is a reason to believe that the variance in reproductive success does change over time.

One of the key aspects of the original manuscript that I want to engage with is the DDH model. As the authors point out, their equations 5 and 6 are assumptions, and not derived from any principles. In essence, the authors are positing that that the variance in reproductive success, given by 6, changes as a function of the current population size. There is nothing "inherent" to a negative binomial branching mechanism that results in this: in fact, the the variance in offspring number could in principle be the same for all time. As relates to models that exist in the literature, I believe that this is the key difference: unlike Cannings models, the authors allow for a changing variance in reproduction through time.

This is, of course, an interesting thing to consider, and I think that the situation the authors point out, in which drift is lower at small population sizes and larger at large population sizes, is not appreciated in the literature. However, I am not so sure that there is anything that needs to be resolved in Paradox 1. A very strong prediction of that model is that Ne and N could be inversely related, as shown by the blue line in Fig 3b. This suggests that you could see something very strange if you, for example, infer a population size history using a Wright-Fisher framework, because you would infer a population *decline* when there is in fact a population *expansion*. However, as far as I know there are very few "surprising population declines" found in empirical data. An obvious case where we know there is very rapid population growth is human populations; I don't think I've ever seen an inference of recent human demographic history from genetic data that suggests anything other than a massive population expansion. While I appreciate the authors empirical data supporting their claim of Paradox 1 (more on the empirical data later), it's not clear to me that there's a "paradox" in the literature that needs explaining so much as this is a "words of caution about interpreting inferred effective population sizes". To be clear, I think those words of caution are important, and I had never considered that you might be so fundamentally misled as to infer decline when there is growth, but calling it a "paradox" seems to suggest that this is an outstanding problem in the literature, when in fact I think the authors are raising a *new* and important problem. Perhaps an interesting thing for the authors to do to raise the salience of this point would be to perform simulations under this model and then infer effective population sizes using e.g. dadi or psmc and show that you could identify a situation in which the true history is one of growth, but the best fit would be one of decline

The authors also highlight that their approach reflects a case where the population size is determined by the population dynamics themselves, as opposed to being imposed externally as is typical in Cannings models. I agree with the authors that this aspect of population regulation is understudied. Nonetheless, several manuscripts have dealt with the case of population genetic dynamics in populations of stochastically fluctuating size. For example, Kaj and Krone (2003) show that under pretty general conditions you get something very much like a standard coalescent; for example, combining their theorem 1 with their arguments on page 36 and 37, they find that exchangeable populations with stochastic population dynamics where the variance does not change with time still converge to exactly the coalescent you would expect from Cannings models. This is strongly suggestive that the authors key result isn't about stochastic population dynamics per se, but instead related to arguing that variance in reproductive success could change through time. In fact, I believe that the result of Kaj and Krone (2003) is substantially more general than the models considered in this manuscript. That being said, I believe that the authors of this manuscript do a much better job of making the implications for evolutionary processes clear than Kaj and Krone, which is important---it's very difficult to understand from Kaj and Krone the conditions under which effective population sizes will be substantially impacted by stochastic population dynamics.

I also find the authors exposition on Paradox 3 to be somewhat strange. First of all, I'm not sure there's a paradox there at all? The authors claim that the lack of dependence of the fixation probability on Ne is a paradox, but this is ultimately not surprising---fixation of a positively selected allele depends mostly on escaping the boundary layer, which doesn't really depend on the population size (see Gillespie's book "The Causes of Molecular Evolution" for great exposition on boundary layer effects). Moreover, the authors *use a Cannings-style argument* to get gain a good approximation of how the fixation probability changes when there is non-Poisson reproduction. So it's not clear that the WFH model is really doing a lot of work here. I suppose they raise the interesting point that the particularly simple form of p(fix) = 2s is due to the assumption that variance in offspring is equal to 1.

In addition, I raised some concerns about the analysis of empirical results on reproductive variance in my original review, and I don't believe that the authors responded to it at all. I'm not super worried about that analysis, but I think that the authors should probably respond to me.

Overall, I feel like I now have a better understanding of this manuscript. However, I think it still presents its results too strongly: Paradox 1 contains important words of caution that reflect what I am confident is an under appreciated possibility, and Paradox 3 is, as far as I'm concerned, not a paradox at all. I have not addressed Paradox 2 very much because I think that another reviewer had solid and interesting comments on that front and I am leaving it to them. That being said, I do think Paradox 2 actually presents a deep problem in the literature and that the authors' argument may actually represent a path toward a solution.

This manuscript can be a useful contribution to the literature, but as it's presented at the moment, I think most of it is worded too strongly and it continues to not engage appropriately with the literature. Theoretical advances are undoubtedly important, and I think the manuscript presents some interesting things to think about, but ultimately needs to be better situated and several of the claims strongly toned down.

References:<br /> Kaj, I., & Krone, S. M. (2003). The coalescent process in a population with stochastically varying size. Journal of Applied Probability, 40(1), 33-48.

Reviewer #2 (Public review):

Summary:

This theoretical paper examines genetic drift in scenarios deviating from the standard Wright-Fisher model. The authors discuss Haldane's branching process model, highlighting that the variance in reproductive success equates to genetic drift. By integrating the Wright-Fisher model with the Haldane model, the authors derive theoretical results that resolve paradoxes related to effective population size.

Strengths:

The most significant and compelling result from this paper is perhaps that the probability of fixing a new beneficial mutation is 2s/V(K). This is an intriguing and potentially generalizable discovery that could be applied to many different study systems.

The authors also made a lot of effort to connect theory with various real-world examples, such as genetic diversity in sex chromosomes and reproductive variance across different species.

Comments on previous revisions:

The author has addressed some of the concerns in my review, and I think the revised manuscript is more clear. I like the discussion about the caveats of the WFH model.

I hope the authors could also discuss the conditions needed for V(K)/Ne to be a reasonable approximation. It is currently unclear how the framework should be adopted in general.

The idea about estimating male-female V(K) ratios from population genetic data is interesting. Unfortunately, the results fell short. The accuracy of their estimators (derived using approximation Ne/V(K) approximation, and certain choice of theta, and then theta estimated with Watterson's estimator) should be tested with simulated results before applying to real data. The reliability of their estimator and their results from real data are unclear.

Arguments made in this paper sometimes lack precision (perhaps the authors want to emphasize intuition, but it seems more confusing than otherwise). For example: The authors stated that "This independence from N seems intuitively obvious: when an advantageous mutation increases to say, 100 copies in determining a population (depending mainly on s), its fixation would be almost certain, regardless of N.". Assuming large Ne, and with approximation, one could assume the probability of loss is e^(-2sn), but the writing about "100 copies" and "almost certain" is very imprecise, in fact, a mutation with s=0.001 segregating at 100 copies in a large Ne population is most probably lost. Whereas in a small population, it will be fixed. Yet the following sentence states "regardless of N. This may be a most direct argument against equating genetic drift, certainly no less important than 1/ N . with N, or Ne (which is supposed to be a function of N's)." I find this new paragraph misleading.

Some of the statements/wordings in this paper still seem too strong to me.

Comments on revisions:

The authors toned down. I am a bit confused because I do not seem to find any point-to-point response to my review.

Reviewer #3 (Public review):

Summary:

Ruan and colleagues consider a branching process model (in their terminology the "Haldane model") and the most basic Wright-Fisher model. They convincingly show that offspring distributions are usually non-Poissonian (as opposed to what's assumed in the Wright-Fisher model), and can depend on short-term ecological dynamics (e.g., variance in offspring number may be smaller during exponential growth). The authors discuss branching processes and the Wright-Fisher model in the context of 3 "paradoxes" --- 1) how Ne depends on N might depend on population dynamics; 2) how Ne is different on the X chromosome, the Y chromosome, and the autosomes, and these differences do match the expectations base on simple counts of the number of chromosomes in the populations; 3) how genetic drift interacts with selection. The authors provide some theoretical explanations for the role of variance in the offspring distribution in each of these three paradoxes. They also perform some experiments to directly measure the variance in offspring number, as well as perform some analyses of published data.

Strengths:

- The theoretical results are well-described and easy to follow.<br /> - The analyses of different variances in offspring number (both experimentally and analyzing public data) are convincing that non-Poissonian offspring distributions are the norm.<br /> - The point that this variance can change as the population size (or population dynamics) change is also very interesting and important to keep in mind.<br /> - I enjoyed the Density-Dependent Haldane model. It was a nice example of the decoupling of census size and effective size.<br /> - Equation (10) is a nice result

Comments on revisions:

I appreciate the effort that the authors have put into the revision, but I still find the framing to be a bit confusing -- these apparent paradoxes only appear in the most basic version of Wright-Fisher models, and so framing the paper as the solution to these paradoxes overlooks much previous work. Saying that existing work discussing exactly these phenomena is "beyond the scope of this study", without citing or interacting in any way with that work is unscholarly. I agree with the authors that the apparent paradoxes that they consider and interesting, and by thinking about branching processes, the apparent paradoxes appear to be less paradoxical, but without contextualizing this work in the substantial Wright-Fisher literature (e.g., Cannings Exchangeable Models and the work of Möhle) it misrepresents the state of the field and the contributions of this paper.

Author response:

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

eLife Assessment (divided into 3 parts)

This study presents a useful modification of a standard model of genetic drift by incorporating variance in reproductive success, claiming to address several paradoxes in molecular evolution. ……

It is crucial to emphasize that our model is NOT a modification of the standard model. The Haldane model, which is generalized here for population regulation, is based on the branching process. The Haldane model and the WF model which is based on population sampling are fundamentally different. We referred to our model as the integrated WF-H model because the results obtained from the WF model over the last 90 years are often (but not always) good approximations for the Haldane model. The analogy would be the comparisons between the Diffusion model and the Coalescence model. Obviously, the results from one model are often good approximations for the other.  But it is not right to say that one is a useful modification of the other.

We realize that it is a mistake to call our model the integrated WFH model, thus causing confusions over two entirely different models. Clearly, the word “integrated” did not help. We have now revised the paper by using the more accurate name for the model – the Generalized Haldane (GH) model. The text explains clerarly that the original Haldane model is a special case of the GH model.

Furthermore, we present the paradoxes and resolve them by the GH model.  We indeed overreached by claiming that WF models could not resolve them. Whether the WF models have done enough to resolve the paradoxes or at least will be able to resolve them should not be a central point of our study. Here is what we state at the end of this study.:

“We understand that further modifications of the WF models may account for some or all of these paradoxes. However, such modifications have to be biologically feasible and, if possible, intuitively straightforward. Such possible elaborations of WF models are beyond the scope of this study. We are only suggesting that the Haldane model can be extensively generalized to be an alternative approach to genetic drift. The GH model attempts to integrate population genetics and ecology and, thus, can be applied to genetic systems far more complex than those studied before. The companion study is one such example.”

….. However, some of the claimed "paradoxes" seem to be overstatements, as previous literature has pointed out the limitations of the standard model and proposed more advanced models to address those limitations….

As stated in the last paragraph of the paper, it is outside of the scope of our study to comment on whether the earlier WF models can resolve these paradoxes.  So, all such statements have been removed or at least drastically toned down in the formal presentation.  That said, editors and reviewers may ask whether we are re-inventing the wheels.  The answers are as follows:

First, two entirely different models reaching the same conclusion are NOT the re-invention of wheels. The coalescence theory does not merely rediscover the results obtained by the diffusion models. The process of obtaining the results is itself a new invention.  This would lead to the next question: is the new process more rigorous and more efficient?  I think the Haldane model is indeed more efficient in comparisons with the very complex modifications of the WF models. 

Second, we are not sure that the paradoxes have been resolved, or even can be resolved.  Note that these skepticisms have been purged from the formal presentation. Thefore, I am presenting the arguments outside of the paper for a purely intellectual discourse. Below, please allow us to address the assertions that the WF models can resolve the paradoxes. 

The first paradox is that the drift strength in relation to N is often opposite of the WF model predictions.  Since the WF models (standard or modified) do not generate N from within the model, how can it resolve the paradox?  In contrast, the Generalized Haldane model generates N within the model. It is the regulation of N near the carrying capacity that creates the paradox – When N increases, drift also increases.

The second paradox that the same locus experiences different drifts in males and females is accepted by the reviewers.  Nevertheless, we would like to point out that this second paradox echoed the first one as newly stated in the Discussion section “The second paradox of sex-dependent drift is about different V(K)’s between sexes (generally Vm > Vf) but the same E(K) between them. In the conventional models of sampling, it is not clear what sort of biological sampling scheme could yield V(K) ≠ E(K), let alone two separate V(K)’s with one single E(K). Mathematically, given separate K distributions for males and females, it is unlikely that E(K) for the whole population could be 1, hence, the population would either explode in size or decline to zero. In short, N regulation has to be built into the genetic drift model as the GH model does to avoid this paradox.”

The third paradox stems from the fact that drift is operating even for genes under selection. But then the drift strength, 2s/V(K) for an advantage of s, is indepenent of N or Ne. Since the determinant of drift strength in the WF model is ALWAYS Ne, how is Paradox 3 not a paradox for the WF model?

The 4th paradox about multi-copy gene systems is the subject of the companion paper (Wang et al.). Note that the WF model cannot handle systems of evolution that experience totally different sorts of drift within vs. between hosts (viruses, rDNAs etc).  This paradox can be understood by the GH model and and will be addressed in the next paper.

While the modified model presented in this paper yields some intriguing theoretical predictions, the analysis and simulations presented are incomplete to support the authors' strong claims, and it is unclear how much the model helps explain empirical observations.

The objections appear to be that our claims of “paradox resolution” being too strong.  We interpret this objection is based on the view (which we agree) that these paradoxes are intrisicallly difficult to resolve by the WF models. Since our model has been perceived to be a modified WF model, the claim of resolution is clearly too strong.  However, the GH model is conceptually and operationally entirely different from the WF models as we have emphasized above. In case our reading of the editorial comments is incorrect, would it be possible for some clarifications on the nature of “incomplete support”?  We would be grateful for the help.

eLife Assessment

This important study presents a method to visualize the location of the cell types discovered through single-cell RNA sequencing. The data allowed the authors to build spatial tissue atlases of the fly head and body, and to identify the location of previously unknown cell types. The data are convincing and appropriate, and the authors validate the methodology in line with the current state-of-the-art.

Reviewer #1 (Public review):

Summary:

In this manuscript, Janssens et al. addressed the challenge of mapping the location of transcriptionally unique cell types identified by single nuclei sequencing (snRNA-seq) data available through the Fly Cell Atlas. They identified 100 transcripts for head samples and 50 transcripts for fly body samples allowing identification of every unique cell type discovered through the Fly Cell Atlas. To map all of these cell types, the authors divided the fly body into head and body samples and used the Molecular Cartography (Resolve Biosciences) method to visualize these transcripts. This approach allowed them to build spatial tissue atlases of the fly head and body, to identify the location of previously unknown cell types and the subcellular localization of different transcripts. By combining snRNA-seq data from the Fly Cell Atlas with their spatially resolved transcriptomics (SRT) data, they demonstrated an automated cell type annotation strategy to identify uncharacterized clusters and infer their location in the fly body. This manuscript constitutes a proof-of-principle study to map the location of the cells identified by ever-growing single-cell transcriptomics datasets generated by others.

Strengths:

The authors used the Molecular Cartography (Resolve Biosciences) method to visualize 100 transcripts for head samples and 50 transcripts for fly body samples in high resolution. This method achieves high resolution by multiplexing a large number of transcript visualization steps and allows the authors to map the location of unique cell types identified by the Fly Cell Atlas.

Weaknesses:

Combining single-nuclei sequencing (snRNA-seq) data with spatially resolved transcriptomics (SRT) data is challenging, and the methods used by the authors in this study cannot reliably distinguish between cells, especially in brain regions where the processes of different neurons are clustered, such as neuropils. This means that a grid that the authors mark as a unique cell may actually be composed of processes from multiple cells.

Comments on revisions:

I believe the authors have improved the manuscript by addressing all the concerns and incorporating the suggestions raised by the reviewers. I have no further concerns or suggestions.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Janssens et al. addressed the challenge of mapping the location of transcriptionally unique cell types identified by single nuclei sequencing (snRNA-seq) data available through the Fly Cell Atlas. They identified 100 transcripts for head samples and 50 transcripts for fly body samples allowing the identification of every unique cell type discovered through the Fly Cell Atlas. To map all of these cell types, the authors divided the fly body into head and body samples and used the Molecular Cartography (Resolve Biosciences) method to visualize these transcripts. This approach allowed them to build spatial tissue atlases of the fly head and body, to identify the location of previously unknown cell types and the subcellular localization of different transcripts. By combining snRNA-seq data from the Fly Cell Atlas with their spatially resolved transcriptomics (SRT) data, they demonstrated an automated cell type annotation strategy to identify unknown clusters and infer their location in the fly body. This manuscript constitutes a proof-of-principle study to map the location of the cells identified by ever-growing single-cell transcriptomic datasets generated by others.

Strengths:

The authors used the Molecular Cartography (Resolve Biosciences) method to visualize 100 transcripts for head samples and 50 transcripts for fly body samples in high resolution. This method achieves high resolution by multiplexing a large number of transcript visualization steps and allows the authors to map the location of unique cell types identified by the Fly Cell Atlas. 

We thank this reviewer for appreciating the quality of our spatial data. We do not know what caused the technical problem (grayscale version of PDF) for this reviewer (the PDF figures are in color on the eLife website and on bioRxiv). We are surprised that the eLife discussion session did not resolve this issue.

Weaknesses:

Combining single-nuclei sequencing (snRNA-seq) data with spatially resolved transcriptomics (SRT) data is challenging, and the methods used by the authors in this study cannot reliably distinguish between cells, especially in brain regions where the processes of different neurons are clustered, such as in neuropils. This means that a grid that the authors mark as a unique cell may actually be composed of processes from multiple cells. 

The small size of an individual fly is one of the most challenging aspects of performing spatial transcriptomics. While the resolution of Molecular Cartography is rather high (< 200 nm), in the brain challenges remain as noted by the reviewer. Drosophila neuronal nuclei are notoriously small and cannot be easily resolved with the current imaging techniques. We agree that for a full atlas either expansion microscopy, 3D techniques or other super-resolution techniques will be required. 

Reviewer #2 (Public Review):

Summary:

The landmark publication of the "Fly Atlas" in 2022 provided a single cell/nuclear transcriptomic dataset from 15 individually dissected tissues, the entire head, and the body of male and female flies. These data led to the annotation of more than 250 cell types. While certainly a powerful and datarich approach, a significant step forward relies on mapping these data back to the organism in time and space. The goal of this manuscript is to map 150 transcripts defined by the Fly Atlas by FISH and in doing so, provide, for the first time, a spatial transcriptomic dataset of the adult fly. Using this approach (Molecular Cartography with Resolve Biosciences), the authors, furthermore, distinguish different RNA localizations within a cell type. In addition, they seek to use this approach to define previously unannotated clusters found in the Fly Atlas. As a resource for the community at large interested in the computational aspects of their pipeline, the authors compare the strengths and weaknesses of their approach to others currently being performed in the field.

Strengths:

(1) The authors use Resolve Biosciences and a novel bioinformatics approach to generate a FISHbased spatial transcriptomics map. To achieve this map, they selected 150 genes (50 body; 100 head) that were highly expressed in the single nuclear RNA sequencing dataset and were used in the 2022 paper to annotate specific cell types; moreover, the authors chose several highly expressed genes characteristic of unannotated cell types. Together, the approach and generated data are important next steps in translating the transcriptomic data to spatial data in the organism.

We thank the reviewer for this comment, as it reminded us that we need to be clearer in the text, about how we chose the genes to investigate. The statement that we selected “150 genes (50 body; 100 head) that were highly expressed in the single nuclear RNA sequencing dataset” is not correct. We have chosen genes with widely differing expression levels (log-scale range of 3.95 in body, 5.76 in head, we show this now in the new Figure 1 – figure fupplement 1B, D). Many of the chosen genes are also transcription factors. In fact, the here introduced method is more sensitive than the single cell atlas: the tinman positive cells were readily located (even non-heart cells were found to express tinman), whereas in the single cell FCA data tinman expression is often not detected in the cardiomyocytes (tinman is detected in 273 cells in the entire FCA (mean expression of 1.44 UMI in positive cells), and in 71 cells out of 273 cardiac cells (26%)). 

(2) Working with Resolve, the authors developed a relatively high throughput approach to analyze the location of transcripts in Drosophila adults. This approach confirmed the identification of particular cell types suggested by the FlyAtlas as well as revealed interesting subcellular locations of the transcripts within the cell/tissue type. In addition, the authors used co-expression of different RNAs to unbiasedly identify "new cell types". This pipeline and data provide a roadmap for additional analyses of other time points, female flies, specific mutants, etc.

(3) The authors show that their approach reveals interesting patterns of mRNA distribution (e.g alpha- and beta-Trypsin in apical and basal regions of gut enterocytes or striped patterns of different sarcomeric proteins in body muscle). These observations are novel and reveal unexpected patterns. Likewise, the authors use their more extensive head database to identify the location of cells in the brain. They report the resolution of 23 clusters suggested by the single-cell sequencing data, given their unsupervised clustering approach. This identification supports the use of spatial cell transcriptomics to characterize cell types (or cell states).

(4) Lastly, the authors compare three different approaches --- their own described in this manuscript, Tangram, and SpaGE - which allow integration of single cell/nuclear RNA-seq data with spatial localization FISH. This was a very helpful section as the authors compared the advantages and disadvantages (including practical issues, like computational time).

Weaknesses:

(1) Experimental setup. It is not clear how many and, for some of the data, the sex of the flies that were analyzed. It appears that for the body data, only one male was analyzed. For the heads, methods say male and female heads, but nothing is annotated in the figures. As such, it remains unclear how robust these data are, given such a limited sample from one sex. As such, the claims of a spatial atlas of the entire fly body and its head ("a rosetta stone") are overstated. Also, the authors should clearly state in the main text and figure legends the sex, the age, how many flies, and how many replicates contributed to the data presented (not just the methods). What also adds to the confusion is the use of "n" in para 2 of the results. " ... we performed coronal sections at different depths in the head (n=13)..." 13 sections in total from 1 head or sections from 13 heads? Based on the body and what is shown in the figure, one assumes 13 sections from one head. Please clarify.

While we agree that sex differences present indeed an interesting opportunity to study with spatial transcriptomics, our goal was not to define male/female differences but rather to establish the technology to go into this detail if wanted in the future. In the revised version, we have provided an additional supplementary table with a more detailed description of the head sections (Table S3). We have added the number of animals (12 for the head sections, mixed sex; and 1 male for the body sections) to the main text. We would like to point out that we verified the specificity of our MC method on all the 5 body sections (Figure 2A, TpnC4 & Act88F and text) and not only on one. Furthermore, we also would like to state that the idea of “a Rosetta stone” was mentioned as a future prospect that clearly goes beyond our presented work. We have rewritten the discussion to make this clearer and to any avoid overstatements.

(2) Probes selected: Information from the methods section should be put into the main text so that it is clear what and why the gene lists were selected. The current main text is confusing. If the authors want others to use their approach, then some testing or, at the very least, some discussion of lower expressed genes should be added. How useful will this approach be if only highly expressed genes can be resolved? In addition, while it is understood that the company has a propriety design algorithm for the probes, the authors should comment on whether the probes for individual genes detect all isoforms or subsets (exons and introns?), given the high level of splicing in tissues such as muscle.

As stated above, while there is a slight bias to higher expressed genes (as expected for marker genes), we have also used low expressed genes like salm, CG32121, tinman (body) or sens (head). This is now shown in new Figure 1 – figure Supplement 1B, D. This shows that our method is more sensitive than single-cell data, as all cardiomyocytes can be identified by tinman expression and not only some are positive, as is the case in the FCA data. In fact, the method cannot resolve too highly expressed genes due to optical crowding of the signal leading to a worse quantification. For this reason, ninaE was removed from the analysis (as mentioned in Spatial transcriptomics allows the localization of cell types in the head and brain and in Methods).

As mentioned in the Methods, the probes are designed on gene level targeting all isoforms, but favoring principal isoforms (weighted by APPRIS level). The high level of splicing is indeed interesting and we expect that in the future spatial transcriptomics can help to generate more insight into this by designing isoform-specific probes.

(3) Imaging: it isn't clear from the text whether the repeated rounds of imaging impacted data collection. In many of what appear to be "stitched" images, there are gradients of signal (eg, figure 2F); please comment. Also, since this a new technique, could a before and after comparison of the original images and the segmented images be shown in the supplemental data so that the reader can better appreciate how the authors assessed/chose/thresholded their data? More discussion of the accuracy of spot detection would be helpful. 

High-resolution imaging (pixel size = 138 nm) of a large field of view (>1mm) for spatial transcriptomics uses a stitching method to combine several individual images to reconstruct a large field of view. This does not generate signal gradients, apart from lower signal at the extreme edges of each of the individual images, as seen in our images, too. The spot detection algorithm was written and used by Resolve Biosciences and benchmarked for human (Hela) and mouse (NIH-3T3) cell lines in Groiss et al. 2021 (Highly resolved spatial transcriptomics for detection of rare events in cells, bioR xiv). The specificity of the decoded probes was found to lie between 99.45 and 99.9% here, matching the results we found for specific detection of TpnC4 and Act88F (99.4 and 99.8%).

(4) The authors comment on how many RNAs they detected (first paragraph of results). How do these numbers compare to the total mRNA present as detected by single-cell or single-nuclear sequencing?

We can compare the numbers, but the different methodologies make the interpretation of such a comparison difficult. FCA used single nucleus sequencing, so only nuclear pre-mRNAs are detected. The total amount of counts per single cell sample strongly depends on how many cells were sequenced in an experiment. MC detects all mRNAs present in the section. Here, the size of the sample and hence the size or the number of cells analyzed determines how many mRNAs are detected. In Author response image 1, we have compared our MC results versus FCA data, comparing the genes investigated here in MC per section vs per sequencing experiment. Numbers for MC are slightly lower for the brain (not all cell types are on all sections) and much higher for the larger body samples. However, we feel a direct comparison is questionable, so we prefer to not include this figure in our manuscript.

Author response image 1:

Barplots showing total number of mRNA molecules detected in Molecular Cartography (MC, Resolve, spatial spots) and in snRNA-seq data from the Fly Cell Atlas (10x Genomics, UMIs). Individual black dots show individual experiments, counts are only shown for the chosen gene panel for each sample. Bar shows the mean, with error bars representing the standard error.

(5) Using this higher throughput method of spatial transcriptomics, the authors discern different cell types and different localization patterns within a tissue/cell type.

a. The authors should comment on the resolution provided by this approach, in terms of the detection of populations of mRNAs detected by low throughput methods, for example, in glia, motor neuron axons, and trachea that populate muscle tissue. Are these found in the images? Please show.

We did not add any markers for trachea in our gene panel, but we do detect sparse spots of repo (glia) and elav/VGlut in the muscle tissues (Gad1/VAChT are hardly detected in the muscle tissue). This is consistent with the glutamatergic nature of motor neurons in Drosophila as described previously (Schuster CM (2006), Glutamatergic synapses of Drosophila neuromuscular junctions: a high-resolution model for the analysis of experience-dependent potentiation. Cell Tissue Res 326:

287–299.). We have present these new data in new Figure 2 – figure supplement 1.

b.The authors show interesting localization patterns in muscle tissue for different sarcomere proteincoding mRNAs, including enrichment of sls in muscle nuclei located near the muscle-tendon attachment sites. As this high throughput approach is newly being applied to the adult fly, it would increase confidence in these data, if the authors would confirm these data using a low throughput FISH technique. For example, do the authors detect such alternating "stripes" ( Act 88F, TpnC4, and Mhc) or enriched localization (sls) using FISH that doesn't rely on the repeated colorization, imaging, decolorization of the probes? 

We thank the reviewer for the interest in the localization patterns in muscle tissue. We show that Act88F, TpnC4 are not detected outside of flight muscle cells (99.4% and 99.8% of the single molecular signal in flight muscles only), giving us confidence in the specificity of the MC method. Following the suggestion of the reviewer, we have adapted an HCR-FISH method to Drosophila adult body sections for the revised version of the manuscript. Using this method, we were able to confirm the higher expression/localization of sls transcripts to and around the adult flight muscle nuclei, with an enrichment in nuclei close to the muscle-tendon attachment sites (new Figure 4D-F and new Figure 4 – figure supplement 1). We have also been able to confirm some complementarity in the localization patterns of Act88F and TpnC4 in longitudinal stripes in adult flight muscles, however for Mhc we could not confirm this pattern with HCR-FISH (new Figure 5C-F and new Figure 5 – figure supplement 1). While we could confirm most of the pattern seen, we do not know the exact reason for the slight discrepancies. Thus, we now recommend that insights found with SRT should be confirmed with more classical FISH methods.

(6) The authors developed an unbiased method to identify "new cell types" which relies on coexpression of different transcripts. Are these new cell types or a cell state? While expression is a helpful first step, without any functional data, the significance of what the authors found is diminished. The authors need to soften their statements.

The term “new cell types” only appeared in the old title. We agree that with the current spatial map we cannot be sure to have found “new cell types”, instead we show where unannotated/uncharacterized clusters from the scRNA-seq atlas are located, based on their gene expression. Therefore, we have updated the title in the revised version (Spatial transcriptomics in the adult Drosophila brain and body) and thank the reviewer for this valuable suggestion.

Appraisal:

The authors' goal is to map single cell/nuclear RNAseq data described in the 2022 Fly Atlas paper spatially within an organism to achieve a spatial transcriptomic map of the adult fly; no doubt, this is a critical next step in our use of 'omics approaches. While this manuscript does the hard work of trying to take this next step, including developing and testing a new pipeline for high throughput FISH and its analysis, it falls short, in its present form, in achieving this goal. The authors discuss creating a robust spatial map, based on one male fly. Moreover, they do not reveal principles of mRNA localization, as stated in the abstract; they show us patterns, but nothing about the logic or function of these patterns. This same criticism can be said of the identification of "new cell types, just based on RNA colocalization. In both cases (mRNA subcellular localization or cell type identification), further data in the form of validation with traditional low throughput FISH and genetic manipulations to assess the relation to cell function are required for the authors to make such claims. 

We have indeed used one male fly for the adult male body data. This is mainly due to the cost of the sample processing. We used 12 individuals for the head samples (from 1 individual we acquired 2 sections, a total of 13 sections). We show that the body samples show a high correlation with each other, while the head samples cover multiple depths of the head. Still, even in the head, we find that sections at similar depths show a high similarity to each other in terms of gene-gene coexpression and expression patterns. Although obtaining sections from more animals would be valuable, we do not believe it to be necessary for our current goals. Additional replicates beyond the ones we already provide would require significant amounts of extra time and budget, while they would very likely produce similar results as we already show. Following the reviewer’s suggestion, we have tested several genes with HCR-FISH and could readily confirm the localization pattern of sls mRNA close to the terminal nuclei of the flight muscles. This pattern is likely due to a higher expression of sls in these nuclei, as a large amount of sls mRNA signal is detected within the nuclei (Figure 4). A detailed dissection of the mechanism that establishes this pattern is beyond the scope of this manuscript, which is the first one on applying spatial transcriptomics to adult Drosophila.

The usage of the term “new cell types” was indeed ambiguous and we removed this from the revised version. We now clarified that we map the spatial location of unannotated clusters in the brain. This may or may not include uncharacterized cell types. We now further specify that we have only inferred the location of the nuclei; thus, neuronal function or the location of their axonal processes are still unknown. As such, our data provides a starting point to identify uncharacterized cell types, since their marker genes and nuclear location are now determined. The next step to identify “new cell types” would indeed be to acquire genetic access to these cell types and characterize them in more detail. This is beyond the scope of this manuscript, and therefore we have toned down the title in the revised version and thank the reviewer for this valuable suggestion. 

Discussion of likely impact:

If revised, these data, and importantly the approach, would impact those working on Drosophila adults as well as those working in other model systems where single cell/nuclear sequencing is being translated to the spatial localization within the organism. The subcellular localization data - for example, the size of transcripts and how that relates to localization or the patterns of sarcomeric protein localization in muscle - are intriguing, and would likely impact our thinking on RNA localization, transport, etc if confirmed. Lastly, the authors compare their computational approaches to those available in the field; this is valuable as this is a rapidly evolving field and such considerations are critical for those wishing to use this type of approach.

We thank this reviewer for appreciating the impact of our findings and approach to the Drosophila field and beyond. We here provide the groundwork for a full Drosophila adult spatial atlas, similar to how early scRNA-seq datasets provided a framework for the Fly Cell Atlas. In the manuscript we provide both experimental information on how to successfully perform spatial transcriptomics (treating slides for optimal attachment) and the data serves as a benchmark for future experiments to improve upon (similar to how early Drop-seq datasets were compared to later 10x datasets in single-cell transcriptomics). In addition, it also provides proof of principle methods on how to integrate the FCA data with these spatial data and it identifies localized mRNA species in large adult muscle cells, showing the complementarity of spatial techniques with single-cell RNA-seq. For a small number of genes, we have confirmed the mRNA patterns using HCR-FISH in the revised version of this manuscript. To conclude, this is the first spatial adult Drosophila transcriptomics paper, locating 150 mRNA species with easy data access in our user portal (https://spatialfly.aertslab.org/).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) All figures in the manuscript were in grayscale, which made it difficult to interpret the results because the data could only be interpreted by distinguishing different colors to visualize different transcripts. This is likely a technical problem. The manuscript must contain colored images.

We apologize to the reviewer for this technical issue. The manuscript was uploaded in color to bioRxiv and to eLife. We therefore do not understand to reason for this problem. We are surprised that this issue was not resolved in the reviewers’ discussion since color is obviously essential to appreciate the beauty of this manuscript.

(2) In Figure 2a, the authors comment on the subcellular localization of trypsin isoforms, but the figure does not indicate the cell borders or the apical and basal regions of the cell. These must be indicated in the figure to help readers understand the results. 

We thank the reviewer for pointing this out; we have now indicated the outlines of the single-cell layer epithelium on the figure. While we have no marker for cell borders, we have a nuclear marker showing that it is a single cell layer. We hope this allows the reader to appreciate the subcellular localization of the trypsin isoforms.

(3) All figures (including the data on the authors' website) contain background staining, which I assume is labeling nuclei. This is not indicated in the manuscript, and should be clarified.

We again thank the reviewer for pointing this out; the background staining indeed labels nuclei (using DAPI). We have indicated this better in the revised version.

(4) In Figure 5c, the authors claim that neuronal and muscular genes are grouped into the same cluster, but they do not indicate which transcripts are neuronal and which ones are muscular. This must be indicated in the figure.

We thank the reviewer for this comment. Indeed, there was only one gene, acj6, present in the muscle cluster. So, we decided to delete this statement in the revised version.

(5) The authors utilized and compared three different approaches to integrate single nuclei sequencing data from the Fly Cell Atlas to their spatially resolved transcriptomics (SRT) data. I was wondering if it is possible to generate a virtual expression explorer using this integrated data, similar to the dataset published in the 2017 Science article by Karaiskos et al., where they combined publicly available in situ hybridization data of fly embryos and their single-cell sequencing data. This virtual expression explorer would be useful to visualize the expression pattern of transcripts that the authors of this paper did not use for their SRT.

We thank the reviewer for this interesting comment. Using Tangram, we indeed infer gene expression for all genes from the Fly Cell Atlas. To make this visible we have created a Scope session (https://scope.aertslab.org/#/Spatial_Fly/*/welcome), with which users can browse inferred gene expression levels (note that this is on a segmented cell level). We do notice that the inferred gene expression levels contain many false positives and should therefore be used with caution. The spatial data themselves can be browsed through the spatial portal at https://spatialfly.aertslab.org/ .

Reviewer #2 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses:

The authors have used a new high throughput approach to examine the location of 150 RNAs in adult Drosophila heads or one body. It is unclear whether the fixation/repeated imaging etc is accurately reflecting the patterns of expression in vivo. The authors should confirm these data using low throughput established techniques for the RNA patterns in muscle for example.

The authors should clarify their experimental approaches and include additional samples if they indeed want to establish the rosetta stone of fly adults. These data are from only a male fly (and as such is not a complete analysis of the adult fly). To be a map of the adult fly, data from both sexes need to be included.

Unless functional data that complement the descriptive data shown here are included, the authors have to soften their conclusions. For example, while spatial transcriptomics has mapped RNA expression to a location, without some functional data, it is difficult to conclude that these are indeed "new cell types". Same with the RNA localization principles.

Recommendations for improving the writing and presentation:

(1) The manuscript should be heavily revised: in many places, important details are left out or should be moved from the methods to the main text. In addition, the authors often overstate their findings throughout the manuscript. As an example, it appears that the data presented is only from 1 fly, so this doesn't increase the reader's confidence in the data or the applicability of the approach. Also, it isn't clear how many flies were analyzed for the heads (one male fly too?) nor what variability is present from fly to fly. For the approach and data to be used by others, this is important to know.

We moved some text from the methods section to the main text to be clearer. We now also state how many animals were used for the MC method. While the data for the body has been generated from 1 male only, the data for the head was generated from 12 flies; for both cases, similar slices show very similar gene expression patterns. Furthermore, in the body we used widely known and published marker genes that all showed expected expression patterns, indicating robustness. We agree that this is not a full spatial atlas of the fly, this was also not our goal and we have removed such general statements from the revised version: we aimed to generate a spatial transcriptomics dataset, covering the entire fly (head and body) as a proof-of-principle, tackling data generation and analysis, and highlighting challenges in both.

(2) The grammar and word choice throughout are challenging often making the text difficult to follow. This reads like an early draft of the paper.

We apologize to the reviewer for any difficulties. We have revised the text and hope it is now easier to read, while still being accurate on the technical details of the various methods used in our manuscript.

Minor corrections to the text and figures.

See the weaknesses mentioned above. Also:

Figure S1 is unreadable.

There is no simple way to describe the expression values of 100 genes in 100 cell types on a single page. The resolution of the PDF is high enough that after zooming in, all the information can be read easily.

Figure S2, in a, please include the axes so that the reader can better understand the sections shown.

In b, it is unclear what the pink boxes mean. In c, the labels are barely legible.

In Figure 1 – figure supplement 2 (head sections), we have ordered the head sections from anterior to posterior. The boxes in (B) represent boxplots. We have updated this plot for clarity to better display the number of mRNA molecules detected for each gene. We have increased the font size in (C).

Figure S3, in a, please include axes. In b, the meaning of the pink box

In Figure 1 – figure supplement 3 (the body sections) we have added the anterior to posterior and dorso-ventral axis, and ordered the sections that stem from the same animal. The boxes in (B) represent boxplots. We have updated this plot for clarity to better display the number of mRNA molecules detected for each gene. We have added an explanation to the figure legend.  

Figure S4, the text in the axes of the heatmap should have a darker typeface

We have changed it to black, thanks.

Figure S5c, are the colors in the dendrogram supposed to match the spatial location on the right?

The purple of the muscles is barely visible.

Yes, they do match. Colors were modified in the revised version for better visibility.

eLife Assessment

In this valuable study, Seidel et al. identify and characterize a novel subset of hepatocellular carcinoma patient-derived xenograft models defined by active Jagged 1-Notch2 signaling and a distinctive progenitor-like gene expression profile. Within the limitations of the PDX system they used, their methods are state-of-the-art, their data are strong and believable, and their conclusions are convincing. However, the ability to identify HCC patients that might respond is limited, and the mechanistic assessment downstream of JAG1/NOTCH2 is relatively descriptive. Some additional clarifications and experiments would strengthen the paper.

Reviewer #1 (Public review):

Summary:

The significance of Notch in liver cancer has been inconsistently described to date. The authors conduct a PDX screen using JAG1 ab and identify 2 sensitive tumor models. Further characterization with bulk RNA seq, scRNA seq, and ATAC seq of these tumors was performed.

Strengths:

The reliance on an extensive panel of PDXs makes this study more definitive than prior studies.

Gene expression analyses seem robust.

Identification of a JAG1-dependent signature associated with hepatocyte differentiation is interesting.

Weaknesses:

The introduction is rather lengthy and not entirely accurate. HCC is a single cancer type/histology. There may be variants of histology (allusion to "mixed-lineage" is inaccurate as combined HCC-CCa are not conventionally considered HCC and are not treated as HCC in clinical practice as they are even excluded from HCC trials), but any cancer type can have differences in differentiation. Just state there are multiple molecular subtypes of this disease.

There is minimal data on the PDXs, despite this being highlighted throughout the text. Clinical and possibly some molecular characterization of these cancers should be provided. It is also odd that the authors include only 35 HCC and then a varied sort of cancer histologies, which is peculiar given their prior statements regarding the heterogeneity of HCC.

"super-responder" is not a meaningful term, I would eliminate this use as it has no clinical or scientific convention that I am aware of.

The "expansion" of the PDX screen is poorly described. Why weren't these PDXs included in the first screen? This is quite odd as the responses in the initial screen were underwhelming. What was the denominator number of all PDXs that were assessed for JAG1 and NOTCH2 expression? This is important as it clarifies how relevant JAG1 inhibition would be to an unselected HCC population.

Was there some kind of determination of the optimal dose or dose dependency for the JAG1 ab? The original description of the JAG1 ab was in mouse lungs, not malignant or liver cells. In addition, supplementary Figure 2D is missing. There needs to be data provided on the specificity of the human-specific JAG1 ab and the anti-NOTCH2 ab. I'm not familiar with these ab, and if they are not publicly accessible reagents, more transparency on this is needed. In addition, given the reliance of the entire paper on these antibodies, I would recommend orthogonal approaches (either chemical or genetic) to confirm the sensitivity and insensitivity of select PDXs to Notch inhibition.

scRNA-seq data seems to add little to the paper and there is no follow-up of the findings. Are the low-expressing JAG1 cells eventually enriched in treated tumors contributing to disease recurrence?

The discussion should be tempered. The finding of only 2 PDXs that are sensitive out of 45+ tumors treated or selected for indicates that JAG1/NOTCH2 inhibition is likely only effective in rare HCC.

Reviewer #2 (Public review):

Summary:

The authors used a large panel of hepatocellular carcinoma patient-derived xenograft models to test the hypothesis that the developmental dependence of the liver on Jagged1-Notch2 signaling is retained in at least a subset of hepatocellular carcinomas. This led to the identification of two models that were extraordinarily sensitive to well-characterized, specific inhibitory antibodies against Jagged1 or Notch2. Based on additional analyses in these in vivo models, the authors provide compelling evidence that the response is due to the inhibition of human Notch2 and human Jagged1 on tumor cells and that this inhibition leads to a change in gene expression from a progenitor-like state to a hepatocyte-like state accompanied by cell cycle arrest. This change in cell state is associated with up-regulation of HNF4a and CEBPB and increased accessibility of predicted HNF4a and CEBPB genomic binding sites, accompanied by loss of accessibility to sequences predicted to bind TFs linked to multipotent liver progenitors. The authors put forth a plausible model in which inhibition of Notch2 downregulates transcriptional repressors of the Hairy/Enhancer of Split family, leading to increased expression of CEBPB and changes in gene expression that drive hepatocyte differentiation.

Strengths:

The strengths of the paper include the breadth of the preclinical screen in PDX models (which may be of an unprecedented size as preclinical trials go), the high quality of the well-characterized antibodies used as therapeutics and as biological perturbagens, the quality of the data and data analysis, and the authors balanced discussion of the strengths and weaknesses of their findings.

Weaknesses:

The principal weakness is the inability to clearly demonstrate the "translatability" of the PDX findings to primary human hepatocellular carcinoma.

Additional Comments:

Hepatocellular carcinoma is increasing in frequency and is difficult to treat; cure is only possible through early diagnosis and surgery, often in the form of liver transplantation. It is also a common cancer, and so even if only 5% of tumors (a value based on the frequency of super-responders in this preclinical trial) fall into the Jagged1-Notch2 group defined by Seidel et al., the development of an effective therapy for this subgroup would be a very important advance. The chief limitation of their work is that it stops short of identifying primary human hepatocellular carcinomas that correspond to the super-responder PDX models. It can be hoped that their intriguing observations will spur work aimed at filling this gap

There are several other loose ends. An unusual feature of this model is that both Jagged 1 and Notch2 are expressed in the same cells, and even in the same individual cells. In developmental systems, the expression of ligands and receptors in the same cell generally produces receptor inhibition rather than activation, a phenomenon described as cis inhibition. Their super-responder tumor models appear to break this rule, and how and why this is so remains to be understood. A follow-up question is what explains the observed heterogeneity in tumor cells, both at the level of Notch2 activation and scRNAseq clustering, and whether these different cell states are static or interchangeable.

Another unanswered issue pertains to the nature of the tumor response to Notch signaling blockade, which appears to be mainly cell cycle arrest. There are a number of human tumors with cell autonomous Notch signaling due to gain of function Notch receptor mutations that also respond to Notch blockade with cell cycle arrest, such as T cell acute lymphoblastic leukemia (T-ALL). In general, clinical trials of pan-Notch inhibitors such as gamma-secretase inhibitors have been disappointing in such tumors, perhaps reflecting a limitation of treatments with significant toxicity that do not kill tumor cells directly. It could be argued that this limitation will be mitigated by the apparently excellent safety profile of Notch2 blocking antibody, which perhaps could be administered for a sustained period, akin to the use of tyrosine kinase inhibitors in chronic myeloid leukemia---but this remains to be determined.

A minor comment is reserved for the statement in the discussion that "In chronic myelomonocytic leukemia, which results from an inactivating mutation in the y-secretase complex component nicastrin, Notch signaling has a tumor suppressive function, that is mediated through direct repression of CEBPA and PU.1 by HES1 (Klinakis et al., 2011)". Thousands of cases of CMML and related myeloid tumors have been subjected to whole exome and even whole genome sequencing without the identification of Notch signaling pathway mutations. Thus, an important tumor suppressive role for Notch-mediated through HES1 in myeloid tumors is not proven.

Reviewer #3 (Public review):

Summary:

Notch is active in HCC, but generally not mutated. The authors use a JAG1-selective blocking antibody in a large panel of liver cancer patient-derived xenograft models. They find JAG-dependent HCCs, and these are aggressive and proliferative. Notch inhibition induces cycle arrest and promotes hepatocyte differentiation, through upregulation of CEBPA expression and activation of existing HNF4A, mimicking normal developmental programs.

The authors use aJ1.b70, a potent and selective therapeutic antibody that inhibits JAG1 against PDX models. They tested over 40 PDX models and found a handful of super-responders to single-agent inhibition. In LIV78 and Li1035 cancer cells, NOTCH2 was expressed and required, in contrast to NOTCH1. RNA-seq showed that the responsive HCCs resembled the S2 transcriptional class of HCCs, which were enriched for Notch-dependent models. They conclude that these dependent tumors have transcriptomes that resemble a hybrid progenitor cell expressing FGF9 and GAS7. Inhibition was able to induce hepatocyte differentiation away from a NOTCH-driven progenitor program. scRNA-seq analysis showed a large population of NOTCH-JAG expressing cells but also showed that there are cells that did not. Not surprisingly, NOTCH2 inhibition leads to increased CEBPA and HNF4A transcriptional activity, which are standard TFs in hepatocytes.

Strengths:

The paper provides useful information about the frequency of HCCs and CCA that respond to NOTCH inhibition and could allow us to anticipate the super-responder rate if these antibodies were actually used in the clinic. The inhibitor tools are highly specific, and provide useful information about NOTCH activities in liver cancers. The large number of PDXs and the careful transcriptomic analyses were positives about the study.

Weaknesses:

The paper is mostly descriptive.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The significance of Notch in liver cancer has been inconsistently described to date. The authors conduct a PDX screen using JAG1 ab and identify 2 sensitive tumor models. Further characterization with bulk RNA seq, scRNA seq, and ATAC seq of these tumors was performed.

Strengths:

The reliance on an extensive panel of PDXs makes this study more definitive than prior studies.

Gene expression analyses seem robust.

Identification of a JAG1-dependent signature associated with hepatocyte differentiation is interesting.

Weaknesses:

The introduction is rather lengthy and not entirely accurate. HCC is a single cancer type/histology. There may be variants of histology (allusion to "mixed-lineage" is inaccurate as combined HCC-CCa are not conventionally considered HCC and are not treated as HCC in clinical practice as they are even excluded from HCC trials), but any cancer type can have differences in differentiation. Just state there are multiple molecular subtypes of this disease.

We will shorten the Introduction, in part by eliminating the discussion of histological variation in HCC and focusing on the molecular classifications.

There is minimal data on the PDXs, despite this being highlighted throughout the text. Clinical and possibly some molecular characterization of these cancers should be provided. It is also odd that the authors include only 35 HCC and then a varied sort of cancer histologies, which is peculiar given their prior statements regarding the heterogeneity of HCC.

We agree that clinical and molecular characterizations of the PDX models would be helpful and will follow up with the relevant contract research organization to determine what characterization is available.

Regarding the liver cancer PDX panel, we suggest that a major strength of the manuscript is the large number of HCC models that were tested (the reviewer also notes the importance of the “extensive” panel); thus, we are a bit confused by the reference to “only 35 HCC”.  To clarify the choice of models in the PDX screen, it may help to put the screen in historical perspective as the project unfolded.  In retrospect, our preliminary efficacy studies using only two HCC models were fortunate to identify the highly sensitive model, LIV78.  To go beyond the simple diagnostic hypothesis that focused on Jag1, Notch2 and Hes1 expression, we took an unbiased approach to discover features linked to Notch dependence.  This approach meant running an efficacy screen in all liver cancer models that were up and running at our chosen research organization, without biased selection criteria.  That set of models is what is represented in the “pre-clinical screen” in Fig. 1B

"super-responder" is not a meaningful term, I would eliminate this use as it has no clinical or scientific convention that I am aware of.

We were aware of the interchangeable terms of “exceptional-“ or “super-responder” and prefer to leave this language in the text.  Some references are as follows: 

● Prasad et al., Characteristics of exceptional or super responders to cancer drugs. Mayo Clinic Proceedings, 2015. 

● NCI Press Release 2020:  https://www.cancer.gov/news-events/press-releases/2020/cancer-exceptional-responders-study-genetic-alterations-may-contribute

● NIH Info:  https://www.nih.gov/news-events/nih-research-matters/understanding-exceptional-responders-cancer-treatment

● “What is a Super Responder?  Bradley Jones, Cancer Today, June 26, 2020.

● “What is a Super Responder?”  AACR.  https://www.aacr.org/patients-caregivers/progress-against-cancer/what-is-a-super-responder/

The "expansion" of the PDX screen is poorly described. Why weren't these PDXs included in the first screen? This is quite odd as the responses in the initial screen were underwhelming. What was the denominator number of all PDXs that were assessed for JAG1 and NOTCH2 expression? This is important as it clarifies how relevant JAG1 inhibition would be to an unselected HCC population.

We will revise the writing here to clarify as requested.  For now, we can hopefully clarify by building on the historical context described above.  As the reviewer notes and as we describe in the text, the in vivo screen revealed only a modest JAG1 dependence.  The screen also highlighted that LIV78 was exceptional, and we wanted to understand why.  Hypothesizing that the expression of progenitor markers in LIV78 were important for understanding its JAG1 dependence, we identified four additional models at other contract research organizations.  It is this set of four that comprises the “expansion” cohort.

Was there some kind of determination of the optimal dose or dose dependency for the JAG1 ab? The original description of the JAG1 ab was in mouse lungs, not malignant or liver cells. In addition, supplementary Figure 2D is missing. There needs to be data provided on the specificity of the human-specific JAG1 ab and the anti-NOTCH2 ab. I'm not familiar with these ab, and if they are not publicly accessible reagents, more transparency on this is needed. In addition, given the reliance of the entire paper on these antibodies, I would recommend orthogonal approaches (either chemical or genetic) to confirm the sensitivity and insensitivity of select PDXs to Notch inhibition.

First, we note that the anti-human/mouse Jagged1 and Notch2 blocking antibodies used in our study have been extensively characterized as potent and selective and have been widely used outside of our group by the Notch research community (for the human/mouse cross-reactive antibodies, see Wu et al., Nature, 2010 for anti-NOTCH2 and Lafkas et al., Nature 2015 for anti-JAG1). As noted, the antibodies have been used in studies of normal mouse lungs (Lafkas et al.).  Please note that the characterization also includes mouse models of primary liver cancer that formed the foundation for the current work (please refer to Huntzicker et al, 2015).

While we show dose responses in Figures 1A and 1D, we have not optimized dosing, for example by determining the minimal drug exposures needed for pharmacodynamic changes (pathway inhibition) and efficacy.  For the purposes of this study, we erred on the side of dosing at high concentrations to minimize the risk of false negative responses.

Regarding the specificity of the human-specific anti-JAG1 antibody, which is revealed here for the first time, we apologize that we incorrectly provided a text reference to Supplementary Figure 2D instead of Supplementary Figure 1D.  We will revise accordingly.  Fig. 1D shows results from a reporter assay demonstrating that the antibody blocks signaling induced by human but not mouse JAG1.

We appreciate the value of orthogonal methods in establishing the credibility of a novel finding.  We note that genetic approaches are technically highly challenging in PDX models.  Chemically, we could have tested y-secretase inhibitors (GSIs). Our position is that such inhibitors are poor substitutes for the selective antibodies that we employed, at least for addressing the questions that are relevant in this study.   Although commonly used to perturb Notch signaling, GSIs target numerous proteins and signaling cascades independent of Notch.  Moreover, their use in vivo leads to intestinal and other toxicities, limiting exposure. 

scRNA-seq data seems to add little to the paper and there is no follow-up of the findings. Are the low-expressing JAG1 cells eventually enriched in treated tumors contributing to disease recurrence?

We respectfully disagree with this sentiment. The single-cell RNA sequencing dataset revealed the enrichment of hepatocyte-like tumor cells following Notch inhibition. Importantly, this dataset also allowed us to identify transcription factor activities regulating different cell states, which we could not have done otherwise. This understanding in turn was fundamental to develop our hypothesis that Notch inhibition, through derepressing CEBPA expression, allows chromatin engagement of HNF4A and CEPBA and thereby promotes a hepatocyte differentiation program that is not compatible with tumor maintenance.  

The discussion should be tempered. The finding of only 2 PDXs that are sensitive out of 45+ tumors treated or selected for indicates that JAG1/NOTCH2 inhibition is likely only effective in rare HCC.

We agree that strong responses to Notch inhibition in the PDX models are rare (~5%) and state as much in both the Results and Discussion sections. We maintain that it is important to put this PDX response frequency into a larger context.  First, establishing PDX models---human tumor samples that grow on the flanks of immunocompromised mice---represents a strong selective pressure.  In other words, we don’t know precisely how the frequency of responses in this selected set of PDX models may compare to the frequency that would be observed in human patient populations. Second, the magnitude of the response points to important and hitherto unappreciated biology, with blocking JAG1 or NOTCH2 reproducibly inducing regressions in the most sensitive models.  Our hope is that the field can build from this study to generate diagnostic tools that identify sensitive patient tumors, define the true frequency of this patient group within the larger HCC population (even though likely rare), and direct the relevant Notch-based therapeutics to these patients.  Within this context, and while noting the rarity of PDX responses, we hope that we have not overstated the case.

Reviewer #2 (Public review):

Summary:

The authors used a large panel of hepatocellular carcinoma patient-derived xenograft models to test the hypothesis that the developmental dependence of the liver on Jagged1-Notch2 signaling is retained in at least a subset of hepatocellular carcinomas. This led to the identification of two models that were extraordinarily sensitive to well-characterized, specific inhibitory antibodies against Jagged1 or Notch2. Based on additional analyses in these in vivo models, the authors provide compelling evidence that the response is due to the inhibition of human Notch2 and human Jagged1 on tumor cells and that this inhibition leads to a change in gene expression from a progenitor-like state to a hepatocyte-like state accompanied by cell cycle arrest. This change in cell state is associated with up-regulation of HNF4a and CEBPB and increased accessibility of predicted HNF4a and CEBPB genomic binding sites, accompanied by loss of accessibility to sequences predicted to bind TFs linked to multipotent liver progenitors. The authors put forth a plausible model in which inhibition of Notch2 downregulates transcriptional repressors of the Hairy/Enhancer of Split family, leading to increased expression of CEBPB and changes in gene expression that drive hepatocyte differentiation.

Strengths:

The strengths of the paper include the breadth of the preclinical screen in PDX models (which may be of an unprecedented size as preclinical trials go), the high quality of the well-characterized antibodies used as therapeutics and as biological perturbagens, the quality of the data and data analysis, and the authors balanced discussion of the strengths and weaknesses of their findings.

Weaknesses:

The principal weakness is the inability to clearly demonstrate the "translatability" of the PDX findings to primary human hepatocellular carcinoma.

We agree that translatability has not been fully addressed.  As noted in our response to Reviewer 1, our hope is that the field can build from this study to generate diagnostic tools that identify sensitive patient tumors, define the true frequency of this patient group within the larger HCC population, and direct the relevant Notch-based therapeutics to these patients.  We remain encouraged by the strength of the response in the sensitive models.

Additional Comments:

Hepatocellular carcinoma is increasing in frequency and is difficult to treat; cure is only possible through early diagnosis and surgery, often in the form of liver transplantation. It is also a common cancer, and so even if only 5% of tumors (a value based on the frequency of super-responders in this preclinical trial) fall into the Jagged1-Notch2 group defined by Seidel et al., the development of an effective therapy for this subgroup would be a very important advance. The chief limitation of their work is that it stops short of identifying primary human hepatocellular carcinomas that correspond to the super-responder PDX models. It can be hoped that their intriguing observations will spur work aimed at filling this gap.

There are several other loose ends. An unusual feature of this model is that both Jagged 1 and Notch2 are expressed in the same cells, and even in the same individual cells. In developmental systems, the expression of ligands and receptors in the same cell generally produces receptor inhibition rather than activation, a phenomenon described as cis inhibition. Their super-responder tumor models appear to break this rule, and how and why this is so remains to be understood. A follow-up question is what explains the observed heterogeneity in tumor cells, both at the level of Notch2 activation and scRNAseq clustering, and whether these different cell states are static or interchangeable.

We enthusiastically agree that these are fascinating questions, worthy of further study.  As noted, the majority of tumor cells express both ligand and receptor and seem to be “on” for Notch signaling.  We have not been able to determine whether the signal is induced in a cell autonomous or non-autonomous manner (or both).  As the reviewer notes, the HCC features we observe are inconsistent with the dogma that has arisen from studies on Notch signaling in developmental contexts.

We do not yet have the experimental data to fully address the second question of what causes the heterogeneity of Notch2 activation and scRNAseq clustering.  We speculate that the cell states may be dynamic, which would be consistent with the changes in cell populations observed after antibody treatment.

Another unanswered issue pertains to the nature of the tumor response to Notch signaling blockade, which appears to be mainly cell cycle arrest. There are a number of human tumors with cell autonomous Notch signaling due to gain of function Notch receptor mutations that also respond to Notch blockade with cell cycle arrest, such as T cell acute lymphoblastic leukemia (T-ALL). In general, clinical trials of pan-Notch inhibitors such as gamma-secretase inhibitors have been disappointing in such tumors, perhaps reflecting a limitation of treatments with significant toxicity that do not kill tumor cells directly. It could be argued that this limitation will be mitigated by the apparently excellent safety profile of Notch2 blocking antibody, which perhaps could be administered for a sustained period, akin to the use of tyrosine kinase inhibitors in chronic myeloid leukemia---but this remains to be determined.

We agree that a full understanding of the tumor response warrants further investigation.  Like the reviewer, we speculate that the improved safety profile of selective antibodies relative to pan-Notch inhibitors may enable greater and sustained therapeutic coverage of Notch inhibition than has been feasible in T-ALL trials.  Given that in the sensitive PDX models we observe rapid tumor regressions, not just stasis, it would seem to follow that the mechanism underpinning the tumor response involves more than just cell cycle blockade.  Whether tumor shrinkage reflects additional cell death mechanisms or simply tumor cell turnover after cell cycle arrest remains to be determined. 

A minor comment is reserved for the statement in the discussion that "In chronic myelomonocytic leukemia, which results from an inactivating mutation in the y-secretase complex component nicastrin, Notch signaling has a tumor suppressive function, that is mediated through direct repression of CEBPA and PU.1 by HES1 (Klinakis et al., 2011)". Thousands of cases of CMML and related myeloid tumors have been subjected to whole exome and even whole genome sequencing without the identification of Notch signaling pathway mutations. Thus, an important tumor suppressive role for Notch-mediated through HES1 in myeloid tumors is not proven.

We agree that our sentence about Notch and CMML does not fit well with the prevalent paradigm established by genome wide sequencing and other methods.  We will edit this paragraph accordingly, focusing on Hes1 negative regulation of CEBPA in myeloid fate control and how that shapes our thinking on molecular mechanisms in the Notch-dependent HCCs.

Reviewer #3 (Public review):

Summary:

Notch is active in HCC, but generally not mutated. The authors use a JAG1-selective blocking antibody in a large panel of liver cancer patient-derived xenograft models. They find JAG-dependent HCCs, and these are aggressive and proliferative. Notch inhibition induces cycle arrest and promotes hepatocyte differentiation, through upregulation of CEBPA expression and activation of existing HNF4A, mimicking normal developmental programs.

The authors use aJ1.b70, a potent and selective therapeutic antibody that inhibits JAG1 against PDX models. They tested over 40 PDX models and found a handful of super-responders to single-agent inhibition. In LIV78 and Li1035 cancer cells, NOTCH2 was expressed and required, in contrast to NOTCH1. RNA-seq showed that the responsive HCCs resembled the S2 transcriptional class of HCCs, which were enriched for Notch-dependent models. They conclude that these dependent tumors have transcriptomes that resemble a hybrid progenitor cell expressing FGF9 and GAS7. Inhibition was able to induce hepatocyte differentiation away from a NOTCH-driven progenitor program. scRNA-seq analysis showed a large population of NOTCH-JAG expressing cells but also showed that there are cells that did not. Not surprisingly, NOTCH2 inhibition leads to increased CEBPA and HNF4A transcriptional activity, which are standard TFs in hepatocytes.

Strengths:

The paper provides useful information about the frequency of HCCs and CCA that respond to NOTCH inhibition and could allow us to anticipate the super-responder rate if these antibodies were actually used in the clinic. The inhibitor tools are highly specific, and provide useful information about NOTCH activities in liver cancers. The large number of PDXs and the careful transcriptomic analyses were positives about the study.

Weaknesses:

The paper is mostly descriptive.

eLife Assessment

The manuscript contains important findings regarding inflammatory macrophage subsets that have theoretical and/or practical applications beyond the field of rheumatology. The authors demonstrate with convincing evidence the effects of PGE2 on TNF signaling in a well-written manuscript that features methods, data, and analyses in line with current state-of-the-art technologies. This work will be of broad interest to immunologists and cell biologists.

Reviewer #1 (Public review):

Summary:

This article investigates the phenotype of macrophages with a pathogenic role in arthritis, particularly focusing on arthritis induced by immune checkpoint inhibitor (ICI) therapy.

Building on prior data from monocyte-macrophage coculture with fibroblasts, the authors hypothesized a unique role for the combined actions of prostaglandin PGE2 and TNF. The authors studied this combined state using an in vitro model with macrophages derived from monocytes of healthy donors. They complemented this with single-cell transcriptomic and epigenetic data from patients with ICI-RA, specifically, macrophages sorted out of synovial fluid and tissue samples. The study addressed critical questions regarding the regulation of PGE2 and TNF: Are their actions co-regulated or antagonistic? How do they interact with IFN-γ in shaping macrophage responses?

This study is the first to specifically investigate a macrophage subset responsive to the PGE2 and TNF combination in the context of ICI-RA, describes a new and easily reproducible in vitro model, and studies the role of IFNgamma regulation of this particular Mф subset.

Strengths:

Methodological quality: The authors employed a robust combination of approaches, including validation of bulk RNA-seq findings through complementary methods. The methods description is excellent and allows for reproducible research. Importantly, the authors compared their in vitro model with ex vivo single-cell data, demonstrating that their model accurately reflects the molecular mechanisms driving the pathogenicity of this macrophage subset.

Weaknesses:

Introduction: The introduction lacks a paragraph providing an overview of ICI-induced arthritis pathogenesis and a comparison with other types of arthritis. Including this would help contextualize the study for a broader audience.

Results Section: At the beginning of the results section, the experimental setup should be described in greater detail to make an easier transition into the results for the reader, rather than relying just on references to Figure 1 captions.

There is insufficient comparison between single-cell RNA-seq data from ICI-induced arthritis and previously published single-cell RA datasets. Such a comparison may include DEGs and GSEA, pathway analysis comparison for similar subsets of cells. Ideally, an integration with previous datasets with RA-tissue-derived primary monocytes would allow for a direct comparison of subsets and their transcriptomic features.

While it's understandable that arthritis samples are limited in numbers and myeloid cell numbers, it would still be interesting to see the results of PGE2+TNF in vitro stimulation on the primary RA or ICI-RA macrophages. It would be valuable to see RNA-Seq signatures of patient cell reactivation in comparison to primary stimulation of healthy donor-derived monocytes.

Discussion: Prior single-cell studies of RA and RA macrophage subpopulations from 2019, 2020, 2023 publications deserve more discussion. A thorough comparison with these datasets would place the study in a broader scientific context.<br /> Creating an integrated RA myeloid cell atlas that combines ICI-RA data into the RA landscape would be ideal to add value to the field.<br /> As one of the next research goals, TNF blockade data in RA and ICI-RA patients would be interesting to add to such an integrated atlas. Combining responders and non-responders to TNF blockade would help to understand patient stratification with the myeloid pathogenic phenotypes. It would be great to read the authors' opinion on this in the Discussion section.

Conclusion: The authors demonstrated that while PGE2 maintains the inflammatory profile of macrophages, it also induces a distinct phenotype in simultaneous PGE2 and TNF treatment. The study of this specific subset in single-cell data from ICI-RA patients sheds light on the pathogenic mechanisms underlying this condition, however, how it compares with conventional RA is not clear from the manuscript.<br /> Given the substantial incidence of ICI-induced autoimmune arthritis, understanding the unique macrophage subsets involved for future targeting them therapeutically is an important challenge. The findings are significant for immunologists, cancer researchers, and specialists in autoimmune diseases, making the study relevant to a broad scientific audience.

Reviewer #2 (Public review):

Summary/Significance of the findings:

The authors have done a great job by extensively carrying out transcriptomic and epigenomic analyses in the primary human/mouse monocytes/macrophages to investigate TNF-PGE2 (TP) crosstalk and their regulation by IFN-γ in the Rheumatoid arthritis (RA) synovial macrophages. They proposed that TP induces inflammatory genes via a novel regulatory axis whereby IFN-γ and PGE2 oppose each other to determine the balance between two distinct TNF-induced inflammatory gene expression programs relevant to RA and ICI-arthritis.

Strengths:

The authors have done a great job on RT-qPCR analysis of gene expression in primary human monocytes stimulated with TNF and showing the selective agonists of PGE2 receptors EP2 and EP4 22 that signal predominantly via cAMP. They have beautifully shown IFN-γ opposes the effects of PGE2 on TNF-induced gene expression. They found that TP signature genes are activated by cooperation of PGE2-induced AP-1, CEBP, and NR4A with TNF-induced NF-κB activity. On the other hand, they found that IFN-γ suppressed induction of AP-1, CEBP, and NR4A activity to ablate induction of IL-1, Notch, and neutrophil chemokine genes but promoted expression of distinct inflammatory genes such as TNF and T cell chemokines like CXCL10 indicating that TP induces inflammatory genes via IFN-γ in the RA and ICI-arthritis.

Weaknesses:

(1) The authors carried out most of the assays in the monocytes/macrophages. How do APC-cells like Dendritic cells behave with respect to this TP treatment similar dosing?

(2) The authors studied 3h and 24h post-treatment transcriptomic and epigenomic. What happens to TP induce inflammatory genes post-treatment 12h, 36h, 48h, 72h. It is critical to see the upregulated/downregulated genes get normalised or stay the same throughout the innate immune response.

(3) The authors showed IL1-axis in response to the TP-treatment. Do other cytokine axes get modulated? If yes, then how do they cooperate to reduce/induce inflammatory responses along this proposed axis?

Overall, the data looks good and acceptable but I need to confirm the above-mentioned criticisms.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This article investigates the phenotype of macrophages with a pathogenic role in arthritis, particularly focusing on arthritis induced by immune checkpoint inhibitor (ICI) therapy.

Building on prior data from monocyte-macrophage coculture with fibroblasts, the authors hypothesized a unique role for the combined actions of prostaglandin PGE2 and TNF. The authors studied this combined state using an in vitro model with macrophages derived from monocytes of healthy donors. They complemented this with single-cell transcriptomic and epigenetic data from patients with ICI-RA, specifically, macrophages sorted out of synovial fluid and tissue samples. The study addressed critical questions regarding the regulation of PGE2 and TNF: Are their actions co-regulated or antagonistic? How do they interact with IFN-γ in shaping macrophage responses?

This study is the first to specifically investigate a macrophage subset responsive to the PGE2 and TNF combination in the context of ICI-RA, describes a new and easily reproducible in vitro model, and studies the role of IFNgamma regulation of this particular Mф subset.

Strengths:

Methodological quality: The authors employed a robust combination of approaches, including validation of bulk RNA-seq findings through complementary methods. The methods description is excellent and allows for reproducible research. Importantly, the authors compared their in vitro model with ex vivo single-cell data, demonstrating that their model accurately reflects the molecular mechanisms driving the pathogenicity of this macrophage subset.

Weaknesses:

Introduction: The introduction lacks a paragraph providing an overview of ICI-induced arthritis pathogenesis and a comparison with other types of arthritis. Including this would help contextualize the study for a broader audience.

Thank you for this suggestion, we will add a paragraph on ICI-arthritis to intro.

Results Section: At the beginning of the results section, the experimental setup should be described in greater detail to make an easier transition into the results for the reader, rather than relying just on references to Figure 1 captions.

We will clarify the experimental setup.

There is insufficient comparison between single-cell RNA-seq data from ICI-induced arthritis and previously published single-cell RA datasets. Such a comparison may include DEGs and GSEA, pathway analysis comparison for similar subsets of cells. Ideally, an integration with previous datasets with RA-tissue-derived primary monocytes would allow for a direct comparison of subsets and their transcriptomic features.

This is a great idea, we will integrate the data sets and if batch correction is successful will present this analysis.

While it's understandable that arthritis samples are limited in numbers and myeloid cell numbers, it would still be interesting to see the results of PGE2+TNF in vitro stimulation on the primary RA or ICI-RA macrophages. It would be valuable to see RNA-Seq signatures of patient cell reactivation in comparison to primary stimulation of healthy donor-derived monocytes.

We agree that this would be interesting but given limited samples and distribution of samples amongst many studies and investigators this is beyond the scope of the current study. 

Discussion: Prior single-cell studies of RA and RA macrophage subpopulations from 2019, 2020, 2023 publications deserve more discussion. A thorough comparison with these datasets would place the study in a broader scientific context.

Creating an integrated RA myeloid cell atlas that combines ICI-RA data into the RA landscape would be ideal to add value to the field.

As one of the next research goals, TNF blockade data in RA and ICI-RA patients would be interesting to add to such an integrated atlas. Combining responders and non-responders to TNF blockade would help to understand patient stratification with the myeloid pathogenic phenotypes. It would be great to read the authors' opinion on this in the Discussion section.

We will be happy to improve the discussion by including these topics.

Conclusion: The authors demonstrated that while PGE2 maintains the inflammatory profile of macrophages, it also induces a distinct phenotype in simultaneous PGE2 and TNF treatment. The study of this specific subset in single-cell data from ICI-RA patients sheds light on the pathogenic mechanisms underlying this condition, however, how it compares with conventional RA is not clear from the manuscript.

Given the substantial incidence of ICI-induced autoimmune arthritis, understanding the unique macrophage subsets involved for future targeting them therapeutically is an important challenge. The findings are significant for immunologists, cancer researchers, and specialists in autoimmune diseases, making the study relevant to a broad scientific audience.

Reviewer #2 (Public review):

Summary/Significance of the findings:

The authors have done a great job by extensively carrying out transcriptomic and epigenomic analyses in the primary human/mouse monocytes/macrophages to investigate TNF-PGE2 (TP) crosstalk and their regulation by IFN-γ in the Rheumatoid arthritis (RA) synovial macrophages. They proposed that TP induces inflammatory genes via a novel regulatory axis whereby IFN-γ and PGE2 oppose each other to determine the balance between two distinct TNF-induced inflammatory gene expression programs relevant to RA and ICI-arthritis.

Strengths:

The authors have done a great job on RT-qPCR analysis of gene expression in primary human monocytes stimulated with TNF and showing the selective agonists of PGE2 receptors EP2 and EP4 22 that signal predominantly via cAMP. They have beautifully shown IFN-γ opposes the effects of PGE2 on TNF-induced gene expression. They found that TP signature genes are activated by cooperation of PGE2-induced AP-1, CEBP, and NR4A with TNF-induced NF-κB activity. On the other hand, they found that IFN-γ suppressed induction of AP-1, CEBP, and NR4A activity to ablate induction of IL-1, Notch, and neutrophil chemokine genes but promoted expression of distinct inflammatory genes such as TNF and T cell chemokines like CXCL10 indicating that TP induces inflammatory genes via IFN-γ in the RA and ICI-arthritis.

Weaknesses:

(1) The authors carried out most of the assays in the monocytes/macrophages. How do APC-cells like Dendritic cells behave with respect to this TP treatment similar dosing?

We agree that this is an interesting topic especially as TNF + PGE2 is one of the standard methods of maturing in vitro generated human DCs. As DC maturation is quite different from monocyte activation this would represent an entire new study and is beyond the scope of the current manuscript. We will instead describe and cite the literature on DC maturation by TNF + PGE2 including one of our older papers (PMID: 18678606; 2008)

(2) The authors studied 3h and 24h post-treatment transcriptomic and epigenomic. What happens to TP induce inflammatory genes post-treatment 12h, 36h, 48h, 72h. It is critical to see the upregulated/downregulated genes get normalised or stay the same throughout the innate immune response.

We will clarify that the gene response is mostly subsiding at the 24 hour time point, which is in line with in vitro stimulation of primary monocytes in other systems.

(3) The authors showed IL1-axis in response to the TP-treatment. Do other cytokine axes get modulated? If yes, then how do they cooperate to reduce/induce inflammatory responses along this proposed axis?

We will analyze the data for other pathways that are modulated.

Overall, the data looks good and acceptable but I need to confirm the above-mentioned criticisms.

eLife Assessment

This important study presents novel data on variation in sperm whale communication, contributing to a richer understanding of the social transmission of vocal styles across neighbouring clans. The evidence is solid but could have been further improved with clarification of the specialized metrics and terminology used, particularly for comparisons to other taxa. This research will be of interest for bioacoustics and animal communication specialists, particularly those working on social learning and culture.

Reviewer #2 (Public review):

Summary:

The current article presents a new type of analytical approach to the sequential organisation of whale song units.

Strengths:

The detailed description of the internal temporal structure of whale songs is something that has been thus far lacking.

Weaknesses:

The conceptual and terminological bases of the paper are problematical and hamper comparison with other taxa, including humans. According to signal theory, codas are indexical rather than symbolic. They signal an individual's group identity. Borrowing from humans and linguistics, coda inter-group variation represents a case of accents - phonologically different varieties of the same call - not dialects, confirming they are an index. This raises serious doubt about whether alleged "symbolism" and similarity between whale and human vocal behaviour is factual. The same applies to the difference between ICIs (inter-click interval) and IOIs (inter-onset interval). If the two are equivalent, variation in click duration needs to be shown so small that can be considered negligible. This raises serious doubt about whether the alleged variation in whale codas is indeed rhythmic in nature and prevents future efforts for comparison with the vocal capacities of other species. The scope and relevance of this paper for the broader field is limited.

Author response:

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

Reviewer #1 (Public review):

Summary:

This manuscript presents evidence of ’vocal style’ in sperm whale vocal clans. Vocal style was defined as specific patterns in the way that rhythmic codas were produced, providing a fine-scale means of comparing coda variations. Vocal style effectively distinguished clans similar to the way in which vocal repertoires are typically employed. For non-identity codas, vocal style was found to be more similar among clans with more geographic overlap. This suggests the presence of social transmission across sympatric clans while maintaining clan vocal identity.

Strengths:

This is a well-executed study that contributes exciting new insights into cultural vocal learning in sperm whales. The methodology is sound and appropriate for the research question, building on previous work and ground-truthing much of their theories. The use of the Dominica dataset to validate their method lends strength to the concept of vocal style and its application more broadly to the Pacific dataset. The results are framed well in the context of previous works and clearly explain what novel insights the results provide to the current understanding of sperm whale vocal clans. The discussion does an overall great job of outlining why horizontal social learning is the best explanation for the results found.

Weaknesses:

The primary issues with the manuscript are in the technical nature of the writing and a lack of clarity at times with certain terminology. For example, several tree figures are presented and ’distance’ between trees is key to the results, yet ’distance’ is not clearly defined in a way for someone unfamiliar with Markov chains to understand. However, these are issues that can easily be dealt with through minor revisions with a view towards making the manuscript more accessible to a general audience.

I also feel that the discussion could focus a bit more on the broader implications - specifically what the developed methods and results might imply about cultural transmission in other species. This is specifically mentioned in the abstract but not really delved into in detail during the discussion.

We are grateful for the Reviewer’s recognition of the study’s contributions to understanding cultural vocal learning in sperm whales. In response to the concerns regarding clarity and accessibility, we have revised the manuscript to improve the definition of key concepts, such as the notion of “distance” between subcoda trees. This adjustment ensures clarity for readers unfamiliar with the technical details of Markov chains. Additionally, we have expanded the discussion to highlight broader implications of our findings, particularly their relevance to understanding cultural transmission in other species, as suggested.

Reviewer #2 (Public review):

Summary:

The current article presents a new type of analytical approach to the sequential organisation of whale coda units.

Strengths:

The detailed description of the internal temporal structure of whale codas is something that has been thus far lacking.

Weaknesses:

It is unclear how the insight gained from these analyses differs or adds to the voluminous available literature on how codas varies between whale groups and populations. It provides new details, but what new aspects have been learned, or what features of variation seem to be only revealed by this new approach? The theoretical basis and concepts of the paper are problematical and indeed, hamper potentially the insights into whale communication that the methods could offer. Some aspects of the results are also overstated.

We appreciate the Reviewer’s acknowledgment of the novelty in describing the internal temporal structure of whale codas. Regarding the concern about the unique contributions of this approach, we have further emphasized in the revised manuscript how our methodology reveals previously uncharacterized dimensions of coda structure. Specifically, our work highlights how non-identity codas, which have received limited attention, play a significant role in inter-clan acoustic interactions. By leveraging Variable Length Markov Chains, we provide a nuanced understanding of coda subunits that complements existing studies and demonstrates the value of this analytical approach.

Reviewer #3 (Public review):

Summary:

The study presented by Leitao et al., represents an important advancement in comprehending the social learning processes of sperm whales across various communicative and socio-cultural contexts. The authors introduce the concept of ”vocal style” as an addition to the previously established notion of ”vocal repertoire,” thereby enhancing our understanding of sperm whale vocal identity.

Strengths:

A key finding of this research is the correlation between the similarity of clan vocal styles for non-ID codas and spatial overlap (while no change occurs for ID codas), suggesting that social learning plays a crucial role in shaping symbolic cultural boundaries among sperm whale populations. This work holds great appeal for researchers interested in animal cultures and communication. It is poised to attract a broad audience, including scholars studying animal communication and social learning processes across diverse species, particularly cetaceans.

Weaknesses:

In terms of terminology, while the authors use the term ”saying” to describe whale vocalizations, it may be more conservative to employ terms like ”vocalize” or ”whale speech” throughout the manuscript. This approach aligns with the distinction between human speech and other forms of animal communication, as outlined in prior research (Hockett, 1960; Cheney & Seyfarth, 1998; Hauser et al., 2002; Pinker & Jackendoff, 2005; Tomasello, 2010).

We thank the Reviewer for recognizing the importance of our findings and their appeal to broader audiences interested in animal cultures and communication. In response to the suggestion regarding terminology, we have adopted a more conservative language to align with distinctions between human and non-human communication systems. For example, terms like “vocalize” and “vocal repertoire” are used in place of anthropomorphic terms such as “saying”. This ensures consistency with established conventions while maintaining clarity for a broad readership.

Reviewer #1 (Recommendations):

Comment 1

Lines 11-13: As mentioned above, the implications for comparing communication systems and cultural transmission in other species isn’t really discussed much and I think it’s a really interesting component of the study’s broader implications.

Thank you for the comment.

Action - We added a few more sentences to the discussion regarding this.

Comment 2

Figure 1: More information on the figure of these trees would help. What do the connecting lines represent? What do the plain black dots and the black dot with the white dot represent? Especially since the ”distance between trees” is a key result, it’s important that someone unfamiliar with Markov chains can understand the basics of how this is calculated and what it represents. It is explained in the methods, but a brief explanation here would make the results and the figure a lot clearer since the methods are the last section of the manuscript.

These were omitted as we believed that attempting to introduce the mathematical structure and the methodology to compare two instances, in a figure caption, would have caused more ambiguity than necessary.

Action - Added an informal introduction to these concepts on the figure caption. Also added a pointer to the Supplementary Materials.

Comment 3

Table 1: A definition of dICIs should be included here.

Added the definition of discrete ICI to the table.

Comment 4

Figure 2: The placement of the figures is a bit confusing because they are quite far from the text that references them.

We thank the reviewer for pointing this out, we tried to edit the manuscript to improve this issue, but this part of the editing is more within the journal’s powers than our own.

Action - Moved images closes to the corresponding text in manuscript.

Comment 5

Line 117: Probabilistic distance needs to be briefly explained earlier when you first mention distance (see Lines 11-13 comments).

Action - Clarifications added in the caption of figure 1. as per comment on Lines 11-13

Comment 6

Figure 4: Is order considered in these pairwise comparisons? It looks like there are two dots for each pairwise comparison. Additionally, why is the overlap different in these two comparisons? For example, short:four-plus has an overlap of 0.6, while four-plus:short has an overlap of 0.95.

The x-axis of the plots in Figure 4 is geographical clan overlap. This is calculated as per (Hersh et al., 2022) and is described in our Methods (see “Measuring clan overlap” section). Given two clans—for example, the Four-Plus and the Short clan—spatial overlap is calculated twice: as the proportion of the Four-Plus clan’s repertoires that were recorded within 1,000 km of at least one of the Short clan’s repertoires, and as the proportion of the Short clan’s repertoires that were recorded within 1,000 km of at least one of the Four-Plus clan’s repertoires.

Order is important in these pairwise comparisons and generates an asymmetric matrix because the clans have different spatial extents. A clan found in only one small region might overlap completely with a clan that spans the Pacific Ocean, while the opposite is not true. For example, the Short clan spans the Pacific Ocean while the Four-Plus clan has been documented over a smaller area (but that smaller area overlaps extensively with the Short clan range). That is why the value is smaller (0.6) when considering how much of the Short clan’s range is shared with the Four-Plus clan, and larger ( 0.95) when considering how much of the Four-Plus clan’s range is shared with the Short clan.

Action - We have now added a reference to that section of the Methods in our Figure 4 caption and include the clan spatial overlap matrix as a supplemental table (Table S5).

Comment 7

Figure 4: I think the reference should be Hersh et al. [11].

Thank you for catching this.

Action - Reference corrected

Comment 8

Line 227: What aspect of your analysis looked at how often codas were produced? You mention coda frequency, but it is unclear how this was incorporated into your analysis. If this is included in the methods, the language is a bit too technical to easily parse it out.

Indeed here we are referencing the results of the paper mentioned in the previous line. We do not look at coda production frequency.

Action - Added citation to paper that actually performs this analysis.

Comment 9

Lines 253-255: I think you could dig into this a little more, as ”there is currently no evidence” is not the most convincing argument that something is not a driver. Perhaps expanding on the latter sentence that clans are recognizable across oceans basins would be helpful. Does this suggest that clans with similar geographic overlap experience diverse environmental conditions across ocean basins? If so, this might better strengthen your argument against environmental drivers.

Thank you for pointing this out. We feel that the next sentence highlights that clans are recognizable across environmental variation from one side to the other of the ocean basin, which supports the inductive reasoning that codas do not vary systematically with environment. However, we have edited these sentences for clarity.

Comment 10

Lines 311-314: It would also be interesting to look at vocal style across non-ID coda types. Are some more similar to each other across clans than others? Perhaps vocal style can further distinguish types of non-ID codas.

In supplementary Materials 3.4.2 and 3.5 we highlight our results when the codas are separated by coda type summarized in Table S4. We do compare the vocal style across non-ID coda types across clans and within the same clan. The results however are aggregated to highlight the differences in style between the clans and a a coda type-only comparison is not shown.

Comment 11

Lines 390-392: I’m assuming this is why pairwise comparisons were directional (i.e., there was both an A:B and a B:A comparison)? Can you speak to why A:B and B:A comparisons can have such different overlap values?

Given two clans—for example, the Four-Plus and the Short clan—spatial overlap is calculated twice: as the proportion of the Four-Plus clan’s repertoires that were recorded within 1,000 km of at least one of the Short clan’s repertoires, and as the proportion of the Short clan’s repertoires that were recorded within 1,000 km of at least one of the Four-Plus clan’s repertoires.

Order is important in these pairwise comparisons and generates an asymmetric matrix because the clans have different spatial extents. A clan found in only one small region might overlap completely with a clan that spans the Pacific Ocean, while the opposite is not true. For example, the Short clan spans the Pacific Ocean while the Four-Plus clan has been documented over a smaller area (but that smaller area overlaps extensively with the Short clan range). That is why the value is smaller (0.6) when considering how much of the Short clan’s range is shared with the Four-Plus clan, and larger (0.95) when considering how much of the Four-Plus clan’s range is shared with the Short clan.

Action - We now include the clan spatial overlap matrix as a supplemental table (Table S5).

Comment 13

Line 56: Can you briefly explain what memory means in the context of Markov chains?

We provide an explanation of the meaning of memory in the Methods section on ”Variable length Markov Chains”. Briefly, the memory in this case means how many states in the past of the Markov chain’s current state are required to predict the next transition of the chain itself. Standard Markov chains “look” back only one time step, while k-th order Markov chains look back k steps. In our case, there was no reason to assume that the memory required to predict different sequences of states (interclick intervals) should be the same across all sequences, and thus we adopted the formalism of variable length Markov chains, that allow for different levels of memory across the system.

Comment 14

Supplementary Figure S3: Like in the main manuscript, briefly explain or remind us what the blank nodes and the yellow nodes are.

Action - Clarified that the orange node represents the root of the tree in the figures.

Comment 15

Supplementary Figure S7: Put the letters before the dataset name.

Action - Done.

Comment 16

Supplementary Figure S10: Unclear what ’inner vs outer’ means.

One specifies comparisons across clans (outer) and the other within the same clan (inner)

Action - Added clarification on the caption of Figure S10

Comment 17

Supplementary Figure S14: Include a-c labels in the figure itself.

Action - Labels added to figure

Comment 18

Supplementary Figure S14: The information about the nodes is what needs to be included earlier and in the main body when discussing the trees.

Action - Added the explanation earlier in the text and in the main body

Reviewer #2 (Recommendations):

Comment 19

Line 22: ”Symbolic” and ”Arbitrary” are not synonyms. Please see the comment above.

We agree. Here, we make the point that the evolution of symbolic markers of group identity can be explained from what are initially arbitrary, and meaningless, signals (see [L1, L2]). Our point being that any vocalization, any coda, could have become selected for as an identity coda, and to become symbolic, and evolve to play a key role in cultural group formation and in-group favoritism because they enable a community of individuals to solve the problem of with whom to collaborate. The specific coda itself does not affect collaborative pay offs, but group specific differences in behavior can, as such the coda is arguably symbolic; as it is observable and recognizable, and can serve as a means for social assortment even when the behavioural differences are not. This can explain the means by which the social segregation which is observed among behaviorally distinct clans of sperm whales. However, in this manuscript, we do not extend this discussion of existing literature and have attempted to concisely describe this in a couple of lines, which clearly do a disservice to the large body of literature on the evolution of symbolic markers and human ethnic groups. We have added some citations to this section so that the reader may follow up should they disagree with out brief introductory statements.

Action - Added citations and pointers to the literature.

Comment 20

Line 24: The authors’ terminology around ”markers”, ”arbitrary”, ”symbolic” is unnecessarily confusing and mystifying, giving the impression these terms are interchangeable. They are not. These terms are an integral and long-established part of key definitions in signal theory. Term use should be followed accordingly. The observation that whale vocal signals vary per population does not necessarily mean that they function as a social tag. The word ”dog” varies per population but its use relates to an animal, not the population that utters the word. ”Dog” is not ”symbolic” of England, English-speaking populations or the English language. Furthermore, the function of whale vocal signals is extremely challenging to determine. In the best conditions, researchers can pin the signal’s context, this is distinct from signal’s function and further even for the signal’s meaning. How exactly the authors determine that whale vocal signals are arbitrary is, thus, perplexing given that this would require a detailed description and understanding of who is producing the song, when, towards whom, and how the receivers react, none of which the authors have and without which no claim on the signals’ function can be made. This terminological laxness and the sensu latu in extremis to various terms in an unjustified, unnecessary and unhelpful.

We use these terms as established in Hersh et al 2022 and the works leading up to it over the last 20 years in the study of sperm whales. These are often derived from definitions by Boyd and Richerson’s work on culture in humans and animals along with evolution of symbolic markers both in theory and in humans. We agree with the reviewer that these are difficult to establish in non-humans, whales or otherwise, but feel strongly that the accumulating evidence provides strong support for the function of these signals as symbolic markers of cultural groups, and that they likely evolved from initially arbitrary calls which were a part of the vocal repertoire (similar to the process and selective environment in Efferson et al. [L1] and McElreath et al. [L2]). We feel that we do not use these terms interchangeably here, and have inherited their use from definitions from anthropology. The work presented here uses terminology built across two decades of work in cetacean, and sperm whale, culture. And do not feel that these terms should be omitted here.

Comment 21

Lines 21-27: Overly broad and hazy paragraph.

We hope the replies above and our changes satisfy this comment and clarify the text.

Comment 22

Figure 1 legend: What are ”memory structures”? Unjustified descriptor.

The phrase was chosen to make draw some intuition on the variation of context length in variable length markov models.

Action - Re-worded from memory structures to statistical properties

Comment 23

Line 30: Omit ”finite”.

Action - Omitted.

Comment 24

Line 31: Please define and distinguish ”rhythm” and ”tempo”. Also see comment above, rhythm and tempo definitions require the use of IOIs.

We disagree with the reviewer’s claims here. In our research specifically, and for sperm whale research generally, coda inter-click intervals (ICIs) are calculated as the time between the start of the first click and the start of the subsequent click. This makes ICIs identical to inter-onset intervals (IOIs) under all definitions we are aware of. For example, Burchardt and Knornschild [L3] define IOIs as such: “In a sequence of acoustic signals, the time span between the start of an element and the next element, comprising the element duration and the following gap duration”. We now include a sentence making this point.

Regardless, we disagree on a more fundamental level with the statement that unless researchers quantify inter-onset intervals (IOIs), they cannot make any claims about rhythm. There are many studies that investigate rhythmic aspects of human and animal vocalizations without using IOIs [L4–L7]. If the duration of sound elements of interest is relatively constant (as is the case for sperm whale clicks), then rhythm analyses can still be meaningfully conducted on inter-call intervals (the silent intervals between calls).

For sperm whales, coda rhythm is defined by the relative ICIs standardized by their total duration. These can be clustered into discrete, defined rhythm types based on characteristic ICI patterns. Coda tempo is relative to the total duration of the coda itself. This can also be clustered into discrete tempo types across all coda durations as well (see [L8]).

Action - We added a sentence specifying that in this case we can use both ICIs and IOIs because of the standardized length of a single click.

Comment 25

Line 36: Are there non-vocalized codas to require the disambiguation here?

No, we have omitted for clarity.

Comment 26

Line 44: ”Higher” than which other social group class?

Sperm whales live in a multi-level social organization. Clans are a “higher” level of social organization than the social “units” which we define in line 40. Clans are made up of all units which share similar production repertoire of codas.

Action - We have added ’above social units’ on line 44 to make this clear.

Comment 27

Line 47: The use of “symbolic” continues to be enigmatic, even if authors are taking in this classification from other researchers. In signal theory (semiotics), not all biomarkers are necessarily symbols. I advise the authors to avoid the use of the term colloquially and instead adopt the definition used in the research field within which the study falls in.

There is ample examples of the use of ”symbolic” when referring to markers of in-group membership both in human and non-human cultures.Our choice to use the term “symbolic” is based on a previous study [L9] that found quantitative evidence that sperm whale identity codas function as symbolic markers of cultural identity, at least for Pacific Ocean clans. The full reasoning behind why the authors used the term “symbolic markers” is given in that paper, but briefly, they found evidence that identity coda usage becomes more distinct as clan overlap increases, while non-identity coda usage does not change. This matches theoretical and empirical work on human symbolic markers[L1, L2, L10, L11].

Action - We retain the use of the term here, as defined in the works cited, and based on its prior usage in the study of both human and non-human cultures.

Comment 28

Line 50: This statement is not technically accurate. The use of a signal as a marker by individuals can only be determined by how individuals ”interpret” and react to that signal - e.g., via playback experiments - it cannot be determined by how different populations use and produce the signals.

We respectfully disagree. While we agree that the optimal situation would be that of playback, the contextual use can provide insight into the functional use of signals; as can expected patterns of use and variation, as was tested in the papers we cite. However, this argument is not the scope nor the synthesis of this paper. These statements are supported by existing published works, as cited, and we encourage the reviewer to take exception with those papers.

Comment 29

Line 69: ”Meaningful speech characteristics”??? These terms do not logically or technically follow the previous statement. Why not stay faithful to the results and state that the method used seems to be valid and reliable because it confirms former studies and methods?

Action - Reworded to better underline the method’s results with previous studies

Comment 30

Lines 72-74: This statement doesn’t seem to accurately capture/explain/resume the difference between ID and non-ID codas.

We are not sure what the reviewer is referring to in this case. The sentence in this case was meant to explain the different relations that ID/non-ID codas have with clan sympatry.

Comment 31

Line 75: The information provided in the few previous sentences does not allow the reader to understand why these results support the notion that cultural transmission and social learning occurs between clans.

We conclude out introduction with a brief summary of our overall findings, which we then use the rest of the manuscript to support these statements.

Comment 32

Table 1: So far, the authors refer to their analyses as capturing the ”rhythm” of whale clicks. Consequently, it is not readily clear at this point why the authors rely on ”ICIs” (inter click intervals) instead of the ”universal” measure used across taxa to capture the rhythm of signal sequences - IOIs (inter onset intervals). If ICIs are the same measure as IOIs, why not use the common term, instead of creating a new term name? Alternatively, if ICIs are not equivalent to IOIs, then arguably the analyses do not capture the ”rhythm” of whale clicks, as claimed by the authors. Any rhythmic claim will need to be based on IOI measures. In animal behaviour, stereotyped is primarily used to describe pathological, dysfunctional behaviour. I suggest the use of other adjective, such as ”regular”, ”repetitive”, ”recurring”, ”predictable”. Another deviation from typical terminology: ”usage frequency” -¿ ”production rate”. Why is a clan a ”higher-order” level of social organization? This requires explanation, at least a mention, of what are the ”lower-order” levels. To the non-expert reader, there is a logical circularity/gap here: Clans are said to produce clan-specific codas, and then, it is said that codas are used to delineate clans. Either one deduces, or one infers, but not both. This raises the question, are clans confirmed by any other means than codas?

We are not creating a “new term name”: inter-click interval (ICI) is the standard terminology used in odontocete (toothed whale) research. We take the reviewer’s point that some readers will not be coming to our paper with that background, however, and now explicitly point out that ICI is synonymous with IOI for sperm whales. Please see our response to your earlier comment for more on this point.

Comment 33

Line 92: Unclear term, ”sub-sequence”. Fig. 1B doesn’t seem to readily help disambiguate the meaning of the term.

In fact reference to Fig. 1B is misplaced as it does not refer to the text. A sub-sequence is simply a contiguous subset of a coda, a subset of it.

Action - Removed ambiguous reference to Fig. 1B

Comment 34

Line 94: How does the use of ”sequence” compare here with ”sub-sequence” above?

In fact its the same situation although the previous comment highlighted a source of ambiguity.

Action - Reworded the sentence to be less confusing.

Comment 35

Line 95: Signal sequences don’t ”contain” memory, they require memory for processing.

Action - Rephrased from “sequences contain memory” to “states depend on previous sequences of varying length”.

Comment 36

Lines 95-97: The analogy with human language seems forced, combinatorics in any given species are expected to entail different transitions between unit/unit-sequences.

Thank you for the comment. Indeed, the purpose of the analogy is to illustrate how variable length Markov Chains work (which have been shown to be good at discerning even accents of the same language). We used human language as an analogy to provide the readers’ with a more intuitive understanding of the results.

Action - Revised paragraph to read: “Despite we do not have direct evidence of unitary blocks in sperm whale communication, on can imagine this effect similarly to what happens with words (e.g., a word beginning with “re” can continue in more ways than one starting with “zy”).”

Comment 37

Line 97: Unclear which possibility is this.

Action - Made the wording clearer.

Comment 38

Line 99: Invocation of memory, although common in the use of Markov chains, in inadequate here given that the research did not study how individuals perceived or processed click sequences, only how individual produced click sequences. If the authors are referring to the cognitive load imposed by producing clicks sequences, terms such as ”sequence planning” will be more accurate.

Here, we use the term “fixed-memory” in relation to the definition of a variable length Markov model. We feel that, in this section of the manuscript, the context is clear that it is a mathematical definition and in no way invokes the biological idea of memory or cognition. It is rather standard to use memory to describe the order of Markov chains. Swapping words in the definition of mathematical objects when the context is clear seems to cause unnecessary ambiguity.

Action - We clarified this in the manuscript (see comments above).

Reviewer #3 (Recommendations):

Comment 39

Line 16: Add ”broadly defined” as there are many other more restricted definitions (see for example Tomasello 1999; 2009). Tomasello M (1999) The cultural origins of human cognition. Harvard University Press, Cambridge Tomasello M (2009) The question of chimpanzee culture, plus postscript (chimpanzee culture 2009). In: Laland KN, Galef BG (eds) The question of animal culture. Harvard University Press, Cambridge, pp 198-221.

Thanks for the clarification.

Action - We added the term “broadly” and added the last reference.

Comment 40

Line 22: Is all stable social learned behavior that becomes idiosyncratic and ”distinguishable” considered symbolic markers? If not, consider adding ”potentially.”

No, but the evolution of cultural groups with differing behavior can reorganize the selective environment in such a way that it can favour an in-group bias that was not initially advantageous to individuals and lead to a preference towards others who share an overt symbolic marker that initially had no meaning and a random frequency in both populations. That is to say, even randomly assigned trivial groups can evolve arbitrary symbolic markers through in-group favouritism once behavioural differences exist even in the absence of any history of rivalry, conflict, or competition between groups. See for example [L1, L2].

Comment 41

Table 1: Identity codas are defined as a ”Subset of coda types most frequently used by a sperm whale clan; canonically used to define vocal clans.” Therefore, I infer that an identity coda is not exclusively used by a specific clan and may be utilized by other clans, albeit less frequently. If this is the case, what criteria determine the frequency of usage for a coda to be categorized as an identity or non-identity coda? Does the criteria used to differentiate between ID and non-ID codas reflect the observed differences in micro changes between the two and within clans?

The methods for this categorization are defined, discussed, and justified in previous work in [L9, L12]. We feel its outside the scope of this paper to review these details here in this manuscript. However, the differences between vocal styles discussed here and the frequency production repertoires which allow for the definition of identity codas are on different scales. The differences between identity and non-identity codas are not the observed differences in vocal style reported here.

Comment 42

Table 1: The definition of vocal style states that it ”Encodes the rhythmic variations within codas.” However, if rhythm changes, does the type of coda change as well? Typically, in musical terms, the component that maintains the structure of a rhythm is ”tempo,” not ”rhythm.” How much microvariation is acceptable to maintain the same rhythm, and when do these variations constitute a new rhythm?

Thank you for raising this important point about the relationship between rhythmic variations and coda categorization. In our definition, ”vocal style” refers to subtle, micro-level variations in the rhythmic structure of codas that do not alter their overarching categorical identity. These microvariations are akin to ”tempo” changes in musical terms, which can modify the expression of a rhythm without fundamentally altering its structure.

The threshold at which microvariations constitute a new rhythm, and thus a new coda type, remains an open question and is a limitation of current analytical approaches. In our study, we used established classification methods to group codas into types, treating variations within these groups as part of the same rhythm. Future work could refine these thresholds to better distinguish between meaningful rhythmic variation and the emergence of new coda types.

Comment 43

Table 1: Change ”say” to ”vocalize” (similarly as used in line 273 for humpback whales ”vocalizations”).

Thanks.

Action - Done.

Comment 44

Lines 33-35 and Figure 1-C: Can a lay listener discern the microvariations within each coda type by ear? Consider including sound samples of individual rhythmic microvariations for the same coda type pattern (e.g., Four plus, Palindrome, Plus One, Regular) to provide readers/listeners with an impression of their detectability. If authors considered too much or redundant Supplemental material at least give a sound sample for each the 4 subcodas modeled structures examples of 4R2 coda variations depicted in Figure 1-C so the reader can have an acoustic impression of them.

We do not think that human listeners would be able to all of the variation detected here. However, this does not mean that it is not important variation for the whales. Human observers being able to classify call variation aurally shouldn’t be seen as a bar representing important biological variation for non-human species, given that their hearing and vocal production systems have evolved independently. Importantly, ’Four Plus’,’Palindrome’, etc are names of Clans; sympatric, but socially segregated, communities of whale families, which share a distinct vocal dialect of coda types. These clans each have have distinguishable coda dialects made up of dozens of coda types (and delineated based on identity codas), these are not names/categorical coda types themselves.

Action - We now provide audio samples of all coda types listed in Figure 1B in the paper’s Github repository.

Comment 45

Line 69: As stated above, it may be confusing to refer to it as ”speech.” I suggest adding something like: ”Our method does capture one essential characteristic of human speech: phonology.” Reply 45.—Thank you for drawing our attention to this.

Action - We removed the word “speech” from the manuscript, using “communication” and/or “vocalization” depending on the context.

Comment 46

Line 111-112: Consider adding a sound sample of the variation of the 4R2 coda type that can be vocalized as BCC but also as CBB as supplementary data.

What the reviewer has correctly observed is that the traditional categorical coda type ’names’ do not capture the variation within a type by rhythm nor by tempo.

Action - We have added samples of all coda types listed in Figure 1B in the paper’s Github repo.

Comment 47

Figure 3: Include a sound sample for each of the 7 coda types in Figure 1B (”specific vocal repertoires”) to illustrate the set of coda types used and their associated usage frequencies, or at least for each of the 7 coda types in Figure 3 and tables S1 and S2.

Sperm whales in the Eastern Caribbean produce dozens of rhythm types across at least five categorical tempo types [L8, L13]. The coda types represented in Figure 1B do not demonstrate all the variability inherent in the sperm whales’ vocal dialect. Importantly, Figure 3, as well as table S1 and S2, refer to clan-level dialects not specific individual coda types.

Action - We added sound samples for each coda rhythm type listed in Figure 1B to the Github repository.

Comment 48

Lines 184-190: It is unclear what human analogy term is used for ID codas. This needs clarification.

We are not making an analogy in humans for the role of ID vs non-ID codas, but only providing the example of accents as changes in vocalization (style) without a change in the actual words used (repertoire).

Action - We tried to make it clearer in the manuscript.

Comment 49

Line 190: Change ”whale speech” to ”whale vocalizations.”

Thanks.

Action - Done.

Comment 50

Figure 4: Correct citation number Hersh ”10” to Hersh ”11.”

Thanks.

Action - Fixed the reference.

Comment 51

Lines 224-232: Clarify whether the reference to how spatial overlap affects the frequency of ID codas refers to shared ID codas between clans or the production frequency of each coda within the total repertoire of codas.

The similarity between ID coda repertoires we are referring to there is based on the ID codas of both clans.

More details on the comparison can be found in [L9].

Action - We added a sentence explaining the comparison is made using the joint set of ID codas.

Comment 52

Lines 240-241: What are non-ID codas vocal cues for?

Non-ID codas likely serve as flexible, context-dependent signals that facilitate group coordination, convey environmental or social context, and promote social learning, especially in mixed-clan or overlapping habitats. Their variability suggests multifunctional roles shaped by ecological and social pressures.

Comment 53

Lines 267-268: It’s unclear whether non-ID coda vocal styles are genetically inherited or not, as argued in lines 257-258.

We did not intend to argue that non-ID coda vocal styles are genetically inherited. Instead, we aimed to present a hypothetical consideration: if non-ID coda vocal styles were genetically inherited, one would expect a direct correlation between vocal style similarity and genetic relatedness. This hypothetical framework was introduced to strengthen our argument that the observed patterns are unlikely to be explained by genetic inheritance, as such correlations have not been observed. While we acknowledge that we lack definitive proof to rule out genetic influences entirely, the evidence available strongly suggests that social learning, rather than genetic transmission, is the more plausible mechanism.

Action - Clarified in manuscript.

Comment 54

Line 277: Can males mate with females from different clans?

Yes, genetic evidence shows that males may even switch ocean basins.

Action - We have clarified that we mean the female members of units from different clans have only rarely been observed to interact at sea between clans.

Comment 55

Lines 287-292: Consider discussing the difference between controlled/voluntary and automatic/involuntary imitation and their implications for cultural selection and social learning (see Heyes 2011; 2012). Heyes, C. (2011). Automatic imitation. Psychological bulletin, 137(3), 463. Heyes, C. (2012). What’s social about social learning?. Journal of comparative psychology, 126(2), 193.

Thank you for your insightful comment regarding this. The distinction between controlled/voluntary and automatic/involuntary imitation, as highlighted by Heyes [L14, L15], provides a potentially valuable framework for interpreting social learning mechanisms in sperm whales. Automatic imitation refers to reflexive, often unconscious mimicry driven by perceptual or motor coupling, while controlled imitation involves deliberate and goal-directed efforts to replicate behaviors. Both forms likely play complementary roles in the cultural transmission observed in sperm whales.

This dual-process perspective highlights the potential for cultural selection to act at different levels. Automatic imitation may drive convergence in shared environments, promoting acoustic homogeneity and facilitating inter-clan communication. In contrast, controlled imitation ensures the preservation of clan-specific vocal traditions, maintaining cultural diversity. This interplay between automatic and controlled processes could reflect a balancing act between cultural assimilation and differentiation, underscoring the adaptive value of these mechanisms in dynamic social and ecological contexts.

Action - We have incorporated a short discussion of this distinction and its implications for our findings in the Discussion. Additionally, we have cited [L14, L15] to provide theoretical grounding for this interpretation.

Comment 56

Methods: Consider integrating the paragraph from lines 319-321 into lines 28-35 and eliminate redundant information.

Thanks.

Action - We implemented the suggestion, removing the first paragraph of the Dataset description and integrating the information when we introduce the concepts of codas and clicks.

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[L3] L. S. Burchardt and M. Knornschild, PLoS Computational Biology 16, e1007755 (2020).

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[L9] T. A. Hersh, S. Gero, L. Rendell, M. Cantor, L. Weilgart, M. Amano, S. M. Dawson, E. Slooten, C. M. Johnson, I. Kerr, et al., Proc. Natl. Acad. Sci. 119, e2201692119 (2022).

[L10] R. Boyd and P. J. Richerson, Cult Anthropol 2, 65 (1987). [L11] E. Cohen, Curr. Anthropol. 53, 588 (2012).

[L12] T. A. Hersh, S. Gero, L. Rendell, and H. Whitehead, Methods Ecol. Evol. 12, 1668 (2021), ISSN 2041-210X, 2041-210X.

[L13] S. Gero, A. Bøttcher, H. Whitehead, and P. T. Madsen, R. Soc. Open Sci. 3, 160061 (2016).

[L14] C. Heyes, Psychological Bulletin 137, 463 (2011).

[L15] C. Heyes, Journal of Comparative Psychology 126, 193 (2012).

eLife Assessment

This fundamental study highlights potential mechanisms underlying the sex-dependent bias in susceptibility to gut colonization by Methicillin-resistant Staphylococcus aureus (MRSA). The evidence supporting the conclusion is compelling. The work will interest biologists who study intestinal infection and immunity.

Reviewer #1 (Public review):

Summary:

Lejeune et al. demonstrated sex-dependent differences in the susceptibility to MRSA infection. The authors demonstrated the role of the microbiota and sex hormones as potential determinants of susceptibility. Moreover, the authors showed that Th17 cells and neutrophils contribute to the sex hormone-dependent protection in female mice.

Strengths:

The role of microbiota was examined in various models (germ-free, co-housing, microbiota transplantation). The identification of responsible immune cells was achieved using several genetic knockouts and cell-specific depletion models. The involvement of sex hormones was clarified using ovariectomy and the FCG model.

Weaknesses:

The specific microbial species/strains responsible for the protection, as well as the mechanisms by which these bacteria regulate sex hormone-mediated protection, remain unclear. However, this does not diminish the conceptual significance of the study.

Comments on revisions:

The authors have adequately addressed my previous concerns, and the revised manuscript shows significant improvement.

Reviewer #3 (Public review):

Summary:

Using a mouse model of Staphylococcus aureus gut colonization Lejeune et al demonstrate that the microbiome, immune system, and sex are important contributing factors for whether this important human pathogen persists in the gut. The work begins by describing differential gut clearance of S. aureus in female B6 mice bred at NYU compared to those from Jackson Laboratories (JAX). NYU female mice cleared S. aureus from the gut but NYU male mice and mice of both sexes from JAX exhibited persistent gut colonization. Further experimentation demonstrated that differences between staphylococcal gut clearance in NYU and JAX female mice were attributed to the microbiome. However, NYU male and female mice harbor similar microbiomes, supporting the conclusion that the microbiome cannot account for the observed sex-dependent clearance of S. aureus gut colonization. To identify factors responsible for female clearance of S. aureus, the authors performed RNAseq on intestinal epithelia cells and cells enriched within the lamina propria. This analysis revealed sex-dependent transcriptional responses in both tissues. Genes associated with immune cell function and migration were distinctly expressed between the sexes. To determine which immune cell types contribute to S. aureus clearance Lejeune et al employed genetic and antibody-mediated immune cell depletion. This experiment demonstrated that CD4+ IL17+ cells and neutrophils promote elimination of S. aureus from the gut. Subsequent experiments, including the use of the 'four core genotype model' were conducted to discern between the roles of sex chromosomes and sex hormones. This work demonstrated that sex-chromosome linked genes are not responsible for clearance, increasing the likelihood that hormones play a dominant role in controlling S. aureus gut colonization.

Strengths:

A strength of the work is the rigorous experimental design. Appropriate controls were executed and, in most cases, multiple approaches were conducted to strengthen the authors' conclusions. The conclusions are supported by the data.<br /> The following suggestions are offered to improve an already strong piece of scholarship.

Weaknesses:

The correlation between female sex hormones and elimination of S. aureus from the gut could be further validated by quantifying sex hormones produced in the four core genotype mice in response to colonization. Additionally, and this may not be feasible, but according to the proposed model administering female sex hormones to male mice should decrease colonization. Finally, knowing whether the quantity of IL-17a CD4+ cells change in the OVX mice has the potential to discern whether the abundance/migration of the cells or their activation is promoted by female sex hormones.

In the Discussion the authors highlight previous work establishing a link between immune cells and sex hormone receptors, but whether the estrogen (and progesterone) receptor is differentially expressed in response to S. aureus colonization could be assessed in the RNAseq dataset. Differential expression of known X and Y chromosome linked genes were discussed but specific sex hormones or sex hormone receptors, like the estrogen receptor were not. This potential result could be highlighted.

Comments on revisions:

The authors have adequately addressed my comments. I have only one minor adjustment: the Esr1 mice should be included the Materials and Methods.

Author response:

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

Reviewer #1 (Public review):

Summary:

Lejeune et al. demonstrated sex-dependent differences in the susceptibility to MRSA infection. The authors demonstrated the role of the microbiota and sex hormones as potential determinants of susceptibility. Moreover, the authors showed that Th17 cells and neutrophils contribute to sex hormone-dependent protection in female mice.

Strengths:

The role of microbiota was examined in various models (gnotobiotic, co-housing, microbiota transplantation). The identification of responsible immune cells was achieved using several genetic knockouts and cell-specific depletion models. The involvement of sex hormones was clarified using ovariectomy and the FCG model.

Weaknesses:

The mechanisms by which specific microbiota confer female-specific protection remain unclear.

We thank the reviewer for highlighting the strengths of the manuscript including the models and techniques we employ. We agree that the relationship between the microbiota and sex-dependent protection is less developed compared with other aspects of the study. As detailed below, we are attempting to identify specific microbes that confer femalespecific protection and links with sex hormones. We have promising but preliminary results. Thus, in our revised manuscript, we added new data on the host response as suggested by the detailed comments from the Reviewers. We also elaborate on the potential role of the microbiota in the discussion section.

Reviewer #1 (Recommendations for the authors):

(1) The authors nicely showed that the transfer of the protective phenotype by FMT requires the female sex in recipients (Figure 2E). However, it remains unclear whether the female sex is required to develop protective microbiota in donor mice, as only the female NYU donor-male Jax recipient combination was tested. What happens if the microbiota from male NYU mice is transplanted into female Jax mice? If sex hormones act only on the downstream of the microbiota, such mice would show the protective phenotype. However, if sex hormones are required to establish a protective microbiota, the transplantation of microbiota from male NYU mice will not confer protection in recipient female Jax mice.

The Reviewer’s comment is well taken. We have not conducted the suggested experiment of FMT from male NYU mice to JAX female mice yet because we are pursuing an in vitro approach that we hope will eventually provide a more definitive answer. We observed that stool from female NYU mice and not JAX mice inhibits MRSA when cultured under anaerobic conditions, and this inhibitory activity is eliminated by filtration (Author response image 1A). We also observed that stool from male NYU mice inhibits MRSA growth to a similar extent as stool from female NYU mice (Author response image 1B). This result suggests that the protective role of sex hormones is downstream of the microbiota. We are in the process of identifying the specific microbiota member to support this conclusion.

Author response image 1.

Stool from NYU mice inhibits MRSA growth in vitro. (A) MRSA CFU/mL in media (TSB) following culture with unfiltered or filtered stool homogenate from female NYU or JAX mice. Stool homogenate or TSB alone was added in a 1:1 ratio to 1x106 CFU/mL MRSA and cultured anaerobically for up to 24 hours. (B) MRSA CFU/mL in TSB following culture with unfiltered stool homogenate from NYU male or female mice. Stool homogenate or TSB alone was added in a 1:1 ratio to 1x106 CFU/mL MRSA. 3 experimental replicates performed; stool taken from 6 individual mice per condition. Mean MRSA burden ± SEM. Area under the curve analysis + One way ANOVA with Sidak’s multiple comparisons test. ns: not significant.

(2) The results clearly showed the involvement of the specific microbiota in NYU mice in the sex-dependent bias in susceptibility to MRSA. However, the mechanisms by which specific microbiota promotes female sex-mediated protection need to be better described. Is this simply attributed to the different Th17 cell numbers in NYU and Jax mice (i.e., increased commensalspecific Th17 cells in NYU like Taconic mice)? Or is it possible that NYU microbiota impacts the regulation of sex hormones or their downstream signaling? What about the level of sex hormones in NYU and Jax mice? Are these levels equivalent or different? Do NYU and Jax microbiotas regulate the expression of sex hormone receptors in immune cells differently?

These are great questions. We do not observe baseline differences in Th17 cells like JAX versus Taconic mice (Figure 5B), suggesting that the mechanism is different. However, it is quite possible that an antigen-specific T cells, or Th17 cell specifically, is present at low levels and expands rapidly upon MRSA colonization. We have added this possibility to the discussion in the revised manuscript. To address the Reviewer’s question about the effect of the microbiota on sex hormones, we first sought to determine which sex hormone is necessary. Using estrogen receptor knockouts (Esr1^-/-), we were able to implicate estrogen and have added this important finding to the manuscript (Fig 6C). Then, we measured levels of estradiol in stool samples but did not observe a difference between NYU and JAX female mice (Author response image 2). We provide the results below but did not add it to the revised manuscript because we found it difficult to draw a conclusion without more extensive profiling as well as quantification of the receptor on specific immune cell subsets and cell-type specific knockouts. Also, see our response to Reviewer #3 regarding receptor expression. Although we have yet to explain the role of the microbiota, we hope the Reviewer agrees that we have promising yet preliminary results and that the new experiments we added to the manuscript have further strengthened the mechanism on the host-side. 

Author response image 2.

Estradiol levels in stool samples prior to MRSA inoculation. (A) Estradiol levels in stool samples collected prior to MRSA inoculation in male and female mice bred at NYU or purchased from Jackson Labs. Frozen stool samples were normalized by weight and processed using the DetectX® Estradiol ELISA Kit (Arbor Assays).

(3) The authors claimed that Th17-mediated recruitment of neutrophils likely promotes the clearance of MRSA in female NYU mice. However, the experimental evidence supporting this claim could be stronger. The authors should show the neutrophil recruitment in the gut mucosa in female and male NYU mice. Also, the levels of neutrophils between NYU and Jax female mice should be examined. To further strengthen the link between Th17 and neutrophils, it would be ideal to analyze neutrophil recruitment in mice lacking Th17 cells (i.e., Rag2-/-, anti-CD4 treated, Rorgt-/- mice).

We agree and now include a more detailed analyses of neutrophils. We found that the number of neutrophils in the intestine were not higher in NYU female mice compared with NYU male mice, with or without MRSA. Instead, we show that neutrophils in NYU female mice display higher levels of surface CD11b, a sign of activation, compared to males following inoculation with MRSA . We have added these findings to the revised manuscript (Fig5 H and I). IL-17 can activate neutrophils and increase their antimicrobial activity. Consistent with this possibility, we now show that female mice lacking the IL-17 receptor lose the enhanced colonization resistance. Based on these findings, we have modified this aspect of the conclusion, and thank the reviewer for the helpful suggestion.

Reviewer #2 (Public review):

The current study by Lejeune et al. investigates factors that allow for persistent MRSA infection in the GI tract. They developed an intriguing model of intestinal MRSA infection that does not use the traditional antibiotic approach, thereby allowing for a more natural infection that includes the normal intestinal microbiota. This model is more akin to what might be expected to be observed in a healthy human host. They find that biological sex plays a clear role in bacterial persistence during infection but only in mice bred at an NYU Facility and not those acquired from Jackson Labs. This clearly indicates a role for the intestinal microbiome in affecting female bacterial persistence but not male persistence which was unaffected by the origin of the mice and thus the microbiome. Through a series of clever microbiome-specific transfer experiments, they determine that the NYU-specific microbiome plays a role in this sexual dimorphism but is not solely responsible. Additional experiments indicate that Th17 cells, estrogen, and neutrophils also participate in the resistance to persistent infection. Notably, they assess the role of sex chromosomes (X/Y) using the established four core genotype model and find that these chromosomes appear to play little role in bacterial persistence.

Overall, the paper nicely adds to the growing body of literature investigating how biological sex impacts the immune system and the burden of infectious disease. The conclusions are mostly supported by the data although there are some aspects of the data that could be better addressed and clarified.

We thank the Reviewer for appreciating our contribution and these supportive comments. We have added several experiments to fill-in gaps and text revisions to increase clarity and acknowledge limitations. 

(1) There is something of a disconnect between the initial microbiome data and the later data that analyzes sex hormones and chromosomes. While there are clearly differences in microbial species across the two sites (NYU and JAX) how these bacterial species might directly interact with immune cells to induce female-specific responses is left unexplored. At the very least it would help to try and link these two distinct pieces of data to try and inform the reader how the microbiome is regulating the sex-specific response. Indeed, the reader is left with no clear exploration of the microbiota's role in the persistence of the infection and thus is left wanting.

We agree. This comment is similar to Reviewer #1’s feedback. As mentioned above, we are attempting to clarify the association between sex differences and the microbiota and have included preliminary results for the Reviewers. However, addressing this disconnect will require substantially more investigation. Instead, we have added insightful new data that elaborate on aspects of the host response.  We hope the Reviewer agrees that revised manuscript is stronger and that further delineation of the microbiota can be addressed by future studies.

(2) While the authors make a reasonable case that Th17 T cells are important for controlling infection (using RORgt knockout mice that cannot produce Th17 cells), it is not clear how these cells even arise during infection since the authors make most of the observations 2 days postinfection which is longer before a normal adaptive immune response would be expected to arise. The authors acknowledge this, but their explanation is incomplete. The increase in Th17 cells they observe is predicated on mitogenic stimulation, so they are not specific (at least in this study) for MRSA. It would be helpful to see a specific restimulation of these cells with MRSA antigens to determine if there are pre-existing, cross-reactive Th17 cells specific for MRSA and microbiota species which could then link these two as mentioned above.

We acknowledge that this is a limitation of our study. Although an experiment demonstrating pre-existing, cross-reactive T cells would help support our conclusion, aspects of MRSA biology may make the results of this experiment difficult to interpret. We have consulted with an expert on MRSA virulence factors, co-lead author Dr. Victor Torres, about the feasibility of this experiment. MRSA possess superantigens, such as Staphylococcal enterotoxin B, which bind directly to specific Vβ regions of T-cell receptors (TCR) and major histocompatibility complex (MHC) class II on antigen-presenting cells, resulting in hyperactivation of T lymphocytes and monocytes/macrophages. Additionally, other MRSA virulence factors, such as α-hemolysin and LukED, induce cell death of lymphocytes. MRSA’s enterotoxins are heat stable, so heat-inactivation of the bacterium may not help in this matter.  For these reasons, it is unlikely that we can perform a simple restimulation of lymphocytes with MRSA antigens. 

A study by Shao et al. provides an example of a host commensal species inducing Th17 cells with cross-reactivity against MRSA. Upon intestinal colonization, the intestinal fungus Candida albicans influences T cell polarization towards a Th17 phenotype in the spleen and peripheral lymph nodes which provided protection to the host against systemic candidemia. Interestingly, this induction of protective Th17 cells, increased IL-17 and responsiveness in circulating Ly6G+ neutrophils also protected mice from intravenous infection with MRSA, indicating that T cell activation and polarization by intestinal C. albicans leads to non-specific protective responses against extracellular pathogens.

Shao TY, Ang WXG, Jiang TT, Huang FS, Andersen H, Kinder JM, Pham G, Burg AR, Ruff B, Gonzalez T, Khurana Hershey GK, Haslam DB, Way SS. Commensal Candida albicans Positively Calibrates Systemic Th17 Immunological Responses. Cell Host & Microbe. 2019 Mar 13;25(3):404-417.e6. doi: 10.1016/j.chom.2019.02.004. PMID: 30870622; PMCID: PMC6419754.

We have added a brief version of the above discussion in the revised manuscript. Also, as mentioned earlier, we have added new data strengthening the axis between Th17 and neutrophils, including showing that IL-17 receptor is necessary and that neutrophils display signs of heightened activation in female mice during MRSA colonization.   

(3) The ovariectomy experiment demonstrates a role for ovarian hormones; however, it lacks a control of adding back ovarian hormones (or at least estrogen) so it is not entirely obvious what is causing the persistence in this experiment. This is especially important considering the experiments demonstrating no role for sex chromosomes thus demonstrating that hormonal effects are highly important. Here it leaves the reader without a conclusive outcome as to the exact hormonal mechanism.

This is a great suggestion. Rather than adding back ovarian hormones, we performed the more direct experiment and tested whether the estrogen receptor (ERα, encoded by Esr1) is necessary for the enhanced colonization resistance. Indeed, we observed that Esr1^-/- female mice have increased MRSA burden compared to Esr1^+/- littermates. We have added this new result (Figure 6C) and thank the Reviewer for their guidance. 

4) The discussion is underdeveloped and is mostly a rehash of the results. It would greatly enhance the manuscript if the authors would more carefully place the results in the context of the current state of the field including a more enhanced discussion of the role of estrogen, microbiome, and T cells and how the field might predict these all interact and how they might be interacting in the current study as well.

Author response: We thank the Reviewer for their feedback in improving the scholarship on the manuscript. We have expanded on the literature and the mechanistic model in both the discussion section and other parts to provide better context for our findings. 

Reviewer #3 (Public review):

Summary:

Using a mouse model of Staphylococcus aureus gut colonization, Lejeune et al. demonstrate that the microbiome, immune system, and sex are important contributing factors for whether this important human pathogen persists in the gut. The work begins by describing differential gut clearance of S. aureus in female B6 mice bred at NYU compared to those from Jackson Laboratories (JAX). NYU female mice cleared S. aureus from the gut but NYU male mice and mice of both sexes from JAX exhibited persistent gut colonization. Further experimentation demonstrated that differences between staphylococcal gut clearance in NYU and JAX female mice were attributed to the microbiome. However, NYU male and female mice harbor similar microbiomes, supporting the conclusion that the microbiome cannot account for the observed sex-dependent clearance of S. aureus gut colonization. To identify factors responsible for female clearance of S. aureus, the authors performed RNAseq on intestinal epithelial cells and cells enriched within the lamina propria. This analysis revealed sexdependent transcriptional responses in both tissues. Genes associated with immune cell function and migration were distinctly expressed between the sexes. To determine which immune cell types contribute to S. aureus clearance Lejeune et al employed genetic and antibody-mediated immune cell depletion. This experiment demonstrated that CD4+ IL17+ cells and neutrophils promote the elimination of S. aureus from the gut. Subsequent experiments, including the use of the 'four core genotype model' were conducted to discern between the roles of sex chromosomes and sex hormones. This work demonstrated that sex-chromosome-linked genes are not responsible for clearance, increasing the likelihood that hormones play a dominant role in controlling S. aureus gut colonization.

Strengths:

A strength of the work is the rigorous experimental design. Appropriate controls were executed and, in most cases, multiple approaches were conducted to strengthen the authors' conclusions. The conclusions are supported by the data.

The following suggestions are offered to improve an already strong piece of scholarship.

Weaknesses:

The correlation between female sex hormones and the elimination of S. aureus from the gut could be further validated by quantifying sex hormones produced in the four core genotype mice in response to colonization. Additionally, and this may not be feasible, but according to the proposed model administering female sex hormones to male mice should decrease colonization. Finally, knowing whether the quantity of IL-17a CD4+ cells change in the OVX mice has the potential to discern whether abundance/migration of the cells or their activation is promoted by female sex hormones.

In the Discussion, the authors highlight previous work establishing a link between immune cells and sex hormone receptors, but whether the estrogen (and progesterone) receptor is differentially expressed in response to S. aureus colonization could be assessed in the RNAseq dataset. Differential expression of known X and Y chromosome-linked genes were discussed but specific sex hormones or sex hormone receptors, like the estrogen receptor, were not. This potential result could be highlighted.

We appreciate the comment on the scholarship and thank the Reviewer for the insightful suggestions to improve this manuscript. We apologize for not including references that address some of the Reviewer’s questions. Other research groups have compared the levels of hormones between XX and XY males and females in the four core genotypes model and have found similar levels of circulating testosterone in adult XX and XY males. No difference was found in circulating estradiol levels in XX vs XY- females when tested at 4-6 or 79 months of age. 

Karen M. Palaszynski, Deborah L. Smith, Shana Kamrava, Paul S. Burgoyne, Arthur P. Arnold, Rhonda R. Voskuhl, A Yin-Yang Effect between Sex Chromosome Complement and Sex Hormones on the Immune Response. Endocrinology, Volume 146, Issue 8, 1 August 2005, Pages 3280–3285, https://doi.org/10.1210/en.2005-0284

Sasidhar MV, Itoh N, Gold SM, Lawson GW, Voskuhl RR. The XX sex chromosome complement in mice is associated with increased spontaneous lupus compared with XY. Ann Rheum Dis. 2012 Aug;71(8):1418-22. doi: 10.1136/annrheumdis-2011-201246. Epub 2012 May 12. PMID: 22580585; PMCID: PMC4452281.

Administering female sex hormones to males is a good idea. We did not observe an effect of injecting males with estrogen on MRSA colonization (data not shown), perhaps due to the dose or timing, or because it is not sufficient (i.e., additional hormones and factors may be required). Therefore, we analyzed the necessity of estrogen signaling and found that Esr1^-/- female mice impairs colonization resistance to MRSA. We have added this new experiment to the revised manuscript (Fig6 C).

Examination of the levels of estrogen, progesterone, and androgen receptors in our cecalcolonic lamina propria RNA-seq dataset is an excellent idea. We observed a significant increase in the G-protein coupled estrogen receptor 1 (Gper1) and a non-significant increase in Estrogen receptor alpha (Esr1) following MRSA inoculation in the immune cell compartment. This analysis has been added to the revised manuscript (Supplemental Fig6).

Reviewer #3 (Recommendations for the authors)

Minor editing issues:

The topic sentence of the last paragraph in the Results section states - 'male sex defining gene sex determining region Y (Sry) has been moved from the Y chromosome to an autosome'. 'Sex defining gene' and sex-determining region seems redundant in this context. A sex-defining gene would presumably be located within a sex-determining region.

Bold the letter 'F' in the Figure 5 legend.

It's not clear from the Figure 6E legend when the IL-17A+ CD4+ cells were quantified, 2 dpi?

In the third sentence of the second paragraph of the Discussion, the two references are merged together.

We thank the Reviewer for pointing out these editing issues. They have been addressed in the revised manuscript.

eLife Assessment

This important study identifies one way in which episodic heat exposure can result in negative changes in motivated and affective behaviors. This work positively expands the field of thermoregulation. The data were collected using a myriad of next-generation approaches, including extensive behavior testing, thermal monitoring, electrophysiology, circuit mapping, and manipulations. There is convincing evidence that neurons of the paraventricular thalamus change plastically over three weeks of episodic heat stimulation this affects behavioral outputs such as social interactions and anxiety-related behavior. Conclusions regarding the specificity of the POA-pPVT pathway compared to other inputs to the PVT in the control of observed effects would benefit from further validation. The study will be of interest to behavioral neuroscientists, climate/environmental biologists, and pre-clinical neuropsychiatrists.

Reviewer #1 (Public review):

Summary:

The manuscript by Cao et al. examines an important but understudied question of how chronic exposure to heat drives changes in affective and social behaviors. It has long been known that temperature can be a potent driver of behaviors and can lead to anxiety and aggression. However, the neural circuitry that mediates these changes is not known. Cao et al. take on this question by integrating optical tools of systems neuroscience to record and manipulate bulk activity in neural circuits, in combination with a creative battery of behavior assays. They demonstrate that chronic daily exposure to heat leads to changes in anxiety, locomotion, social approach, and aggression. They identify a circuit from preoptic area (POA) to posterior paraventricular thalamus (pPVT) in mediating these behavior changes. The POA-PVT circuit increases activity during heat exposure. Further, manipulation of this circuit can drive affective and social behavioral phenotypes even in the absence of heat exposure. Moreover, silencing this circuit during heat exposure prevents the development of negative phenotypes. Overall the manuscript makes an important contribution to the understudied area of how ambient temperature shapes motivated behaviors.

Strengths

The use of state-of-the-art systems neuroscience tools (in vivo optogenetics and fiber photometry, slice electrophysiology), chronic temperature-controlled experiments, and a rigorous battery of behavioral assays to determine affective phenotypes. The optogenetic gain of function of affective phenotypes in the absence of heat, and loss of function in the presence of heat are very convincing manipulation data. Overall a significant contribution to the circuit-level instantiation of temperature induced changes in motivated behavior, and creative experiments.

Weaknesses

The authors have fully addressed all of my questions and concerns, with the exception of one comment. They mention that they did carry out measurements of core body temperature as a control during optogenetic experiments and did not see any effects. However, I could only find this reported in the text but could not find the data in the main or supplementary figures.

Reviewer #2 (Public review):

Summary:

The study by Cao et al. highlights an interesting and important aspect of heat- and thermal biology: the effect of repetitive, long-term heat exposure and its impact on brain function.<br /> Even though peripheral, sensory temperature sensors and afferent neuronal pathways conveying acute temperature information to the CNS have been well established, it is largely unknown how persistent, long-term temperature stimuli interact with and shape CNS function, and how these thermally-induced CNS alterations modulate efferent pathways to change physiology and behavior. This study is therefore not only novel but, given global warming, also timely.

The authors provide compelling evidence that neurons of the paraventricular thalamus change plastically over three weeks of episodic heat stimulation and they convincingly show that these changes affect behavioral outputs such as social interactions, and anxiety related behaviors.

Strengths:

• It is impressive that the assessed behaviors can be (i) recruited by optogenetic fiber activation and (ii) inhibited by optogenetic fiber inhibition when mice are exposed to heat. Technically, when/how long is the fiber inhibition performed? It says in the text "3 min on and 3 min off". Is this only during the 20 minutes heat stimulation or also at other times?<br /> • It is interesting that the frequency of activity in pPVT neurons, as assessed by fiber photometry, stays increased after long-term heat exposure (day 22) when mice are back at normal room temperature. This appears similar to a previous study that found long-term heat exposure to transform POA neurons plastically to become tonically active (https://www.biorxiv.org/content/10.1101/2024.08.06.606929v1 ). Interestingly, the POA neurons that become tonically active by persistent heat exposure described in the above study are largely excitatory and thus these could drive the activity of the pPVT neurons analyzed in this study.<br /> How can it be reconciled that the majority of the inputs from the POA are found to be largely inhibitory (Fig. 2H)? Is it possible that this result stems from the fact that non-selective POA-to-pPVT projections are labelled by the approach used in this study and not only those pathways activated by heat? These points would be nice to discuss.<br /> • It is very interesting that no LTP can be induced after chronic heat exposure (Fig. K-M); the authors suggest that "the pathway in these mice were already saturated" (line 375). Could this hypothesis be tested in slices by employing a protocol to extinguish pre-existing (chronic heat exposure-induced) LTP? This would provide further strength to the findings/suggestion that an important synaptic plasticity mechanism is at play that conveys behavioral changes upon chronic heat stimulation.<br /> • It is interesting that long-term heat does not increase parameters associated with depression (Fig. 1N-Q), how is it with acute heat stress, are those depression parameters increased acutely? It would be interesting to learn if "depression indicators" increase acutely but then adapt (as a consequence of heat acclimation) or if they are not changed at all and are also low during acute heat exposure.

Reviewer #3 (Public review):

In this study, Cao et al. explore the neural mechanisms by which chronic heat exposure induces negative valence and hyperarousal in mice, focusing on the role of the posterior paraventricular nucleus (pPVT) neurons that receive projections from the preoptic area (POA). The authors show that chronic heat exposure leads to heightened activity of the POA projection-receiving pPVT neurons, potentially contributing to behavioral changes such as increased anxiety level and reduced sociability, along with heightened startle responses. In addition, using electrophysiological methods, the authors suggest that increased membrane excitability of pPVT neurons may underlie these behavioral changes. The use of a variety of behavioral assays enhances the robustness of their claim. Moreover, while previous research on thermoregulation has predominantly focused on physiological responses to thermal stress, this study adds a unique and valuable perspective by exploring how thermal stress impacts affective states and behaviors, thereby broadening the field of thermoregulation.

While the manuscript has been revised and some efforts have been made to address the reviewers' concerns, the majority of the issues raised remain insufficiently resolved. Therefore, the reviewer has highlighted key major points that the authors should address to strengthen the manuscript's conclusions.

Major points<br /> The manuscript highlights the increased activity in pPVT neurons receiving projections from the POA (Figure 3) and shows that these neurons are necessary for heat-induced behavioral changes (Figures 4N-W). However, it remains unclear whether the POA-to-pPVT projection itself plays a critical role. Since pPVT recipient neurons can receive inputs from various brain regions, the role of the POA input in driving these effects needs to be validated more explicitly.<br /> (1) To establish this, the authors should conduct experiments directly inhibiting the POA-to-pPVT projection and demonstrate whether the increased activity in pPVT neurons due to chronic heat exposure is abolished when the POA is blocked.<br /> (2) Alternatively, the authors could use anterograde labeling from the POA and specifically target recipient neurons in the pPVT to confirm that the observed excitatory inputs originate from the POA (related to Figure 6).<br /> (3) If these experiments are not feasible, the authors should consider toning down the emphasis on the POA's role throughout the manuscript and discussing this limitation explicitly. The term "POA recipient pPVT neurons" should be used consistently to avoid misleading implications that the POA-to-pPVT excitatory projection is definitively established as the key pathway.<br /> a) For example, in lines 368-369, the phrase "The increase in presynaptic excitability of the POA to pPVT excitatory pathway" represents a logical jump, as the data only support the "differential increase in presynaptic excitability of the excitatory pathway" (as described in lines 358-359) without specifically confirming the POA-to-pPVT pathway.<br /> b) Similarly, in lines 442-446, the statement "the role of excitatory projections from POA to pPVT in chronic heat exposure-induced emotional changes" should be revised to "the role of excitatory projection recipient pPVT in chronic heat~," as the data do not provide direct evidence that heat-responsive POA neurons projecting to pPVT mediate these effects. Such revisions would improve clarity and ensure that the conclusions remain aligned with the presented data.

Author response:

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

Reviewer #1 (Public review):

Summary:

The manuscript by Cao et al. examines an important but understudied question of how chronic exposure to heat drives changes in affective and social behaviors. It has long been known that temperature can be a potent driver of behaviors and can lead to anxiety and aggression. However, the neural circuitry that mediates these changes is not known. Cao et al. take on this question by integrating optical tools of systems neuroscience to record and manipulate bulk activity in neural circuits, in combination with a creative battery of behavior assays. They demonstrate that chronic daily exposure to heat leads to changes in anxiety, locomotion, social approach, and aggression. They identify a circuit from the preoptic area (POA) to the posterior paraventricular thalamus (pPVT) in mediating these behavior changes. The POA-PVT circuit increases activity during heat exposure. Further, manipulation of this circuit can drive affective and social behavioral phenotypes even in the absence of heat exposure. Moreover, silencing this circuit during heat exposure prevents the development of negative phenotypes. Overall the manuscript makes an important contribution to the understudied area of how ambient temperature shapes motivated behaviors.

Strengths:

The use of state-of-the-art systems neuroscience tools (in vivo optogenetics and fiber photometry, slice electrophysiology), chronic temperature-controlled experiments, and a rigorous battery of behavioral assays to determine affective phenotypes. The optogenetic gain of function of affective phenotypes in the absence of heat, and loss of function in the presence of heat are very convincing manipulation data. Overall a significant contribution to the circuit-level instantiation of temperature-induced changes in motivated behavior, and creative experiments.

Weaknesses：

(1) There is no quantification of cFos/rabies overlap shown in Figure 2, and no report of whether the POA-PVT circuit has a higher percentage of Fos+ cells than the general POA population. Similarly, there is no quantification of cFos in POA recipient PVT cells for Figure 2 Supplement 2.

Thanks for the comment. The quantification results of c-Fos signal have been provided in the main text and figures.  

(2) The authors do not address whether stimulation of POA-PVT also increases core body temperature in Figure 3 or its relevant supplements. This seems like an important phenotype to make note of and could be addressed with a thermal camera or telemetry.

Thanks for raising this point. We did indeed monitor the core body temperature during stimulation of POA-PVT pathway, but we did not observe any significant changes. We have included this finding in the revised manuscript.

(3) In Figure 3G: is Day 1 vs Day 22 "pre-heat" significant? The statistics are not shown, but this would be the most conclusive comparison to show that POA-PVT cells develop persistent activity after chronic heat exposure, which is one of the main claims the authors make in the text. This analysis is necessary in order to make the claim of persistent circuit activity after chronic heat exposure.

Figure 3G does compare the Day 1 preheat to Day22 preheat, and the difference was significant. The wording has been corrected to avoid confusion. Also, we have modified Figure 3D to 3H in our revised manuscript to improve the clarity of these plots.

(4) In Figure 4, the control virus (AAV1-EYFP) is a different serotype and reporter than the ChR2 virus (AAV9-ChR2-mCherry). This discrepancy could lead to somewhat different baseline behaviors.

Thanks for bringing out this issue. We acknowledge that using AA1-EGFP (a different serotype and reporter compared to the AAV9-ChR2-mCherry) as our control virus is not ideal. But based on our own prior experiments, we observed no significant differences in baseline behaviors between animals injected with AAV1 and AAV9 EYFP as well as control mice without virus injection. Therefore, we believe that the baseline behaviors of the animals were unaffected.

(5) In Figure 5G, N for the photometry data: the authors assess the maximum z-score as a measure of the strength of calcium response, however the area under the curve (AUC) is a more robust and useful readout than the maximum z score for this. Maximum z-score can simply identify brief peaks in amplitude, but the overall area under the curve seems quite similar, especially for Figure 5N.

Thanks for the comment. We agree with the reviewer that the area under the curve (AUC) is an alternative readout for measurement of the strength of calcium response. However, the reason why we chose the maximum z-score is based on the observation that we found POA recipient pPVT neurons after chronic heat treatment exhibited a higher calcium peak corresponding to certain behavioral performances when compared to pre-heat conditions. We thus applied the maximum z-score as a representative way to describe the neuronal activity changes of mice during certain behaviors before and after chronic heat treatment. The other consideration is that we want to reflect that POA recipient pPVT neurons become more sensitive and easier to be activated after chronic heat exposure under the same stressful situations compared to control mice. The maximum z score represented by peak in combination with particular behavioral performances is considered more suitable to highlight our findings in this study.

(6) For Fig 5V: the authors run the statistics on behavior bouts pooled from many animals, but it is better to do this analysis as an animal average, not by compiling bouts. Compiling bouts over-inflates the power and can yield significant p values that would not exist if the analysis were carried out with each animal as an n of 1.

Thanks for the comment and suggestion. We had tried both methods and the statistical results were similar. As suggested, we have updated Fig 5V, as well as Fig. 5H and 5O by comparing animal average in our revised manuscript.

(7) In general this is an excellent analysis of circuit function but leaves out the question of whether there may be other inputs to pPVT that also mediate the same behavioral effect. Future experiments that use activity-dependent Fos-TRAP labeling in combination with rabies can identify other inputs to heat-sensitive pPVT cells, which may have convergent or divergent functions compared to the POA inputs.

Thanks for the valuable suggestion, which would enhance the conclusion. We will consider adopting this approach in future investigations into this question.

Reviewer #2 (Public review):

Summary

The study by Cao et al. highlights an interesting and important aspect of heat- and thermal biology: the effect of repetitive, long-term heat exposure and its impact on brain function.

Even though peripheral, sensory temperature sensors and afferent neuronal pathways conveying acute temperature information to the CNS have been well established, it is largely unknown how persistent, long-term temperature stimuli interact with and shape CNS function, and how these thermally-induced CNS alterations modulate efferent pathways to change physiology and behavior. This study is therefore not only novel but, given global warming, also timely.

The authors provide compelling evidence that neurons of the paraventricular thalamus change plastically over three weeks of episodic heat stimulation and they convincingly show that these changes affect behavioral outputs such as social interactions, and anxiety-related behaviors.

Strengths

(1) It is impressive that the assessed behaviors can be (i) recruited by optogenetic fiber activation and (ii) inhibited by optogenetic fiber inhibition when mice are exposed to heat. Technically, when/how long is the fiber inhibition performed? It says in the text "3 min on and 3 min off". Is this only during the 20-minute heat stimulation or also at other times?

Thanks for pointing out the need for clarification. Our optogenetic inhibition had been conducted for 21 days during the heat exposure period (90 mins) for each mouse. And to avoid the light-induced heating effect, we applied the cyclical mode of 3 minutes’ light on and 3 minutes’ light off only during the process of heat exposure but not other time. The detailed description has been supplemented in the Method part of our revised manuscript.

(2) It is interesting that the frequency of activity in pPVT neurons, as assessed by fiber photometry, stays increased after long-term heat exposure (day 22) when mice are back at normal room temperature. This appears similar to a previous study that found long-term heat exposure to transform POA neurons plastically to become tonically active (https://www.biorxiv.org/content/10.1101/2024.08.06.606929v1). Interestingly, the POA neurons that become tonically active by persistent heat exposure described in the above study are largely excitatory, and thus these could drive the activity of the pPVT neurons analyzed in this study.

Thanks for pointing out this study that suggests similar plasticity of POA neurons under long-term heat exposure serving a different purpose. We have included this information in our discussion as well.  

(3) How can it be reconciled that the majority of the inputs from the POA are found to be largely inhibitory (Fig. 2H)? Is it possible that this result stems from the fact that non-selective POA-to-pPVT projections are labelled by the approach used in this study and not only those pathways activated by heat? These points would be nice to discuss.

Thanks for raising these important questions. Although it is not our primary focus, we are aware of the substantial inhibitory inputs from POA to pPVT which suggests an important function. However, we do not think that this pathway, which would exert an opposite effect on POA-recipient pPVT neurons compared to the excitatory input, contributes to the long-term effect of chronic heat exposure. This is due to the increased, rather than decreased, excitability of the neurons. There is a possibility that this inhibitory input serves as a short-term inhibitory control for other purpose. Further work is needed to fully address this question.

(4) It is very interesting that no LTP can be induced after chronic heat exposure (Figures K-M); the authors suggest that "the pathway in these mice were already saturated" (line 375). Could this hypothesis be tested in slices by employing a protocol to extinguish pre-existing (chronic heat exposure-induced) LTP? This would provide further strength to the findings/suggestion that an important synaptic plasticity mechanism is at play that conveys behavioral changes upon chronic heat stimulation.

We agree with the reviewer that the results of the suggested experiment would further strengthen our hypothesis. We will try to confirm this in future studies.

(5) It is interesting that long-term heat does not increase parameters associated with depression (Figure 1N-Q), how is it with acute heat stress, are those depression parameters increased acutely? It would be interesting to learn if "depression indicators" increase acutely but then adapt (as a consequence of heat acclimation) or if they are not changed at all and are also low during acute heat exposure.

Based on our observations, we did not find increased depression parameters after acute heat stress in our experiments (data not shown), which was consistent with other two previous studies (Beas et al., 2018; Zhang et al., 2021). It appears that acute heat stress is more associated with anxiety-like behavior and may not be sufficient to induce depression-like phenotypes in rodents, aligning with our observation during experiments.

Beas BS, Wright BJ, Skirzewski M, Leng Y, Hyun JH, Koita O, Ringelberg N, Kwon HB, Buonanno A, Penzo MA (2018) The locus coeruleus drives disinhibition in the midline thalamus via a dopaminergic mechanism Nat Neurosci 21:963-973.

Zhang GW, Shen L, Tao C, Jung AH, Peng B, Li Z, Zhang LI, Whit Tao HZ (2021) Medial preoptic area antagonistically mediates stress-induced anxiety and parental behavior Nat Neurosci 24:516-528.

Weaknesses/suggestions for improvement.

(1) The introduction and general tenet of the study is, to us, a bit too one-sided/biased: generally, repetitive heat exposure --heat acclimation-- paradigms are known to not only be detrimental to animals and humans but also convey beneficial effects in allowing the animals and humans to gain heat tolerance (by strengthening the cardiovascular system, reducing energy metabolism and weight, etc.).

Thanks for the suggestion. We have modified the introduction in our revised manuscript to make it more balanced.

(2) The point is well taken that these authors here want to correlate their model (90 minutes of heat exposure per day) to heat waves. Nevertheless, and to more fully appreciate the entire biology of repetitive/chronic/persistent heat exposure (heat acclimation), it would be helpful to the general readership if the authors would also include these other aspects in their introduction (and/or discussion) and compare their 90-minute heat exposure paradigm to other heat acclimation paradigms. For example, many past studies (using mice or rats)m have used more subtle temperatures but permanently (and not only for 90 minutes) stimulated them over several days and weeks (for example see PMID: 35413138). This can have several beneficial effects related to cardiovascular fitness, energy metabolism, and other aspects. In this regard: 38{degree sign}C used in this study is a very high temperature for mice, in particular when they are placed there without acclimating slowly to this temperature but are directly placed there from normal ambient temperatures (22{degree sign}C-24{degree sign}C) which is cold/coolish for mice. Since the accuracy of temperature measurement is given as +/- 2{degree sign}C, it could also be 40{degree sign}C -- this temperature, 40{degree sign}C, non-heat acclimated C57bl/6 mice will not survive for long.

The authors could consider discussing that this very strong, short episodic heat-stress model used here in this study may emphasize detrimental effects of heat, while more subtle long-term persistent exposure may be able to make animals adapt to heat, become more tolerant, and perhaps even prevent the detrimental cognitive effects observed in this study (which would be interesting to assess in a follow-up study).

Thanks for pointing out the important aspect regarding the different heat exposure paradigms and their potential impacts. We have incorporated these points into both the Introduction and Discussion sections of the revised manuscript.

(3) Line 140: It would help to be clear in the text that the behaviors are measured 1 day after the acute heat exposure - this is mentioned in the legend to the figure, but we believe it is important to stress this point also in the text. Similarly, this is also relevant for chronic heat stimulation: it needs to be made very clear that the behavior is measured 1 day after the last heat stimulus. If the behaviors had been measured during the heat stimulus, the results would likely be very different.

Thanks for the suggestion, and we have clarified the procedure in the revised manuscript.

(4) Figure 2 D and Figure 2- Figure Supplement 1: since there is quite some baseline cFos activity in the pPVT region we believe it is important to include some control (room temperature) mice with anterograde labelling; in our view, it is difficult/not possible to conclude, based on Fig 2 supplement 2C, that nearly 100% of the cfos positive cells are contacted by POA fibre terminals (line 168). By eye there are several green cells that don't have any red label on (or next to) them; additionally, even if there is a little bit of red signal next to a green cell: this is not definitive proof that this is a synaptic contact. It is therefore advisable to revisit the quantification and also revisit the interpretation/wording about synaptic contacts.

In relation to the above: Figure 2h suggests that all neurons are connected (the majority receiving inhibitory inputs), is this really the case, is there not a single neuron out of the 63 recorded pPVT neurons that does not receive direct synaptic input from the POA?

Thanks for the comments. For Figure 2-figure supplement 1, the baseline c-Fos activity in pPVT were indeed measured from mouse under room temperature. Observed activity may be attributed to the diverse functions that the pPVT is responsible for. Compared to the heat-exposed group, we observed significant increases in c-Fos signals, suggesting the effect of heat exposure.

For Figure 2-figure supplement 2, through targeted injection of AAV1-Cre into the POA, we achieved selective expression of Cre-dependent ChR2-mCherry in pPVT neurons receiving POA inputs. Following heat exposure, we observed substantial colocalization between heat-induced c-Fos expression (green signal) and ChR2-mCherry-labeled neurons (red signal) in the pPVT. This extensive overlap indicates that POA-recipient pPVT neurons are predominantly heat-responsive and likely mediate the behavioral alterations induced by chronic heat exposure. We have validated these signals and included updated quantification in our revised manuscript.

For Fig 2H, we specifically patched those neurons that were surrounded by red fluorescence under the microscope, ensuring that the patched neurons had a high likelihood of being innervated from POA. This is why all 63 recorded pPVT neurons were found to receive direct synaptic input from the POA.

(5) It would be nice to characterize the POA population that connects to the pPVT, it is possible/likely that not only warm-responsive POA neurons connect to that region but also others. The current POA-to-pPVT optogenetic fibre stimulations (Figure 4) are not selective for preoptic warm responsive neurons; since the POA subserves many different functions, this optogenetic strategy will likely activate other pathways. The referees acknowledge that molecular analysis of the POA population would be a major undertaking. Instead, this could be acknowledged in the discussion, for example in a section like "limitation of this study".

Thanks for the suggestion. We have supplemented this part in our revised manuscript.

(6) Figure 3a the strategy to express Gcamp in a Cre-dependent manner: it seems that the Gcamp8f signal would be polluted by EGFP (coming from the Cre virus injected into the POA): The excitation peak for both is close to 490nm and emission spectra/peaks of GCaMP8f (510-520 nm) and EGFP (507-510 nm) are also highly overlapping. We presume that the high background (EGFP) fluorescence signal would preclude sensitive calcium detection via Gcamp8f, how did the authors tackle this problem?

Thank you for pointing out this issue. We acknowledge that we included AAV1-EGFP when recording the GCaMP8F signal to assist in the post-verification of the accuracy of the injection site. But we also collected recording data from mice with AAV1-Cre without EGFP injected into POA and Cre-dependent GCaMP8F in pPVT, albert in a smaller number. We did not observe any obvious differences in the change in calcium signal between these two virus strategies, suggesting that the sensitivity of the GCaMP signals was not significantly affected by the increased baseline fluorescence due to EGFP.

(7) How did the authors perform the social interaction test (Figures 1F, G)? Was the intruder mouse male or female? If it was a male mouse would the interaction with the female mouse be a form of mating behavior? If so, the interpretation of the results (Figures 1F, G) could be "episodic heat exposure over the course of 3 weeks reduces mating behavior".

Thanks for the comment. For this female encounter test, we strictly followed the protocol by Ago Y, et al., (2015). During this test, both the strange male and female mice were placed into a wired cup (which is made up of mental wire entanglement and the size for each hole is 0.5 cm [L] x 0.5 cm [W]), which successfully prevented large body contact and the mating behavior but only innate sex-motivated moving around the cup. We have supplemented the details in the method part of our revised manuscript.

Ago Y, Hasebe S, Nishiyama S, Oka S, Onaka Y, Hashimoto H, Takuma K, Matsuda T (2015) The Female Encounter Test: A Novel Method for Evaluating Reward-Seeking Behavior or Motivation in Mice Int J Neuropsychopharmacol 18: pyv062.

Reviewer #3 (Public review):

In this study, Cao et al. explore the neural mechanisms by which chronic heat exposure induces negative valence and hyperarousal in mice, focusing on the role of the posterior paraventricular nucleus (pPVT) neurons that receive projections from the preoptic area (POA). The authors show that chronic heat exposure leads to heightened activity of the POA projection-receiving pPVT neurons, potentially contributing to behavioral changes such as increased anxiety level and reduced sociability, along with heightened startle responses. In addition, using electrophysiological methods, the authors suggest that increased membrane excitability of pPVT neurons may underlie these behavioral changes. The use of a variety of behavioral assays enhances the robustness of their claim. Moreover, while previous research on thermoregulation has predominantly focused on physiological responses to thermal stress, this study adds a unique and valuable perspective by exploring how thermal stress impacts affective states and behaviors, thereby broadening the field of thermoregulation. However, a few points warrant further consideration to enhance the clarity and impact of the findings.

(1) The authors claim that behavior changes induced by chronic heat exposure are mediated by the POA-pPVT circuit. However, it remains unclear whether these changes are unique to heat exposure or if this circuit represents a more general response to chronic stress. It would be valuable to include control experiments with other forms of chronic stress, such as chronic pain, social defeat, or restraint stress, to determine if the observed changes in the POA-pPVT circuit are indeed specific to thermal stress or indicative of a more universal stress response mechanism.

We also share similar considerations as the reviewer and indeed have conducted experiments to explore this possibility. Our findings suggest that the POA-pPVT pathway may also mediate behavioral changes induced by other chronic stress, e.g. chronic restraint stress. Nevertheless, given the well-known prominent role of POA neurons in heat perception, we do believe that the POA-pPVT has a specialized role in mediating chronic heat induced changes. The role of this pathway in other stress-related responses will need a more comprehensive study in the future.

(2) The authors use the term "negative emotion and hyperarousal" to interpret behavioral changes induced by chronic heat (consistently throughout the manuscript, including the title and lines 33-34). However, the term "emotion" is broad and inherently difficult to quantify, as it encompasses various factors, including both valence and arousal (Tye, 2018; Barrett, L. F. 1999; Schachter, S. 1962). Therefore, the reviewer suggests the authors use a more precise term to describe these behaviors, such as valence. Additionally, in lines 117 and 137-139, replacing "emotion" with "stress responses," a term that aligns more closely with the physiological observations, would provide greater specificity and clarity in interpreting the findings.

Thanks for the suggestion. We have modified the description of “emotion” to “emotional valence” in various places throughout the revised manuscript.

(3) Related to the role of POA input to pPVT,

a) The authors showed increased activity in pPVT neurons that receive projections from the POA (Figure 3), and these neurons are necessary for heat-induced behavioral changes (Figures 4N-W). However, is the POA input to the pPVT circuit truly critical? Since recipient pPVT neurons can receive inputs from various brain regions, the reviewer suggests that experiments directly inhibiting the POA-to-pPVT projection itself are needed to confirm the role of POA input. Alternatively, the authors could show that the increased activity of pPVT neurons due to chronic heat exposure is not observed when the POA is blocked. If these experiments are not feasible, the reviewer suggests that the authors consider toning down the emphasis on the role of the POA throughout the manuscript and discuss this as a limitation.<br /> b) In the electrophysiology experiments shown in Figures 6A-I, the authors conducted in vitro slice recordings on pPVT neurons. However, the interpretation of these results (e.g., "The increase in presynaptic excitability of the POA to pPVT excitatory pathway suggested plastic changes induced by the chronic heat treatment.", lines 349-350) appears to be an overclaim. It is difficult to conclude that the increased excitability of pPVT neurons due to heat exposure is specifically caused by inputs from the POA. To clarify this, the reviewer suggests the authors conduct experiments targeting recipient neurons in the pPVT, with anterograde labeling from the POA to validate the source of excitatory inputs.

For point (a), we acknowledge that pPVT neurons receiving POA inputs may also receive projections from other brain regions. While these additional inputs warrant investigation, they fall beyond the scope of our current study and represent promising directions for future research. Notably, compared to other well-characterized regions such as the amygdala and ventral hippocampus, the pPVT receives particularly robust projections from hypothalamic nuclei (Beas et al., 2018). Our optogenetic inhibition of POA-recipient pPVT neurons during chronic heat exposure effectively prevented the influence of POA excitatory projections on pPVT neurons. Furthermore, selective optogenetic activation of POA excitatory terminals within the pPVT was sufficient to induce similar behavioral abnormalities in mice, strongly supporting the causal role of POA inputs in mediating chronic heat exposure-induced behavioral alterations.

Beas BS, Wright BJ, Skirzewski M, Leng Y, Hyun JH, Koita O, Ringelberg N, Kwon HB, Buonanno A, Penzo MA (2018) The locus coeruleus drives disinhibition in the midline thalamus via a dopaminergic mechanism Nat Neurosci 21:963-973.

Regarding point (b), we acknowledge certain limitations in our in vitro patch-clamp recordings when attributing increased pPVT neuronal excitability to enhanced presynaptic POA inputs. Nevertheless, our brain slice recordings clearly demonstrated heightened excitability of pPVT neurons following chronic heat exposure. This finding was further corroborated by our in vivo fiber photometry recordings specifically targeting POA-recipient pPVT neurons, which confirmed that the increased pPVT neuronal activity was indeed modulated by POA inputs. The causal relationship was strengthened by our observation that optogenetic activation of POA excitatory terminals within the pPVT reproduced behavioral abnormalities similar to those observed in chronic heat-exposed mice. Additionally, our inability to induce circuit-specific LTP in the POA-pPVT pathway suggests that these synapses were already potentiated and saturated, reflecting enhanced excitatory inputs from the POA to pPVT. Collectively, these findings support our conclusion that increased excitatory projections from the POA to pPVT likely represent a key mechanism underlying chronic heat exposure-induced behavioral alterations in mice.

(4) The authors focus on the excitatory connection between the POA and pPVT (e.g., "Together, our results indicate that most of the pPVT-projecting POA neurons responded to heat treatment, which would then recruit their downstream neurons in the pPVT by exerting a net excitatory influence.", lines 169-171). However, are the POA neurons projecting to the pPVT indeed excitatory? This is surprising, considering i) the electrophysiological data shown in Figures 2E-K that inhibitory current was recorded in 52.4% of pPVT neurons by stimulation of POA terminal, and ii) POA projection neurons involved in modulating thermoregulatory responses to other brain regions are primarily GABAergic (Tan et al., 2016; Morrison and Nakamura, 2019). The reviewer suggests showing whether the heat-responsive POA neurons projecting to the pPVT are indeed excitatory (This could be achieved by retrogradely labeling POA neurons that project to the pPVT and conducting fluorescence in situ hybridization (FISH) assays against Slc32a1, Slc17a6, and Fos to label neurons activated by warmth). Alternatively, demonstrate, at least, that pPVT-projecting POA neurons are a distinct population from the GABAergic POA neurons that project to thermoregulatory regions such as DMH or rRPa. This would clarify how the POA-pPVT circuit integrates with the previously established thermoregulatory pathways.

Thanks for the comment and suggestion. We acknowledge that there are both excitatory and inhibitory projections from POA to pPVT. Although it is not our primary focus, we are aware of the substantial inhibitory inputs from POA to pPVT which suggests an important function. However, we do not think that this pathway, which would exert an opposite effect on POA-recipient pPVT neurons compared to the excitatory input, contributes to the long-term effect of chronic heat exposure. This is due to the increased, rather than decreased, excitability of the neurons. There is a possibility that this inhibitory input serves as a short-term inhibitory control for other purpose. Further work is needed to fully address this question.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I have a number of suggested minor edits that would improve the readability and interpretation of figures for the reader. In many figures, there are places where it is unclear what is being tested, and making minor changes would make the manuscript flow more easily for the reader:

(1) The authors could add additional details about the behavior paradigms in the Figures, especially Figure 1. How long was the chronic heat exposure for? At what temperature? What is the length of time between the end of heat exposure and the start of behaviors? What was the schedule of testing for EPM and social behaviors? Was it all on the same day or on different days? These details will make it easier for the reader to understand the behavior tests.

We have revised our experimental scheme, especially Figure 1, and added more detailed descriptions in the method section. The modifications have also been applied to the other figures.

(2) In Figures 1J and 1K, it is a bit unclear what is being shown in the right panel, since there are no axes or labels to interpret what is being plotted.

We have added body kinetics (purple dot) in the left panel of Figure 1J and 1K to align with the right panels, and we have updated our descriptions in the figure legend.

(3) In general, Figure 1 would benefit from more headers/labels or schematics to demonstrate what is being tested (for example, it's unclear that forced swim, tail suspension, open field, aggression, sucrose preference, or acoustic startle are being studied unless the reader looks at the figure legend in depth. Simple schematics or titles for each panel would help.

We have added the abbreviated titles for each panel of Figure 1 to help readers to better understand what was being tested.

(4) Figure 2A would benefit from edits to the schematic so that it is clear that heat exposure is being done before the animal is sacrificed and cFos is stained.

We have revised the text to clarify that heat exposure occurred before the animal was sacrificed and c-Fos was stained.

(5) Figure 2D: would help if the quantification of overlap of cFos and rabies was shown in the figure in addition to reporting it in the text (84%).

We have added quantification in Figure 2D.

(6) The supplemental data in Figure 2 - Supplemental Figure 1 showing increased Fos in PVT and POA after heat exposure would actually help if it was in main Figure 2 so that the reader can more clearly see the rationale for choosing the POA-PVT circuit. But this is a matter of preference and up to the author where they want to show this data.

Thanks for the suggestion. But considering the layout and space, we will prefer to retain this part in Figure 2-supplemental figure 1.

(7) Figure 3 would benefit from a behavior schematic illustrating the time course of the experiment and what the heat exposure protocol is for each day (how many minutes heat 'on' vs 'off', the temperature of heat, etc). Also, what is different about day 22 that makes it chronic heat vs day 21? Currently, it is a bit hard to understand the protocol.

We have added the temperature and time of chronic heat exposure in the schematic of Figure 3. The “day 22” represented the time point after chronic heat exposure. And we measured the calcium activity of POA recipient pPVT neurons on day 22 to compare with day 1 to demonstrate that the activity changes of POA recipient pPVT neurons after chronic heat exposure.

(8) Figure 3D, it is unclear what the difference is between the Day 1 data on the left and Day 1 data on the right. Same with Figure 3H, unclear what the difference is between the left and the right.

The left panel and right panel reflect different parameters: frequency /min (left) and amplitude (△F/F) for Figure 3D-3H. By doing this, we want to reflect the dynamic activity changes of POA recipient pPVT neurons throughout chronic heat exposure process. Now, all figures in panel 3D to 3H have been revised to make them clearer in meaning.

(9) Figure 4A would benefit from schematics showing the stimulation protocol for chronic optogenetics (how many days? Frequency? Duration of time? Etc)

We have added detailed schematics in our Figure 4A.

Reviewer #2 (Recommendations for the authors)

(1) It is interesting that social behavior appears to be reduced upon long-term heat exposure but not after acute heat exposure. Interaction of animals, such as huddling, can be used by animals as a form of behavioral thermoregulation in cold environments and heat may drive animals apart to allow for better heat dissipation. The social interaction measured here is not huddling (because, I assume, the animals are separated by a divider?) but is this form of behavior measured here related to huddling/"social thermoregulation"? This could be discussed.

Our behavioral tests were performed at room temperature. Even though huddling is a type of social behavior, based on our observation, the tested mouse was actively revolving around the mental cap, suggesting this type of behavior is not related to huddling/social thermoregulation type of social behavior.

(2) Line 113: The statement "Chronic treatment did not change body temperature" should be clarified/rephrased because 90 minutes of 38 degrees centigrade exposure to heat will increase the body temperature of mice. It would be helpful if the authors made clear that they measure body temperature before the heat stimulus (and not during the heat stimulus), which is now only obvious if one digs into the methods section.

We have revised the text and clarified that body temperature was measured before the heat stimulus in the revised manuscript.

(3) Figure 1J and K: for the non-experts, these graphs are difficult to interpret, some more explanation is needed (what exactly is measured ?). We believe that the term "arousal" may not be justified in this context because the authors have not measured sleep patterns (EEG and EMG) to show that the mice arouse from a sleep (or sleep-like) stage; the authors may consider changing the terminology, e.g. something along the lines of "agitation" or "activity".

We have further elaborated the meaning of Figure 1J and K in our revised manuscript. The acoustic startle response is a well-recognized behavioral parameter reflecting arousal levels in rodent model. The more agitation in response to stimulus, the higher the arousal levels in mice. We have used the term “agitation” to describe mice’s performance in the acoustic startle response test.

Reviewer #3 (Recommendations for the authors):

(1) The authors suggest in the introduction of the manuscript that the HPA axis and other multifaceted factors may influence emotional changes caused by heat stress (lines 63-78). However, there are no experiments or discussions on how the POA-pPVT circuit interacts with these factors. In line with the study's proposed direction in the introduction section, it would be valuable to explore, or at least discuss, whether and how the POA-pPVT circuit interacts with the HPA axis or other neural circuits known to regulate emotional and stress responses. Alternatively, the reviewer suggests revising the content of the introduction to align with the focus of the study.

Although POA is known to possibly interact with the HPA axis via its connection with the paraventricular nucleus of the hypothalamus, there is hardly any evidence for the pPVT. Thus, we prefer not to speculate this question, which remains open, in our current manuscript.

(2) In Figure 5, the authors report that pPVT neurons that receive projections from the POA exhibited increased responses to stressful situations following chronic heat exposure. However, considering the long pre- and post-recording time gap of approximately three weeks, the additional expression of GCaMP protein over time could potentially account for the increased signal. Therefore, the reviewer recommends including a control group without heat exposure to rule out this possibility.

We have included Figure 3-figure supplement 1 in our manuscript to exclude the effect of expression of GCaMP protein over time on the recording of calcium signal.

(3) Related to Figure 2, a) Please include quantification data of the overlap between retrogradely labeled and c-Fos-expressing POA neurons, which can be presented as a bar graph in Figure 2. This would be beneficial for readers to estimate how many warm-activated POA neurons connected to the pPVT are actively engaged under these conditions.

In the revised manuscript, we have included the quantification analysis in Figure 2.

b) The images in Figure 2 - Figure Supplement 1 seem to degrade in quality when magnified, making it difficult to discern finer details. Higher-resolution images would greatly improve the clarity and help in accurately visualizing the c-Fos expression patterns in the POA and pPVT regions.

We have changed our images of Figure 2-figure supplement 1 to higher-resolution in the revised manuscript.

c) The c-Fos images in Figure 2D and Figure 2 - Figure Supplement 2C appear unusual in that the c-Fos signal seems to fill the entire cell, whereas c-Fos protein is localized to the nucleus. Could the authors clarify whether this image accurately represents c-Fos staining or if there might be an issue with the staining or imaging process?

We are confident that the green signals in both Figure 2D and Figure 2-figure supplement 2C, which did not occupy the whole cell body, have already accurately reflected the c-Fos and that they were nucleus staining. We have updated the amplified picture in Figure 2D.

d) In Supplemental Figure 2B, the square marking the region of interest should be clearly explained in the figure legend to ensure that readers can fully understand the context and focus of the image.

We have further modified our figure legend in Figure 2-figure supplement 1 in our revised manuscript.

eLife Assessment

The results from this study, which investigates the mechanisms necessary for initiating tissue invagination using a cellular Potts modelling approach, suggest that apical constriction is not sufficient to drive the process by itself. The study highlights how choices inherent to modelling - such as permitting straight or curved cell edges - may affect the outcome of simulations and, consequently, their biophysical interpretation. Despite incomplete evidence supporting their major claims due to a rather coarse-grained exploration of the model, this work is useful for biophysicists investigating complex tissue deformation through computational frameworks.

Joint Public Review:

Satoshi Yamashita et al., investigate the physical mechanisms driving tissue bending using the cellular Potts Model, starting from a planar cellular monolayer. They argue that apical length-independent tension control alone cannot explain bending phenomena in the cellular Potts Model, contrasting with previous works, particularly Vertex Models. They conclude that an apical elastic term, with zero rest value (due to endocytosis/exocytosis), is necessary to achieve apical constriction and that tissue bending can be enhanced by adding a supracellular myosin cable. Additionally, a very high apical elastic constant promotes planar tissue configurations, opposing bending.

Strengths:

- The finding of the required mechanisms for tissue bending in the cellular Potts Model provides a natural alternative for studying bending processes in situations with highly curved cells.

- Despite viewing cellular delamination as an undesired outcome in this particular manuscript, the model's capability to naturally allow T1 events might prove useful for studying cell mechanics during out-of-plane extrusion.

[Editors' note: The previous reviews have not been updated, as the changes to the manuscript were restricted to refining the text. The authors addressed all of the minor points raised by the reviewers. Some of the major points such as the lack of a summary quantification still stand. The previous reviews are here: https://doi.org/10.7554/eLife.93496.2.sa1]

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):  

Summary:  

Satoshi Yamashita et al., investigate the physical mechanisms driving tissue bending using the cellular Potts Model, starting from a planar cellular monolayer. They argue that apical length-independent tension control alone cannot explain bending phenomena in the cellular Potts Model, contrasting with previous works, particularly Vertex Models. They conclude that an apical elastic term, with zero rest value (due to endocytosis/exocytosis), is necessary to achieve apical constriction, and that tissue bending can be enhanced by adding a supracellular myosin cable. Additionally, a very high apical elastic constant promotes planar tissue configurations, opposing bending.  

Strengths:  

- The finding of the required mechanisms for tissue bending in the cellular Potts Model provides a natural alternative for studying bending processes in situations with highly curved cells. 

- Despite viewing cellular delamination as an undesired outcome in this particular manuscript, the model's capability to naturally allow T1 events might prove useful for studying cell mechanics during out-of-plane extrusion. 

We thank the reviewer for the careful comments and suggestions.

Weaknesses: 

- The authors claim that the cellular Potts Model (CPM) is unable to achieve the results of the vertex model (VM) simulations due to naturally non-straight cellular junctions in the CPM versus the VM. The lack of a substantial comparison undermines this assertion. None of the references mentioned in the manuscript are from a work using vertex model with straight cellular junctions, simulating apical constriction purely by a enhancing a length-independent apical tension. Sherrard et al and Pérez-González et al. use 2D and 3D Vertex Models, respectively, with a "contractility" force driving apical constriction. However, their models allow cell curvature. Both references suggest that the cell side flexibility of the CPM shouldn't be the main issue of the "contractility model" for apical constriction. 

We appreciate the comment.

For the reports by Sherrard et al and Pérez-Gonález et al, lack of the cell rearrangement (T1 transition) might have caused the difference. Other than these, Muñoz et al. (doi:10.1016/j.jbiomech.2006.05.006), Polyakov et al. (doi:10.1016/j.bpj.2014.07.013), Inoue et al.

(doi:10.1007/s10237-016-0794-1), Sui et al.

(doi:10.1038/s41467-018-06497-3), and Guo et al. (doi:10.7554/eLife.69082) used simulation models with the straight lateral surface.

We updated an explanation about the difference between the vertex model and the cellular Potts model in the discussion.

P12L318 “An edge in the vertex model can be bent by interpolating vertices or can be represented with an arc of circle (Brakke, 1992). Even in cases where vertex models were extended to allow bent lateral surfaces, the model still limited cell rearrangement and neighbor changes (Pérez-González et al., 2021), limiting the cell delamination. Thus the difference in simulation results between the models could be due to whether the cell rearrangement was included or not. However, it is not clear how the absence of the cell rearrangement affected cell behaviors in the simulation, and it shall be studied in future. In contrast to the vertex model, the cellular Potts model included the curved cell surface and the cell rearrangement innately, it elucidated the importance of those factors.”

- The myosin cable is assumed to encircle the invaginated cells. Therefore, it is not clear why the force acts over the entire system (even when decreasing towards the center), and not locally in the contour of the group of cells under constriction. The specific form of the associated potential is missing. It is unclear how dependent the results of the manuscript are on these not-well-motivated and model-specific rules for the myosin cable.

A circle radius decreases when the circle perimeter shrinks, and this was simulated with the myosin cable moving toward the midline in the cross section.

We added an explanation in the introduction and the results.

P2L74 “In the same way with the contracting circumferential myosin belt in a cell decreasing the cell apical surface, the circular supracellular myosin cable contraction decreases the perimeter, the radius of the circle, and an area inside the circle.”

P6L197 “In the cross section, the shrinkage of the circular supracellular myosin cable was simulated with a move of adherens junction under the myosin cable toward the midline.”

- The authors are using different names than the conventional ones for the energy terms. Their current attempt to clarify what is usually done in other works might lead to further confusion. 

The reviewer is correct. However we named the energy terms differently because the conventional naming would be misleading in our simulation model.

We added an explanation in the results.

P4L140 “Note that the naming for the energy terms differs from preceding studies. For example, Farhadifar et al. (2007) named a surface energy term expressed by a proportional function "line tensions" and a term expressed by a quadratic function "contractility of the cell perimeter". In this study, however, calling the quadratic term "contractility" would be misleading since it prevents the contraction when  < _0. Therefore we renamed the terms accordingly.”

Reviewer #2 (Public Review): 

Summary: 

In their work, the Authors study local mechanics in an invaginating epithelial tissue. The work, which is mostly computational, relies on the Cellular Potts model. The main result shows that an increased apical "contractility" is not sufficient to properly drive apical constriction and subsequent tissue invagination. The Authors propose an alternative model, where they consider an alternative driver, namely the "apical surface elasticity". 

Strengths: 

It is surprising that despite the fact that apical constriction and tissue invagination are probably most studied processes in tissue morphogenesis, the underlying physical mechanisms are still not entirely understood. This work supports this notion by showing that simply increasing apical tension is perhaps not sufficient to locally constrict and invaginate a tissue. 

We thank the reviewer for the careful comments.

Weaknesses: 

Although the Authors have improved and clarified certain aspects of their results as suggested by the Reviewers, the presentation still mostly relies on showing simulation snapshots. Snapshots can be useful, but when there are too many, the results are hard to read. The manuscript would benefit from more quantitative plots like phase diagrams etc. 

We agree with the comment.

However, we could not make the qualitative measurement for the phase diagram since 1) the measurement must be applicable to all simulation results, and 2) measured values must match with the interpretation of the results. To do so, the measurement must distinguish a bent tissue, delaminated cells, a tissue with curved basal surface and flat apical surface, and a tissue with closed invagination. Such measurement is hardly designed.

Recommendations for the authors: 

Reviewing Editor (Recommendations For The Authors): 

I see that the authors have worked on improving their paper in the revision. However, I agree with both reviewer #1 and reviewer #2 that the presentation and discussion of findings could be clearer. 

Concrete recommendations for improvement: 

(1) I find the observation by reviewer #1 on cell rearrangement very illuminating: It is indeed another key difference between the Cellular Potts Model that the authors use compared to typical Vertex Models, and could very well explain the different model outcomes. The authors could expand on the discussion of this point. 

We updated an explanation about the difference between the vertex model and the cellular Potts model in the discussion.

P12L318 “An edge in the vertex model can be bent by interpolating vertices or can be represented with an arc of circle (Brakke, 1992). Even in cases where vertex models were extended to allow bent lateral surfaces, the model still limited cell rearrangement and neighbor changes (Pérez-González et al., 2021), limiting the cell delamination. Thus the difference in simulation results between the models could be due to whether the cell rearrangement was included or not. However, it is not clear how the absence of the cell rearrangement affected cell behaviors in the simulation, and it shall be studied in future. In contrast to the vertex model, the cellular Potts model included the curved cell surface and the cell rearrangement innately, it elucidated the importance of those factors.”

(2) In lines 161-164, the authors write "Some preceding studies assumed that the apical myosin generated the contractile force (Sherrard et al, 2010: Conte et al., 2012; Perez-Mockus et al., 2017; Perez-Gonzalez et al., 2021), while others assumed the elastic force (Polyakov et al., 2014; Inoue et al. 2016; Nematbakhsh et al., 2020)." 

Similarly, in lines 316-319 the authors write "In the preceding studies, the apically localized myosin was assumed to generate either the contractile force (Sherrard et al, 2010: Conte et al., 2012; Perez-Mockus et al., 2017; Perez-Gonzalez et al., 2021), or the elastic force (Polyakov et al., 2014; Inoue et al. 2016; Nematbakhsh et al., 2020)." 

The phrasing here is poor, as it suggests that the latter three studies (Polyakov et al., 2014; Inoue et al. 2016; Nematbakhsh et al., 2020) do not use the assumption that apical myosin generated contractile forces. This is wrong. All three of these studies do in fact assume apical surface contractility mediated by myosin. In addition, they also include other factors such as elastic restoring forces from the cell membrane (but not mediated by myosin as far as I understand). 

These statements should be corrected. 

We named the energy term expressed with the proportional function “contractility” and the energy term expressed with the quadratic function “elasticity”. Here we did not define what biological molecules correspond with the contractility or the elasticity.

For the three studies, the effect of myosin was expressed by the quadratic function, and Polyakov et al. (2014) named it “springlike elastic properties”, Inoue et al. (2016) named it “Apical circumference elasticity”, and Nematbakhsh et al. (2020) named it “Actomyosin contractility”. To explain that the for generated by myosin was expressed with the quadratic function in these studies, we wrote that they “assumed the elastic force”.

We assumed the myosin activity to be approximated with the proportional function in later parts and proposed that the membrane might be expressed with the quadratic function and responsible for the apical constriction based on other studies.

To clarify this, we added it to the results.

P4L175 “Some preceding studies assumed that the apical myosin generated the contractile force (Sherrard et al., 2010; Conte et al., 2012; Perez-Mockus et al., 2017; Pérez-González et al., 2021), while the others assumed the myosin to generate the elastic force (Polyakov et al., 2014; Inoue et al., 2016; Nematbakhsh et al., 2020).”

(3) Lines 294-296: The phrasing suggests that the "alternative driving mechanism" consists of apical surface elasticity remodelling alone. This is not true, it's an additional mechanism, not an alternative. The authors' model works by the combined action of increased apical surface contractility and apical surface elasticity remodelling (and the effect can be strengthened by including a supracellular actomyosin cable). 

We agree with the comment that the surface remodeling is not solely driving the apical constriction but with myosin activity. However, if we wrote it as an additional mechanism, it might look like that both the myosin activity alone and the surface remodeling alone could drive the apical constriction, and they would drive it better when combined together. So we replaced “mechanism” with “model”.

P12L311 “In this study, we demonstrated that the increased apical surface contractility could not drive the apical constriction, and proposed the alternative driving model with the apical surface elasticity remodeling.”

(4) In general, the part of the results section encompassing equations 1-5 should more explicitly state which equations were used in all simulations (Eqs1+5), and which ones were used only for certain conditions (Eqs2+3+4). 

We added it as follows.

P4L153 “While the terms Equation 1 and Equation 5 were included in all simulations since they were fundamental and designed in the original cellular Potts model (Graner and Glazier, 1992), the other terms Equation 2-Equation 4 were optional and employed only for certain conditions.”

(5) Lines 150-152: Please state which parameters were examined. I assume Equation 4 was also left out of this initial simulation, as it is the potential energy of the actomyosin cable that was only included in some simulations. 

We added it as follows.

P4L163 “The term Equation 4 was not included either. For a cell, its compression was determined by a balance between the pressure and the surface tension, i.e., the heigher surface tension would compress the cell more. The bulk modulus 𝜆 was set 1, the lateral cell-cell junction contractility 𝐽_𝑙 was varied for different cell compressions, and the apical and basal surface contractilities 𝐽_𝑎 and 𝐽_𝑏 were varied proportional to 𝐽_𝑙.”

(6) Lines 118-122: The sentence is very long and hard to parse. I suggest the following rephrasing: 

“In this study, we assumed that the cell surface tension consisted of contractility and elasticity. We modelled the contractility as constant to decrease the surface, but not dependent on surface width or strain. We modelled the elasticity as proportional to the surface strain, working to return the surface to its original width." 

We updated the explanation as follows.

P3L121 “In this study, we assumed that the cell surface tension consisted of contractility and elasticity. We modeled the contractility as a constant force to decrease the surface, but not dependent on surface width or strain. We modeled the elasticity as a force proportional to the surface strain, working to return the surface to its original width.”

(7) Lines 270-274: Another long sentence that is difficult to understand.

Suggested rephrasing: 

"Note that the supracellular myosin cable alone could not reproduce the apical constriction (Figure 2c), and cell surface elasticity in isolation caused the tissue to stay almost flat. However, combining both the supracellular myosin cable and the cell surface elasticity was sufficient to bend the tissue when a high enough pulling force acted on the adherens junctions." 

We updated the sentence as follows.

P9L287 “Note that the supracellular myosin cable alone could not reproduce the apical constriction (Figure 2c), and that with some parameters the modified cell surface elasticity kept the tissue almost flat (Figure 4). However, combining both the supracellular myosin cable and the cell surface elasticity made a sharp bending when the pulling force acting on the adherens junction was sufficiently high.”

(8) Lines 434-435: Unclear what is meant with sentence starting with "Rest of sites" 

We update the sentence as follows.

P17L456 “At the initial configuration and during the simulation, sites adjacent to medium and not marked as apical are marked as basal.”

(9) Fixing typos and other minor grammar and wording changes would improve readability. Following is a list in order of appearance in the text with suggestions for improvement. 

We greatly appreciate the careful editing, and corrected the manuscript accordingly.

Line 14: "a" is not needed in the phrase "increased a pressure" 

Line 15: "cell into not the wedge shape" --"cell not into the wedge shape"  In fact it might be better to flip the sentence around to say, e.g. "making the cells adopt a drop shape instead of the expected wedge shape". 

Line 24: "cells decrease its apical surface" --"cells decrease their apical surface" 

Line 25: instead of "turn into wedge shape", a more natural-sounding expression could be "adopt a wedge shape" 

Line 28: "which crosslink and contract" --because the subject is the singular "motor protein", the verb tense needs to be changed to "crosslinks and contracts" 

Line 29: I suggest to use the definite article "the" before "actin filament network" as this is expected to be a known concept to the reader. 

Line 31: "adherens junction and tight junction" --use the plural, because there are many per cell: "adherens junctions and tight junctions" 

Line 42: "In vertebrate" --"In vertebrates" 

Line 46: "Since the interruption to" --"Since the interruption of" 

Line 56: "the surface tension of the invaginated cells were" --since the subject is "the surface tension", the verb "were" needs to be changed to "was"  Line 63: "extra cellular matrix" --generally written as "extracellular matrix" without the first space 

Line 66: "many epithelial tissues" --"in many epithelial tissues" 

Line 70: "This supracellular cables" --"These supracellular cables" 

Line 72: "encircling salivary gland" --either "encircling the salivary gland" or "encircling salivary glands" 

Lines 76-77: "investigated a cell physical property required" --"investigated what cell physical properties were required" 

Line 78: "was another framework" --"is another framework" (it is a generally and currently valid true statement, so use the present tense) 

Line 79: "simulated an effect of the apically localized myosin" --for clarity, I suggest rephrasing as "simulated the effect of increased apical contractility mediated by apically localized myosin" 

Similarly, in Line 80: "did not reproduce the apical constriction" --"did not reproduce tissue invagination by apical constriction", as technically the cells in the model do reduce their apical area, but fail to invaginate as a tissue. 

Line 82: "we found that a force" --"we found that the force" 

Line 101: "apico-basaly" --"apico-basally" 

Lines 107-108: "in order to save a computational cost" --"in order to save on computational cost" 

Line 114: "Therefore an area of the cell" --"Therefore the interior area of the cell" 

Line 139: "formed along adherens junction" --"formed along adherens junctions" 

Line 166: "we ignored an effect" --"we ignored the effect" 

Line 167: "and discussed it later" --"and discuss it later" 

Lines 167-168: "an experiment with a cell cultured on a micro pattern showed that the myosin activity was well corresponded by the contractility" --"an experiment with cells cultured on a micro pattern showed that the myosin activity corresponded well to the contractility" 

Line 172: "success of failure" --"success or failure" 

Figure 1 caption: "none-polar" --"non-polarized"; "reg" --"red" 

Line 179: "To prevented the surface" --"To prevent the surface" 

Line 180: "It kept the cells surface" --"It kept the cells' surface" (apostrophe missing) 

Line 181: "cells were delaminated and resulted in similar shapes" --"cells were delaminated and adopted similar shapes" 

Line 190: "To investigate what made the difference" --"To investigate the origin of the difference" 

Line 203: For clarity, I would suggest to add more specific wording. "the pressure, and a difference in the pressure between the cells resulted in" --"the internal pressure due to cell volume conservation, and a difference in the pressure between the contracting and non-contracting cells resulted in" 

Line 206: "by analyzing the energy with respect to a cell shape" --"by analyzing the energy with respect to cell shape" 

Line 220: "indicating that cell could shrink" --"indicating that a cell could shrink" 

Line 224: For clarity, I would suggest more specific wording "lateral surface, while it seems not natural for the epithelial cells" --"lateral surface imposed on the vertex model, a restriction that seems not natural for epithelial cells" 

Line 244: "succeeded in invaginating" --"succeeding in invaginating" 

Line 247: "were checked whether the cells" --"were checked to assess whether the cells" 

Line 250: "cells became the wedge shape" --"cells adopted the wedge shape" 

Line 286: "there were no obvious change in a distribution pattern" --"there was no obvious change in the distribution pattern" 

Lines 296-297: "When the cells were assigned the high apical surface contractility, the cells were rounded" --"When the cells were assigned a high apical surface contractility, the cells became rounded" 

Line 298: "This simulation results" --"These simulation results" 

Lines 301-302: I suggest to increase clarity by somewhat rephrasing.  "Even when the vertex model allowed the curved lateral surface, the model did not assume the cells to be rearranged and change neighbors" --"Even in cases where vertex models were extended to allow curved lateral surfaces, the model still limited cell rearrangement and neighbor changes" 

Line 326: "high surface tension tried to keep" --"high surface tension will keep" 

Line 334: "In many tissue" --"In many tissues" 

Line 345: "turned back to its original shape" --"turned back to their original shape" (subject is the plural "cells") 

Lines 348-349: "resembles the result of simulation" --"resembles the result of simulations" 

Line 352: "how the myosin" --"how do the myosin" 

Line 356: "it bears the surface tension when extended and its magnitude" What does the last "its" refer to? The surface tension? 

Line 365: "the endocytosis decrease" --"the endocytosis decreases" 

Line 371: "activatoin" --"activation" 

Line 374 "the cells undergoes" --"the cells undergo" 

Line 378: "entier" --"entire" 

Line 389: "individual tissue accomplish" --"individual tissues accomplish" 

Line 423: "is determined" --"are determined" (subject is the plural "labels") 

Line 430: "phyisical" --"physical" 

Table 6 caption: "cell-ECN" --cell-ECM 

Line 557: "do not confused" --"should not be confused" 

Reviewer #1 (Recommendations For The Authors): 

- The phrase "In addition, the encircling supracellular myosin cable largely promoted the invagination by the apical constriction, suggesting that too high apical surface tension may keep the epithelium apical surface flat." is not clear to me. It sounds contradictory. 

This finding was unexpected and surprising for us too. However, it is actually not contradictory since stronger surface tension will make the surface flatter in general. Figure 4 shows the flat apical surface with the wedge shape cells for the too strong apical surface tension. On the other hand, the supracellular myosin cable promoted the cell shape changes without raising the surface tension, and thus it could make a sharp bending (Figure 5).

We updated the explanation for the effect of the supracellular myosin cable as follows.

P2L74 “In the same way as the contracting circumferential myosin belt in a cell decreasing the cell apical surface, the circular supracellular myosin cable contraction decreases the perimeter, the radius of the circle, and an area inside the circle.”

P6L197 “In the cross section, the shrinkage of the circular supracellular myosin cable was simulated with a move of adherens junction under the myosin cable toward the midline.”

- Even when the authors now avoid to say "in contrast to vertex model simulations" in pg.4, in the next section there is still the intention to compare VM to CPM. Idem in the Discussion section. The conclusion in that section is that the difference between the results arising with VM (achieving the constriction) and the CPM (not achieving the constriction, and leading to cell delamination) are due to the straight lateral surfaces. However, Sherrard et at could achieve the constriction with an enhanced apical surface contractility using a 2D VM that allows curvatures. Therefore, I don't think the main difference is given by the deformability of the lateral surfaces. Instead, it might be due to the facility of the CPM to drive cellular rearrangements, coupled to specific modeling rules such as the permanent lost of the "apical side" once a delamination occurs and the boundary conditions. A clear example is the observation of loss of cell-cell adherence when all the tensions are set the same. Instead, in a VM cells conserve their lateral neighbors in the uniform tension regime (Sherrard et at). Is it noteworthy that the two mentioned works using vertex models to achieve apical constriction (Sherrard et at. (2D) and Pérez-González (3D) et al.) seem to neglect T1 transitions. I specifically think the added discussion on the impact of the T1 events (fundamental for cell delamination) is quite poor. A more detailed description would help justify the differences between model outcomes. 

We updated an explanation about the difference between the vertex model and the cellular Potts model in the discussion.

P12L318 “ An edge in the vertex model can be bent by interpolating vertices or can be represented with an arc of circle (Brakke, 1992). Even in cases where vertex models were extended to allow bent lateral surfaces, the model still limited cell rearrangement and neighbor changes (Pérez-González et al., 2021), limiting the cell delamination. Thus the difference in simulation results between the models could be due to whether the cell rearrangement was included or not. However, it is not clear how the absence of the cell rearrangement affected cell behaviors in the simulation, and it shall be studied in future. In contrast to the vertex model, the cellular Potts model included the curved cell surface and the cell rearrangement innately, it elucidated the importance of those factors.”

- Fig6c: cell boundary colors are quite difficult to see. 

The images were drawn by custom scripts, and those scripts do not implement a method to draw wide lines.

- Title Table 1: "epitherila". 

We corrected the typo.

Reviewer #2 (Recommendations For The Authors): 

The Authors have addressed most of my initial comments. In my opinion, the results could be better represented. Overall, the manuscript contains too many snapshots that are hard to read. I am sure the Authors could come up with a parameter that would tell the overall shape of the tissue and distinguish between a proper invagination and delamination. Then they could plot this parameter in a phase diagram using color plots to show how varying values of model parameters affects the shape. Presentation aside, I believe the manuscript will be a valuable piece of work that will be very useful for the community of computational tissue mechanics. 

We agree with the comment.

However, we could not make a suitable qualitative measurement method. For the phase diagrams, the measurement must be applicable to simulation results, otherwise each figure introduce a new measurement and a color representation would just redraw the snapshots but no comparison between the figures. So the different measurements would make the figures more difficult to read.

The single measurement must distinguish the cell delamination by the increased surface contractility from the invagination by the modified surface elasticity and the supracellular contractile ring, even though the center cells were covered by the surrounding cells and lost contact with apical side extracellular medium in both cases.

With the center of mass, the delaminated cells would return large values because they were moved basally. With the tissue basal surface curvature, it would not measure if the tissue apical surface was also curved or kept flat. If the phase diagram and interpretation of the simulation results do not match with each other, it would be misleading.

A measurement meeting all these conditions was hardly designed.

eLife Assessment

This important study combines single nucleus transcriptional profiling with spatial transcriptomics to identify and map heterogeneity among dopamine neurons in the mouse ventral midbrain. The compelling results separate dopamine neurons into three broad families that have unique (yet overlapping) spatial distribution within the ventral tegmental area and substantia nigra, and also identify population-specific changes in a LRRK2 mouse model of Parkinson's Disease. The creation of a public-facing app where the snRNA-seq data can be investigated by anyone is a major strength.

Reviewer #1 (Public review):

Summary:

Dopamine neurons contribute to motivated and motor behaviors in many ways, and ample recent evidence has suggested that distinct dopamine neuron subclasses support discrete behavioral and circuit functions. Prior studies have subdivided dopamine neurons by spatial localization, gene expression patterns, and physiological properties. However, many of these studies were bound by previous technical limitations that made comprehensive subclassification efforts difficult or impossible. The main goal of this manuscript was to characterize and further define dopamine neuron heterogeneity in the ventral midbrain. The study uses cutting-edge single nucleus RNA-seq (on the 10X Genomics platform) and spatial transcriptomics (on the MERFISH platform) to define dopamine neuron heterogeneity with unprecedented resolution. The result is a convincing and comprehensive subclassification of dopamine neurons into three main families, each with major branches and subtypes. In addition, the study reports comparisons between wild type mice and mice that harbor a G2019S mutation in the Lrrk2 gene, which models a common cause of autosomally dominant Parkinson's Disease in humans. These results, while less robust due to the nature of the group comparisons, nevertheless identify vulnerability within specific dopamine neuron subpopulations. This vulnerability may contribute unique risk to dopamine neuron loss in the context of Parkinson's disease. Overall, the study is careful and rigorous and provides a critical resource for the rapidly evolving knowledge of dopamine neuron subtypes.

Strengths:

-The creation of a public-facing app where the snRNA-seq data can be investigated by anyone is a major strength.<br /> -The manuscript includes careful comparisons to prior datasets that have sought to explore dopamine neuron heterogeneity. The result is a useful synthesis of new findings with previously published work, which is helpful for moving the field forward in this area.<br /> -The integration of snRNA-seq with MERFISH results is particularly strong, and enables insight not only into subclassification, but also into how this relates to spatial localization. The careful neuroanatomy reveals important distinctions between Sox6, Calb1, and Gad2 positive dopamine neuron families, with some degree of spatial overlap.

Reviewer #2 (Public review):

Gaertner and colleagues present a study examining the transcriptomic diversity and spatial location of dopaminergic neurons from mice and examine the changes in gene expression resulting from knock in of the Parkinson's LRRK G2019S risk variant. Overall, I found the manuscript presented their study very clearly, well written with very clear figures for the most part. I am not an expert on mouse neuroanatomy but found their classification reasonably well justified and spatial orientation of dopaminergic neurons within the mouse brain informative and clear. While trends were clear and well presented, the apparent spatial heterogeneity suggests that knowledge of the functional connections and roles of these neurons will be required to better interpret the results presented but nonetheless their findings exposed significant detail that is required for further understanding.

The study of the transcriptional effects of the LRRK2 KI was also informative and clearly framed in terms of a focused analyses on the effects of the KI only on dopaminergic neurons.

I thank the authors for addressing my previous concerns and comments, and feel they have done so well. I agree that as GSEA only includes ranked genes from the specific study, the gene set is already limited to the relevant background.

Author response:

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

Reviewer #1 (Public review):

Weaknesses:

(1) Important details about the nature of DEG comparisons between the wild type and the Lrrk2 G2019S model are missing.

Please see the recommendations section below for specific responses to individual comments from Reviewer #1.

(2) Some aspects of the integration between snRNA-seq and MERFISH data are not clear, and many MERFISH-identified cells do not appear to have a high-confidence cluster transfer into the snRNA-seq data space. Imputation is used to overcome some issues with the MERFISH dataset, but it is not clear that this is appropriate.

Please see the recommendations section below for specific responses to individual comments from Reviewer #1.

Reviewer #2 (Public review):

(1) In the GO pathway analyses (both GSEA and DEG GO), I did not see a correction applied to the gene background considered. The study focusses on dopaminergic neurons and thus the gene background should be restricted to genes expressed in dopaminergic neurons, rather than all genes in the mouse genome. The problem arises that if we randomly sample genes from dopaminergic neurons instead of the whole genome, we are predisposed to sampling genes enriched in relevant cell-type-specific roles (and their relevant GO terms) and correspondingly depleted in genes enriched in functions not associated with this cell type. Thus, I am unsure whether the results presented in Figures 8 and 9 may be more likely to be obtained just by randomly sampling genes from a dopaminergic neuron. The background should be limited and these functional analyses rerun.

Thank you for pointing out this important concern. We agree that overrepresentation analyses (ORAs) are vulnerable to selecting cell-type specific markers as significantly differentially expressed and thus inflating detection of cell-type associated gene sets rather than those truly altered as a function of experimental condition. We have thus re-run the GO analyses in our study with the genetic background being adjusted for each individual comparison. For dataset-level GO in Fig 8, genetic background was defined as genes with expression detected in at least 5% of all cells (to approximate the inclusion of cluster-specific genes). For comparisons of subsets within the dataset (i.e. a family or cluster) across conditions, a minimum detection level of 10% of cells was used to define the genetic background. These same thresholds were applied to filter the DEG lists used as input for GO. Interestingly, this correction appears to have filtered out or lowered the significance of some of the more generic brain-associated pathways that we initially presented, such as axonogenesis or learning and memory, and we feel even more confident in our original interpretation.

Functional class scoring methods like GSEA, however, are unlike ORAs in that they do utilize a hypergeometric test to calculate overrepresentation as no distinction is made between significant and non-significant differential gene expression (nor is a genetic background provided as input to this tool). GSEA takes as input the full DE results, ranking genes according to their association with either group. Thus, genes simply enriched in DA neurons should be present towards both extremes of the rank list, rather than uniformly skewed toward one extreme. Per the GSEA authors’ user manual and original source paper, the entirety of DE testing should be provided as input for GSEA (barring genes with detection levels so low that their differential expression and/or ranking is likely to be artifactual):

“The GSEA algorithm does not filter the expression dataset and generally does not benefit from your filtering of the expression dataset. During the analysis, genes that are poorly expressed or that have low variance across the dataset populate the middle of the ranked gene list and the use of a weighted statistic ensures that they do not contribute to a positive enrichment score. By removing such genes from your dataset, you may actually reduce the power of the statistic and processing time is rarely a factor as GSEA can easily analyze 22,000 genes with even modest processing power. However, an exception exists for RNA-seq datasets where GSEA may benefit from the removal of extremely low count genes (i.e., genes with artifactual levels of expression such that they are likely not actually expressed in any of the samples in the dataset).” [https://www.gsea-msigdb.org/gsea/doc/GSEAUserGuideFrame.html]

In our study, this filtering of very low expression genes (to account for artifactually inflated fold changes or a large number of ties in the rank list that are subsequently ordered at random) occurred at the level of DE testing using the Seurat FindMarkers command, in which differential expression calculations were only performed for genes that were detected in a minimum of 10% of cells in the dataset.

(2) In the scRDS results, I am unsure what is significant and what isn't. The authors refer to relative measures in the text ("highest") but I do not know whether these differences are significant nor whether any associations are significantly unexpected. Can the x-axis of scRDS results presented in Figure 9 H and I be replaced with a corrected p-value instead of the scRDS score?

An important distinction should be made here between scDRS and similar approaches that utilize overrepresentation analyses to assess for associations of DEGs with putative risk genes, similar to the GO analyses performed in our paper. The scDRS score represents the relative association for each individual cell’s expression profile (among all other cells in the dataset) with PD risk loci by utilizing the underlying SNPs and associations described in GWAS summary statistics (see Methods or Zhang et al., Nat Genetics 2022 for more details). While scDRS can be used to generate a p value for each individual cell in the dataset, scDRS does not have a native method for defining group-level p values, nor have we attempted to calculate group-level p values here. In order to compare cluster-level mean scDRS scores and determine their significance, we created bootstrapped 95% confidence intervals for the mean scDRS score of each cluster or family (shown by the error bars in forest plots 9G, 9H). A score of 0 represents the null hypothesis of no association between gene expression and PD risk loci, and thus if the 95% confidence interval does not overlap 0, the mean scDRS score for a given group can be regarded as significant as there is a less than 5% chance of the true group mean containing the null. Similarly, groups can be compared to each other in the same way to determine if the group-level mean scDRS score is significantly different across a given pair. However, this overlap of confidence intervals should be interpreted cautiously, as there are a large number of potential comparisons that can be made, creating the potential for Type I error. We have added language to clarify what the scDRS score represents, and to ensure it is not conflated with approaches such as GO or GSEA.

(3) The results discussed at the bottom of page 13 [page 14 of new version] state that 48.82% of the proteins encoded by the Calb1 DEGs have pre-synaptic localisations as opposed to 45.83% of the SOX6 DEGs, which does not support the statement that "greater proportions of DEGs are associated with presynaptic locations in cells from vulnerable DA neurons (Sox6 family, [and in particular,Sox6^tafa1]), compared to less vulnerable ones (Calb1 family)".

Thank you for pointing this out; the error here lies in the wording of the results. The percentages mentioned above describe the percentages within the synaptic localized genes rather than the total DEG lists. We have rephrased this section for clarity to include both the percentages within this category as well as the total (the results of which are in line with our original statement).

(4) While an interest in the Sox6^tafa1 subtype is explained through their expression of Anxa1 denoting a previously identified subtype associated with locomotory behaviours, it was unclear to me how to interpret the functional associations made to DEGs in this subtype taken out of context of other subtypes. Given all the other subtypes, it is not possible to ascertain how specific and thus how interesting these results are unless other subtypes are analysed in the same way and this Sox6^tafa1 subtype is demonstrated as unusual given results from other subtypes.

In our study, we chose to specifically focus on this population given its unique acceleration-locked functional activity pattern observed in Azcorra & Gaertner et al, Nat Neuro 2023, as there are technical limitations that warrant cautious application of the above approach. We agree that the associations of this population to the described DEGs cannot be interpreted as unique to this population given the data presented and have added language to this effect within the text. There are two major challenges to analyzing all other subtypes to provide a comparison. Firstly, given the number of subtypes involved and number of downstream analyses, it is computationally intensive to carry out this analysis. More importantly however, the results cannot be easily compared across different populations due to the variability in both cluster size and internal heterogeneity of each cluster, as the statistical power in calculating DEGs will be inherently different across these populations (i.e. smaller or more heterogenous clusters would be expected to show a lower number of DEGs reaching significance). While pseudo bulk testing is effective for mitigating these factors, our limited sample number (n=2 independently generated datasets per group) dramatically underpowers differential expression testing using pseudo bulk analysis. One solution is to uniformly limit each cluster size to the minimally observed cluster size through random down-sampling. While this allows the ‘n’ in DE calculations to be uniform, this potentially worsens the problem of internal heterogeneity, which would remain roughly constant but in the setting of a lower ‘n’, increasing the variability in results for larger clusters. To provide a comparator for the population of interest we focused on, we have performed this down sampling approach in order to compare Sox6^Tafa1 to another cluster within the VTA, Calb1^Stac, that also expresses high levels of Anxa1 and Aldh1a1 given the broad interest in these markers as proxies for vulnerability. The results of this comparison are now shown in Figure S10.

(5) On p12, the authors highlight Mir124a-1hg that encodes miR-124. This is upregulated in Figure 8D but the authors note this has been to be downregulated in PD patients and some PD mouse models. Can the authors comment on the directional difference?

We have adjusted the text to reflect this discrepancy and speculate on why this may be observed. In short, one hypothesis is that miR-124, given its proposed neuroprotective effects, is increased in DA neurons facing toxic metabolic insults as a compensatory response. In our prodromal model without observable degeneration, this could represent an early sign of cell stress. While speculative, in PD patients or overtly degenerative models, lack of compensatory miR-124 or fulminant cell death among vulnerable cells could result in an observed decrease in miR-124 expression.

(6) Lastly, can the authors comment on the selection of a LogFC cut-off of 0.15 for their DEG selection? I couldn't see this explained (apologies if I missed it).

The 0.15 cutoff was selected arbitrarily based on the observed range of fold changes seen among our differentially expressed genes. However, importantly, this cutoff was not used for defining DEGs for downstream analyses such as GSEA or GO, nor for defining significance of differential expression, which was done purely based on FDR-adjusted p values <0.05. The selection of 0.15 affects only the coloring seen in the volcano plot, which we have decided to move to supplemental figures given the uniformly small effect size seen in individual genes and a separate reviewer comment regarding concern in the field over differential expression testing methods in single-cell datasets. Instead, this figure now focuses on highlighting pathway- and gene-set level comparisons that can provide easier interpretation of small, but concordant changes across swaths of genes.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In the MERFISH dataset, only around half of the DAergic cells (2,297 of 4,532) were successfully projected into the snRNA-seq UMAP space, based on a similarity score > 0.5. Additionally, key transcripts that were used to define the snRNA-seq clusters (such as Sox6) were not identified at all in the MERFISH dataset. This raises some questions about the ability to integrate and compare these datasets directly, which are not fully considered in the manuscript. These discrepancies are smoothed over using imputation, which allows specific class-defining genes such as Sox6 to be plotted on spatial coordinates in Figure 4D. However, imputation is not without caveats, and the appropriateness of the imputation is not well considered in the text.

We fully agree with the reviewer that the use of an imputation approach needs to be clarified and justified thoroughly. We added a sentence to better clarify the process of imputation on Page 9 “The imputed gene expression is extrapolated from anchors established from pairwise correspondences of cell expression levels between MERFISH and snRNA-Seq datasets.” This pair-wise cell correspondence as defined by anchors can be assessed using Seurat confidence score. We acknowledge the fact that only about 50% of cells could confidently be transferred onto the snRNA-Seq data. This is the result of using a stringent confidence level of 0.5 (similar to previous publications, PMID: 38092916 & 38092912). We preferred mapping fewer high-confidence cells than potentially misrepresenting the spatial location of some of these clusters.

It is also important to demonstrate the reliability of gene imputation. Indeed as pointed out by the reviewer, some probes such as Sox6 were not detected in the MERFISH dataset. To strengthen our data integration and as already mentioned in the manuscript, we excluded 219 genes based on the deviation of average counts per cell between the datasets. The fact that the imputed expression of Sox6 perfectly reflects its well-characterized distribution (PMIDs: 25127144, 30104732, 25437550, 34758317) strengthened our confidence in our imputation pipeline. We also looked at the correlation of imputed gene expression with the detected transcripts in our MERFISH experiments. We added a new supplemental figure (S7) highlighting the correlations between MERFISH and imputed gene expression of 8 genes (4 for each Sox6 and Calb1 family). Together Fig S6 and S7 show the range of correlations between imputed and actual MERFISH transcript. Altogether, we can observe relatively high correlation between the number of detected transcripts per gene in snRNA-Seq and MERFISH datasets

In addition, we added a paragraph discussing limitations of gene expression imputation on page 17: “A strength of our study is that it utilizes advantages of each transcriptomic approach, the deep molecular profiling of individual cells using snRNA-Seq and the spatial resolution of MERFISH. For instance, we relied on gene expression imputation to ascribe expression level to genes not covered/detected in our MERFISH probe panel. Gene imputation as described by Stuart et al.(92) has been used in several recent studies integrating spatial and transcriptomic data(46, 47). It relies on identifying anchors that enable projection of MERFISH data onto the UMAP space of a snRNA-Seq dataset and then uses neighboring cells to extrapolate the expression of genes not included in our probe panel. This approach was used to impute Sox6 expression, which accurately reflects what has been reported in prior immunofluorescence and in situ hybridization studies(11, 27, 38, 43, 55). Moreover, imputed gene expression levels correlated strongly with MERFISH detected transcript for most genes further supporting our approach (Fig S6 and S7). Nevertheless, dataset integration has limitations that should be considered. First, imputed gene expression relies on the ability to identify reliable anchors linking the snRNA-Seq and MERFISH datasets. These anchors are determined in part by the choice of genes included on probe panels and thus could indirectly influence the reliability of imputed gene expression. Secondly, gene counts per cell in MERFISH are determined via segmentation of images, which is susceptible to artifacts and bias from centrally versus peripherally localized gene transcripts. In summary, although limitations are present in multi-modal transcriptomic analyses, merging these two approaches provided a molecular and spatial map of the DA system that could not have been resolved by either method alone.”

(2) In the discussion, the authors argue that the cellular classifications identified here for DA neurons are more likely to reflect discrete cell types than cell states. The rationale for this conclusion is largely based on the absence of subtype differences between wild-type and LRRK2 G2019S transgenic mice. I do not find this argument to be convincing, because it is still possible that certain subdivisions simply reflect dynamic cell states that are also not grossly altered in the mutant mouse. A stronger argument for this claim would be to include trajectory-based analyses that do not show predicted transition points between nearby or related clusters.

We thank the reviewer for pointing out this particular limitation as differentiating “cell type” and “cell states” been debated in the field for years with no consensus emerging how to address the issue. As suggested, we performed a trajectory analysis using Monocle3 on both control and Lrrk2 samples. We’ve built the trajectory map, taking cluster 20 as the starting node. To avoid potential biased trajectories induced by different cell coverage, we’ve down sampled the Lrrk2 condition to match the number of cells of wildtype. As expected, since most of the DA clusters are not segregated in the UMAP space, the trajectory analysis showed predicted transitions between clusters (see Author response image 1A and 1B). Even though some clusters’ pseudotime score were statistically different between the wildtype and Lrrk2 samples, they overall remained similar (Author response image 1C). This analysis suggests that the LRRK2G2019S mutation induces a mild transcriptional perturbation but does not result in a major cell state drift. Indeed, we believe changes in the observed trajectory path would disappear as the number of cells analyzed increases. Because of this bias introduced by cell coverage, we prefer not to include this trajectory analysis in the manuscript to avoid misleading readers. Thus, as suggested by the reviewer, we softened our claim to “This suggests that our taxonomic scheme is agnostic to a mild perturbation such as LRRK2G2019S, suggesting that our clusters are reflective of cell types, rather than cell states. It is possible that with more severe perturbations, such as a toxin lesion, more substantial alterations of taxonomic schemes are observed(86, 93). However, we expect that for mild insults, day to day behavioral changes, or pharmacological paradigms, our clusters will be resistant to changes, although individual gene levels may vary. Nonetheless, we cannot definitively confirm that a given DA neuron cannot convert from one subtype to another. Ultimately, alternative approaches such as detailed fate mapping of clusters or RNAseq-based trajectory analyses with greater numbers of sampled cells could be used to resolve this question.”.

Author response image 1.

A)Trajectory analysis of wildtype and B) LRRK2^G2019S samples. C) Pseudotime scores for each cluster across wildtype and Lrrk2 conditions. Error bars represent the confidence of error for false positives discovery rate of 5%.

(3) The relationship between individual samples, GEMwell, and sequenced library should be clarified. If independent samples were combined into one GEMwell, this should be explicitly stated for clarity.

We have revised the text to better clarify the methodology. In brief, each of our 4 independent samples (2 control, 2 mutants; equal sexes per sample) were isolated from n=2 pooled mice (for a total n=8 mice across the 4 samples). Each sample was processed in its own GEM well to produce 4 distinct libraries that were subsequently sequenced and analyzed as described.

(4) Please include more details on DEG testing in the manuscript, this is key for interpreting the robustness of certain findings. Ideally, pseudobulked comparisons would be used here (given concerns in the field that DEG testing where N = number of cells artificially inflates the statistical power, violates assumptions of independence, and results in false positive DEGs).

While we agree that pseudobulk analysis would be ideal for reducing false positives, our study, while exceptionally large in total numbers of DA cells profiled, was generated from 4 total 10X libraries as described above, without any mechanism to definitively demultiplex to the original n=8 source mice. Thus, pseudobulk comparisons would be performed using only n=2 per group, which is below the recommended sample size for these methods. Given this concern, we have moved the volcano plot from Figure 8D to the supplementals and added language to the methods and relevant figure legend acknowledging the limitation in Seurat’s default differential expression analysis methodology.

eLife Assessment

This important and unique study proposes a framework to understand and predict generalization in visual perceptual learning in humans based on form invariants. Using behavioral experiments in humans and by training deep networks, the authors offer evidence that the presence of stable invariants in a task leads to faster learning. However, this interpretation is promising but counter-intuitive and incomplete, since there could be possible other confounds such as differing attentional demands that lead to differing patterns of generalization. It can be strengthened through additional experiments and by rejecting alternate explanations.

Reviewer #2 (Public review):

The strengths of this paper are clear: The authors are asking a novel question about geometric representation that would be relevant to a broad audience. Their question has a clear grounding in pre-existing mathematical concepts, that have been only minimally explored in cognitive science. Moreover, the data themselves are quite striking, such that my only concern would be that the data seem almost too perfect. It is hard to know what to make of that, however. From one perspective, this is even more reason the results should be published. Yet I am of the (perhaps unorthodox) opinion that reviewers should voice these gut reactions, even if it does not influence the evaluation otherwise. I have a few additional comments:

(1) The authors have now explained their theoretical position in a much more thorough and accessible way. I applaud them for that.

(2) Although I continue to believe that the manipulation in Experiment 1 is imperfect, I am convinced by the authors that the subsequent evidence is more convincing, and thus that the merit of this work lies mostly in those data.

If these results are robust, I believe the authors have discovered something of great value. While this paper stops short of providing definitive evidence in support of the Erlangen program (just as most work in vision science has stopped short of providing definitive evidence in support of its favored view), the data are sufficiently novel and provocative that these theories are worth entertaining further.

Author response:

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

eLife Assessment

This important study proposes a framework to understand and predict generalization in visual perceptual learning in humans based on form invariants. Using behavioral experiments in humans and by training deep networks, the authors offer evidence that the presence of stable invariants in a task leads to faster learning. However, this interpretation is promising but incomplete. It can be strengthened through clearer theoretical justification, additional experiments, and by rejecting alternate explanations.

We sincerely thank the editors and reviewers for their thoughtful feedback and constructive comments on our study. We have taken significant steps to address the points raised, particularly the concern regarding the incomplete interpretation of our findings.

In response to Reviewer #1, we have included long-term learning curves from the human experiments to provide a clearer demonstration of the differences in learning rates across invariants, and have incorporated a new experiment to investigate location generalization within each invariant stability level. These new findings have shifted the focus of our interpretation from learning rates to the generalization patterns both within and across invariants, which, alongside the observed weight changes across DNN layers, support our proposed framework based on the Klein hierarchy of geometries and the Reverse Hierarchy Theory (RHT).

We have also worked to clarify the conceptual foundation of our study and strengthen the theoretical interpretation of our results in light of the concerns raised by Reviewers #1 and #2. We have further expanded the discussion linking our findings to previous work on VPL generalization, and addressed alternative explanations raised by Reviewers #1.

Reviewer #1 (Public Review):

Summary:

Visual Perceptual Learning (VPL) results in varying degrees of generalization to tasks or stimuli not seen during training. The question of which stimulus or task features predict whether learning will transfer to a different perceptual task has long been central in the field of perceptual learning, with numerous theories proposed to address it. This paper introduces a novel framework for understanding generalization in VPL, focusing on the form invariants of the training stimulus. Contrary to a previously proposed theory that task difficulty predicts the extent of generalization - suggesting that more challenging tasks yield less transfer to other tasks or stimuli - this paper offers an alternative perspective. It introduces the concept of task invariants and investigates how the structural stability of these invariants affects VPL and its generalization. The study finds that tasks with high-stability invariants are learned more quickly. However, training with low-stability invariants leads to greater generalization to tasks with higher stability, but not the reverse. This indicates that, at least based on the experiments in this paper, an easier training task results in less generalization, challenging previous theories that focus on task difficulty (or precision). Instead, this paper posits that the structural stability of stimulus or task invariants is the key factor in explaining VPL generalization across different tasks

Strengths:

- The paper effectively demonstrates that the difficulty of a perceptual task does not necessarily correlate with its learning generalization to other tasks, challenging previous theories in the field of Visual Perceptual Learning. Instead, it proposes a significant and novel approach, suggesting that the form invariants of training stimuli are more reliable predictors of learning generalization. The results consistently bolster this theory, underlining the role of invariant stability in forecasting the extent of VPL generalization across different tasks.

- The experiments conducted in the study are thoughtfully designed and provide robust support for the central claim about the significance of form invariants in VPL generalization.

Weaknesses:

- The paper assumes a considerable familiarity with the Erlangen program and the definitions of invariants and their structural stability, potentially alienating readers who are not versed in these concepts. This assumption may hinder the understanding of the paper's theoretical rationale and the selection of stimuli for the experiments, particularly for those unfamiliar with the Erlangen program's application in psychophysics. A brief introduction to these key concepts would greatly enhance the paper's accessibility. The justification for the chosen stimuli and the design of the three experiments could be more thoroughly articulated.

We appreciate your feedback regarding the accessibility of our paper, particularly concerning the Erlangen Program and its associated concepts. We have revised the manuscript to include a more detailed introduction to Klein’s Erlangen Program in the second paragraph of Introduction section. It provides clear descriptions and illustrative examples for the three invariants within the Klein hierarchy of geometries, as well as the nested relationships among them (see revised Figure 1). We believe this addition will enhance the accessibility of the theoretical framework for readers who may not be familiar with these concepts.

In the revised manuscript, we have also expanded the descriptions of the stimuli and experimental design for psychophysics experiments. These additions aim to clarify the rationale behind our choices, ensuring that readers can fully understand the connection between our theoretical framework and experimental approach.

- The paper does not clearly articulate how its proposed theory can be integrated with existing observations in the field of VPL. While it acknowledges previous theories on VPL generalization, the paper falls short in explaining how its framework might apply to classical tasks and stimuli that have been widely used in the VPL literature, such as orientation or motion discrimination with Gabors, vernier acuity, etc. It also does not provide insight into the application of this framework to more naturalistic tasks or stimuli. If the stability of invariants is a key factor in predicting a task's generalization potential, the paper should elucidate how to define the stability of new stimuli or tasks. This issue ties back to the earlier mentioned weakness: namely, the absence of a clear explanation of the Erlangen program and its relevant concepts.

We thank you for highlighting the necessary to integrate our proposed framework with existing observations in VPL research.

Prior VPL studies have not concurrently examined multiple geometrical invariants with varying stability levels, making direct comparisons challenging. However, we have identified tasks from the literature that align with specific invariants. For example, orientation discrimination with Gabors (e.g., Dosher & Lu, 2005) and texture discrimination task (e.g., Wang et al., 2016) involve Euclidean invariants, and circle versus square discrimination (e.g., Kraft et al., 2010) involves affine invariants. On the other hand, our framework does not apply to studies using stimuli that are unrelated to geometric transformations, such as motion discrimination with Gabors or random dots, depth discrimination, vernier acuity, spatial frequency discrimination, contrast detection or discrimination.

By focusing on geometrical properties of stimuli, our work addresses a gap in the field and introduces a novel approach to studying VPL through the lens of invariant extraction, echoing Gibson’s ecological approach to perceptual learning.

In the revised manuscript, we have added a clearer explanation of Klein’s Erlangen Program, including the definition of geometrical invariants and their stability (the second paragraph in Introduction section). Additionally, we have expanded the Discussion section to draw more explicit comparisons between our results and previous studies on VPL generalization, highlighting both similarities and differences, as well as potential shared mechanisms.

- The paper does not convincingly establish the necessity of its introduced concept of invariant stability for interpreting the presented data. For instance, consider an alternative explanation: performing in the collinearity task requires orientation invariance. Therefore, it's straightforward that learning the collinearity task doesn't aid in performing the other two tasks (parallelism and orientation), which do require orientation estimation. Interestingly, orientation invariance is more characteristic of higher visual areas, which, consistent with the Reverse Hierarchy Theory, are engaged more rapidly in learning compared to lower visual areas. This simpler explanation, grounded in established concepts of VPL and the tuning properties of neurons across the visual cortex, can account for the observed effects, at least in one scenario. This approach has previously been used/proposed to explain VPL generalization, as seen in (Chowdhury and DeAngelis, Neuron, 2008), (Liu and Pack, Neuron, 2017), and (Bakhtiari et al., JoV, 2020). The question then is: how does the concept of invariant stability provide additional insights beyond this simpler explanation?

We appreciate your thoughtful alternative explanation. While this explanation accounts for why learning the collinearity task does not transfer to the orientation task—which requires orientation estimation—it does not explain why learning the collinearity task fails to transfer to the parallelism task, which requires orientation invariance rather than orientation estimation. Instead, the asymmetric transfer observed in our study could be perfectly explained by incorporating the framework of the Klein hierarchy of geometries.

According to the Klein hierarchy, invariants with higher stability are more perceptually salient and detectable, and they are nested hierarchically, with higher-stability invariants encompassing lower-stability invariants (as clarified in the revised Introduction). In our invariant discrimination tasks, participants need only extract and utilize the most stable invariant to differentiate stimuli, optimizing their ability to discriminate that invariant while leaving the less stable invariants unoptimized.

For example:

• In the collinearity task, participants extract the most stable invariant, collinearity, to perform the task. Although the stimuli also contain differences in parallelism and orientation, these lower-stability invariants are not utilized or optimized during the task.

• In the parallelism task, participants optimize their sensitivity to parallelism, the highest-stability invariant available in this task, while orientation, a lower-stability invariant, remains irrelevant and unoptimized.

• In the orientation task, participants can only rely on differences in orientation to complete the task. Thus, the least stable invariant, orientation, is extracted and optimized.

This hierarchical process explains why training on a higher-stability invariant (e.g., collinearity) does not transfer to tasks involving lower-stability invariants (e.g., parallelism or orientation). Conversely, tasks involving lower-stability invariants (e.g., orientation) can aid in tasks requiring higher-stability invariants, as these higher-stability invariants inherently encompass the lower ones, resulting in a low-to-high-stability transfer effect.

This unique perspective underscores the importance of invariant stability in understanding generalization in VPL, complementing and extending existing theories such as the Reverse Hierarchy Theory. To help the reader understand our proposed theory, we revised the Introduction and Discussion section.

- While the paper discusses the transfer of learning between tasks with varying levels of invariant stability, the mechanism of this transfer within each invariant condition remains unclear. A more detailed analysis would involve keeping the invariant's stability constant while altering a feature of the stimulus in the test condition. For example, in the VPL literature, one of the primary methods for testing generalization is examining transfer to a new stimulus location. The paper does not address the expected outcomes of location transfer in relation to the stability of the invariant. Moreover, in the affine and Euclidean conditions one could maintain consistent orientations for the distractors and targets during training, then switch them in the testing phase to assess transfer within the same level of invariant structural stability.

We thank you for this good suggestion. Using one of the primary methods for test generalization, we performed a new psychophysics experiment to specifically examine how VPL generalizes to a new test location within a single invariant stability level (see Experiment 3 in the revised manuscript). The results show that the collinearity task exhibits greater location generalization compared to the parallelism task. This finding suggests the involvement of higher-order visual areas during high-stability invariant training, aligning with our theoretical framework based on the Reverse Hierarchy Theory (RHT). We attribute the unexpected location generalization observed in the orientation task to an additional requirement for spatial integration in its specific experimental design (as explained in the revised Results section “Location generalization within each invariant”). Moreover, based on previous VPL studies that have reported location specificity in orientation discrimination (Fiorentini and Berardi, 1980; Schoups et al., 1995; Shiu and Pashler, 1992), along with the substantial weight changes observed in lower layers of DNNs trained on the orientation task (Figure 9B, C), we infer that under a more controlled experimental design—such as the two-interval, two-alternative forced choice (2I2AFC) task employed in DNN simulations, where spatial integration is not required for any of the three invariants—the plasticity for orientation tasks would more likely occur in lower-order areas.

In the revised manuscript, we have discussed how these findings, together with the observed asymmetric transfer across invariants and the distribution of learning across DNN layers, collectively reveal the neural mechanisms underlying VPL of geometrical invariants.

- In the section detailing the modeling experiment using deep neural networks (DNN), the takeaway was unclear. While it was interesting to observe that the DNN exhibited a generalization pattern across conditions similar to that seen in the human experiments, the claim made in the abstract and introduction that the model provides a 'mechanistic' explanation for the phenomenon seems overstated. The pattern of weight changes across layers, as depicted in Figure 7, does not conclusively explain the observed variability in generalizations. Furthermore, the substantial weight change observed in the first two layers during the orientation discrimination task is somewhat counterintuitive. Given that neurons in early layers typically have smaller receptive fields and narrower tunings, one would expect this to result in less transfer, not more.

We appreciate your suggestion regarding the clarity of DNN modeling. While the DNN employed in our study recapitulates several known behavioral and physiological VPL effects (Manenti et al., 2023; Wenliang and Seitz, 2018), we acknowledge that the claim in the abstract and introduction suggesting the model provides a ‘mechanistic’ explanation for the phenomenon may have been overstated. The DNN serves primarily as a tool to generate important predictions about the underlying neural substrates and provides a promising testbed for investigating learning-related plasticity in the visual hierarchy.

In the revised manuscript, we have made significant improvements in explaining the weight change across DNN layers and its implication for understanding “when” and “where” learning occurs in the visual hierarchy. Specifically, in the Results ("Distribution of learning across layers") and Discussion sections, we have provided a more explicit explanation of the weight change across layers, emphasizing its implications for understanding the observed variability in generalizations and the underlying neural mechanisms.

Regarding the substantial weight change observed in the first two layers during the orientation discrimination task, we interpret this as evidence that VPL of this least stable invariant relies more on the plasticity of lower-level brain areas, which may explain the poorer generalization performance to new locations or features observed in the previous literature (Fiorentini and Berardi, 1980; Schoups et al., 1995; Shiu and Pashler, 1992). However, this does not imply that learning effects of this least stable invariant cannot transfer to more stable invariants. From the perspective of Klein’s Erlangen program, the extraction of more stable invariants is implicitly required when processing less stable ones, which leads to their automatic learning. Additionally, within the framework of the Reverse Hierarchy Theory (RHT), plasticity in lower-level visual areas affects higher-level areas that receive the same low-level input, due to the feedforward anatomical hierarchy of the visual system (Ahissar and Hochstein, 2004, 1997; Markov et al., 2013; McGovern et al., 2012). Therefore, the improved signal from lower-level plasticity resulted from training on less stable invariants can enhance higher-level representations of more stable invariants, facilitating the transfer effect from low- to high-stability invariants.

Reviewer #2 (Public Review):

The strengths of this paper are clear: The authors are asking a novel question about geometric representation that would be relevant to a broad audience. Their question has a clear grounding in pre-existing mathematical concepts, that, to my knowledge, have been only minimally explored in cognitive science. Moreover, the data themselves are quite striking, such that my only concern would be that the data seem almost *too* clean. It is hard to know what to make of that, however. From one perspective, this is even more reason the results should be publicly available. Yet I am of the (perhaps unorthodox) opinion that reviewers should voice these gut reactions, even if it does not influence the evaluation otherwise. Below I offer some more concrete comments:

(1) The justification for the designs is not well explained. The authors simply tell the audience in a single sentence that they test projective, affine, and Euclidean geometry. But despite my familiarity with these terms -- familiarity that many readers may not have -- I still had to pause for a very long time to make sense of how these considerations led to the stimuli that were created. I think the authors must, for a point that is so central to the paper, thoroughly explain exactly why the stimuli were designed the way that they were and how these designs map onto the theoretical constructs being tested.

We thank you for reminding us to better justify our experimental designs. In response, we have provided a detailed introduction to Klein’s Erlangen Program, describing projective, affine, and Euclidean geometries, their associated invariants, and the hierarchical relationships among them (see revised Introduction and Figure 1).

All experiments in our study employed stimuli with varying structural stability (collinearity, parallelism, orientation, see revised Figure 2, 4), enabling us to investigate the impact of invariant stability on visual perceptual learning. Experiment 1 was adapted from paradigms studying the "configural superiority effect," commonly used to assess the salience of geometric invariants. This paradigm was chosen to align with and build upon related research, thereby enhancing comparability across studies. To address the limitations of Experiment 1 (as detailed in our Results section), Experiments 2, 3, and 4 employed a 2AFC (two-alternative forced choice)-like paradigm, which is more common in visual perceptual learning research. Additionally, we have expanded descriptions of our stimuli and designs. aiming to ensure clarity and accessibility for all readers.

(2) I wondered if the design in Experiment 1 was flawed in one small but critical way. The goal of the parallelism stimuli, I gathered, was to have a set of items that is not parallel to the other set of items. But in doing that, isn't the manipulation effectively the same as the manipulation in the orientation stimuli? Both functionally involve just rotating one set by a fixed amount. (Note: This does not seem to be a problem in Experiment 2, in which the conditions are more clearly delineated.)

We appreciate your insightful observation regarding the design of Experiment 1 and the potential similarity between the manipulations of the parallelism and orientation stimuli.

The parallelism and orientation stimuli in Experiment 1 were originally introduced by Olson and Attneave (1970) to support line-based models of shape coding and were later adapted by Chen (1986) to measure the relative salience of different geometric properties. In the parallelism stimuli, the odd quadrant differs from the others in line slope, while in the orientation stimuli, the odd quadrant contains identical line segments but differs in the direction pointed by their angles. The faster detection of the odd quadrant in the parallelism stimuli compared to the orientation stimuli has traditionally been interpreted as evidence supporting line-based models of shape coding. However, as Chen (1986, 2005) proposed, the concept of invariants over transformations offers a different interpretation: in the parallelism stimuli, the fact that line segments share the same slope essentially implies that they are parallel, and the discrimination may be actually based on parallelism. This reinterpretation suggests that the superior performance with parallelism stimuli reflects the relative perceptual salience of parallelism (an affine invariant property) compared to the orientation of angles (a Euclidean invariant property).

In the collinearity and orientation tasks, the odd quadrant and the other quadrants differ in their corresponding geometries, such as being collinear versus non-collinear. However, in the parallelism task, participants could rely either on the non-parallel relationship between the odd quadrant and the other quadrants or on the difference in line slope to complete the task, which can be seen as effectively similar to the manipulation in the orientation stimuli, as you pointed out. Nonetheless, this set of stimuli and the associated paradigm have been used in prior studies to address questions about Klein’s hierarchy of geometries (Chen, 2005; Wang et al., 2007; Meng et al., 2019). Given its historical significance and the importance of ensuring comparability with previous research, we adopted this set of stimuli despite its imperfections. Other limitations of this paradigm are discussed in the Results section (“The paradigm of ‘configural superiority effects’ with reaction time measures”), and optimized experimental designs were implemented in Experiment 2, 3, and 4 to produce more reliable results.

(3) I wondered if the results would hold up for stimuli that were more diverse. It seems that a determined experimenter could easily design an "adversarial" version of these experiments for which the results would be unlikely to replicate. For instance: In the orientation group in Experiment 1, what if the odd-one-out was rotated 90 degrees instead of 180 degrees? Intuitively, it seems like this trial type would now be much easier, and the pattern observed here would not hold up. If it did hold up, that would provide stronger support for the authors' theory.

It is not enough, in my opinion, to simply have some confirmatory evidence of this theory. One would have to have thoroughly tested many possible ways that theory could fail. I'm unsure that enough has been done here to convince me that these ideas would hold up across a more diverse set of stimuli.

Thanks for your nice suggestion to validate our results using more diverse stimuli. However, the limitations of Experiment 1 make it less suitable for rigorous testing of diverse or "adversarial" stimuli. In addition to the limitation discussed in response to (2), another issue is that participants may rely on grouping effects among shapes in the quadrants, rather than solely extracting the geometrical invariants that are the focus of our study. As a result, the reaction times measured in this paradigm may not exclusively reflect the extraction time of geometrical invariants but could also be influenced by these grouping effects.

Therefore, we have shifted our focus to the improved design used in Experiment 2 to provide stronger evidence for our theory. Building on this more robust design, we have extended our investigations to study location generalization (revised Experiment 3) and long-term learning effects (revised Figure 6—figure supplement 2). These enhancements allow us to provide stronger evidence for our theory while addressing potential confounds present in Experiment 1.

While we did not explicitly test the 90-degree rotation scenario in Experiment 1, future studies could employ more diverse set of stimuli within the Experiment 2 framework to better understand the limits and applicability of our theoretical predictions. We appreciate this suggestion, as it offers a valuable direction for further research.

Reviewer #1 (Recommendations For The Authors):

Major comments:

- A concise introduction to the Erlangen program, geometric invariants, and their structural stability would greatly enhance the paper. This would not only clarify these concepts for readers unfamiliar with them but also provide a more intuitive explanation for the choice of tasks and stimuli used in the study.

- I recommend adding a section that discusses how this new framework aligns with previous observations in VPL, especially those involving more classical stimuli like Gabors, random dot kinematograms, etc. This would help in contextualizing the framework within the broader spectrum of VPL research.

- Exploring how each level of invariant stability transfers within itself would be an intriguing addition. Previous theories often consider transfer within a condition. For instance, in an orientation discrimination task, a challenging training condition might transfer less to a new stimulus test location (e.g., a different visual quadrant). Applying a similar approach to examine how VPL generalizes to a new test location within a single invariant stability level could provide insightful contrasts between the proposed theory and existing ones. This would be particularly relevant in the context of Experiment 2, which could be adapted for such a test.

- I suggest including some example learning curves from the human experiment for a more clear demonstration of the differences in the learning rates across conditions. Easier conditions are expected to be learned faster (i.e. plateau faster to a higher accuracy level). The learning speed is reported for the DNN but not for the human subjects.

- In the modeling section, it would be beneficial to focus on offering an explanation for the observed generalization as a function of the stability of the invariants. As it stands, the neural network model primarily demonstrates that DNNs replicate the same generalization pattern observed in human experiments. While this finding is indeed interesting, the model currently falls short of providing deeper insights or explanations. A more detailed analysis of how the DNN model contributes to our understanding of the relationship between invariant stability and generalization would significantly enhance this section of the paper.

Minor comments:

- Line 46: "it is remains" --> "it remains"

- Larger font sizes for the vertical axis in Figure 6B would be helpful.

We thank your detailed and constructive comments, which have significantly helped us improve the clarity and rigor of our manuscript. Below, we provide a response to each point raised.

Major Comments

(1) A concise introduction to the Erlangen program, geometric invariants, and their structural stability:

We appreciate your suggestion to provide a clearer introduction to these foundational concepts. In the revised manuscript, we have added a dedicated section in the Introduction that offers a concise explanation of Klein’s Erlangen Program, including the concept of geometric invariants and their structural stability. This addition aims to make the theoretical framework more accessible to readers unfamiliar with these concepts and to better justify the choice of tasks and stimuli used in the study.

(2) Contextualizing the framework within the broader spectrum of VPL research:

We have expanded the Discussion section to better integrate our framework with previous VPL studies that reported generalization, including those using classical stimuli such as Gabors (Dosher and Lu, 2005; Hung and Seitz, 2014; Jeter et al., 2009; Liu and Pack, 2017; Manenti et al., 2023) and random dot kinematograms (Chang et al., 2013; Chen et al., 2016; Huang et al., 2007; Liu and Pack, 2017). In particular, we now discuss the similarities and differences between our findings and these earlier studies, exploring potential shared mechanisms underlying VPL generalization across different types of stimuli. These additions aim to contextualize our framework within the broader field of VPL research and highlight its relevance to existing literature.

(3) Exploring transfer within each invariant stability level:

In response to this insightful suggestion, we have added a new psychophysics experiment in the revised manuscript (Experiment 3) to examine how VPL generalizes to a new test location within the same invariant stability level. This experiment provides an opportunity to further explore the neural substrates underlying VPL of geometrical invariants, offering a contrast to existing theories and strengthening the connection between our framework and location generalization findings in the VPL literature.

(4) Including example learning curves from the human experiments:

We appreciate your suggestion to include learning curves for human subjects. In the revised manuscript, we have added learning curves of long-term VPL (see revised Figure 6—figure supplement 2) to track the temporal learning processes across invariant conditions. Interestingly, and in contrast to the results reported in the DNN simulations, these curves show that less stable invariants are learned faster and exhibit greater magnitudes of learning. We interpret this discrepancy as a result of differences in initial performance levels between humans and DNNs, as discussed in the revised Discussion section.

(5) Offering a deeper explanation of the DNN model's findings:

We acknowledge your concern that the modeling section primarily demonstrates that DNNs replicate human generalization patterns without offering deeper mechanistic insights. To address this, we have expanded the Results and Discussion sections to more explicitly interpret the weight change patterns observed across DNN layers in relation to invariant stability and generalization. We discuss how the model contributes to understanding the observed generalization within and across invariants with different stability, focusing on the neural network's role in generating predictions about the neural mechanisms underlying these effects.

Minor Comments

(1) Line 46: Correction of “it is remains” to “it remains”:

We have corrected this typo in the revised manuscript.

(2) Vertical axis font size in Figure 6B:

We have increased the font size of the vertical axis labels in revised Figure 8B for improved readability.

Reviewer #2 (Recommendations For The Authors):

(1) There are many details throughout the paper that are confusing, such as the caption for Figure 4, which does not appear to correspond to what is shown (and is perhaps a copy-paste of the caption for Experiment 1?). Similarly, I wasn't sure about many methodological details, like: How participants made their second response in Experiment 2? It says somewhere that they pressed the corresponding key to indicate which one was the target, but I didn't see anything explaining what that meant. Also, I couldn't tell if the items in the figures were representative of all trials; the stimuli were described minimally in the paper.

(2) The language in the paper felt slightly off at times, in minor but noticeable ways. Consider the abstract. The word "could" in the first sentence is confusing, and, more generally, that first sentence is actually quite vague (i.e., it just states something that would appear to be true of any perceptual system). In the following sentence, I wasn't sure what was meant by "prior to be perceived in the visual system". Though I was able to discern what the authors were intending to say most times, I was required to "read between the lines" a bit. This is not to fault the authors. But these issues need to be addressed, I think.

(1) We sincerely apologize for the oversight regarding the caption for (original) Figure 4, and thank you for pointing out this error. In the revised manuscript, we have corrected the caption for Figure 4 (revised Figure 5) and ensured it accurately describes the content of the figure. Additionally, we have strengthened the descriptions of the stimuli and tasks in both the Materials and Methods section and the captions for (revised) Figures 4 and 5 to provide a clearer and more comprehensive explanation of Experiment 2. These revisions aim to help readers fully understand the experimental design and methodology.

(2) We appreciate your feedback regarding the clarity and precision of the language in the manuscript. We acknowledge that some expressions, particularly in the abstract, were unclear or imprecise. In the revised manuscript, we have rewritten the abstract to improve clarity and ensure that the statements are concise and accurately convey our intended meaning. Additionally, we have thoroughly reviewed the entire manuscript to address any other instances of ambiguous language, aiming to eliminate the need for readers to "read between the lines." We are grateful for your suggestions, which have helped us enhance the overall readability of the paper.

eLife Assessment

This is a valuable paper that might contribute new insight into the role of GABA in semantic memory, which is a significant question in higher cognition. However, the empirical support for the main claims is incomplete. These results, once further strengthened and more appropriately discussed, will be of interest to broad readers of the neuroscience and cognitive neuroscience community.

Reviewer #1 (Public review):

Summary:

This study examined the changes in ATL GABA levels induced by cTBS and its relationship with BOLD signal changes and performance in a semantic task. The findings suggest that the increase in ATL GABA levels induced by cTBS is associated with a decrease in BOLD signal. The relationship between ATL GABA levels and semantic task performance is nonlinear, and more specifically, the authors propose that the relationship is an inverted U-shaped relationship.

Strengths:

The findings of the research regarding the increase of GABA and decrease of BOLD caused by cTBS, as well as the correlation between the two, appear to be reliable. This should be valuable for understanding the biological effects of cTBS.

Weakness:

I am pleased to see the authors' feedback on my previous questions and suggestions, and I believe the additional data analysis they have added is helpful. Here are my reserved concerns and newly discovered issues.

(1) Regarding the Inverted U-Shaped Curve In the revised manuscript, the authors have accepted some of my suggestions and conducted further analysis, which is now presented in Figure 3B. These results provide partial support for the authors' hypothesis. However, I still believe that the data from this study hardly convincingly support an inverted U-shaped distribution relationship.<br /> The authors stated in their response, "it is challenging to determine the optimal level of ATL GABA," but I think this is achievable. From Figures 4C and 4D, the ATL GABA levels corresponding to the peak of the inverted U-shaped curve fall between 85 and 90. In my understanding, this can be considered as the optimal level of ATL GABA estimated based on the existing data and the inverted U-shaped curve relationship. However, in the latter half of the inverted U-shaped curve, there are quite few data points, and such a small number of data points hardly provides reliable support for the quantitative relationship in the latter half of the curve. I suggest that the authors should at least explicitly acknowledge this and be cautious in drawing conclusions. I also suggest that the authors consider fitting the data with more types of non-linear relationships, such as a ceiling effect (a combination of a slope and a horizontal line), or a logarithmic curve.

(2) In Figure 2F, the authors demonstrated a strong practice effect in this study, which to some extent offsets the decrease in behavioral performance caused by cTBS. Therefore, I recommend that the authors give sufficient consideration to the practice effect in the data analysis.<br /> One issue is the impact of the practice effect on the classification of responders and non-responders. Currently, most participants are classified as non-responders, suggesting that the majority of the population may not respond to the cTBS used in this study. This greatly challenges the generalizability of the experimental conclusions. However, the emergence of so many non-responders is likely due to the prominent practice effect, which offsets part of the experimental effect. If the practice effect is excluded, the number of responders may increase. The authors might estimate the practice effect based on the vertex simulation condition and reclassify participants after excluding the influence of the practice effect.<br /> Another issue is that considering the significant practice effect, the analysis in Figure 4D, which mixes pre- and post-test data, may not be reliable.

(3) The analysis in Figure 3A has a double dipping issue. Suppose we generate 100 pairs of random numbers as pre- and post-test scores, and then group the data based on whether the scores decrease or increase; the pre-test scores of the group with decreased scores will have a very high probability of being higher than those of the group with increased scores. Therefore, the findings in Figure 3A seem to be meaningless.

(4) The authors use IE as a behavioral measure in some analyses and use accuracy in others. I recommend that the authors adopt a consistent behavioral measure.

Reviewer #2 (Public review):

Summary:

The authors combined inhibitory neurostimulation (continuous theta-burst stimulation, cTBS) with subsequent MRI measurements to investigate the impact of inhibition of the left anterior temporal lobe (ATL) on task-related activity and performance during a semantic task and link stimulation-induced changes to the neurochemical level by including MR spectroscopy (MRS). cTBS effects in the ATL were compared with a control site in the vertex. The authors found that relative to stimulation of the vertex, cTBS significantly increased the local GABA concentration in the ATL. cTBS also decreased task-related semantic activity in the ATL and potentially delayed semantic task performance by hindering a practice effect from pre to post. Finally, pooled data with their previous MRS study suggest an inverted u-shape between GABA concentration and behavioral performance. These results help to better understand the neuromodulatory effects of non-invasive brain stimulation on task performance.

Strengths:

Multimodal assessment of neurostimulation effects on the behavioral, neurochemical, and neural levels. In particular, the link between GABA modulation and behavior is timely and potentially interesting.

Weaknesses:

The analyses are not sound. Some of the effects are very weak and not all conclusions are supported by the data since some of the comparisons are not justified. There is some redundancy with a previous paper by the same authors, so the novelty and contribution to the field are overall limited. A network approach might help here.

Reviewer #3 (Public review):

Summary:

The authors used cTBS TMS, magnetic resonance spectroscopy (MRS), and functional magnetic resonance imaging (fMRI) as the main methods of investigation. Their data show that cTBS modulates GABA concentration and task-dependent BOLD in the ATL, whereby greater GABA increase following ATL cTBS showed greater reductions in BOLD changes in ATL. This effect was also reflected in the performance of the behavioural task response times, which did not subsume to practice effects after AL cTBS as opposed to the associated control site and control task. This is in line with their first hypothesis. The data further indicates that regional GABA concentrations in the ATL play a crucial role in semantic memory because individuals with higher (but not excessive) GABA concentrations in the ATLs performed better on the semantic task. This is in line with their second prediction. Finally, the authors conducted additional analyses to explore the mechanistic link between ATL inhibitory GABAergic action and semantic task performance. They show that this link is best captured by an inverted U-shaped function as a result of a quadratic linear regression model. Fitting this model to their data indicates that increasing GABA levels led to better task performance as long as they were not excessively low or excessively high. This was first tested as a relationship between GABA levels in the ATL and semantic task performance; then the same analyses were performed on the pre and post-cTBS TMS stimulation data, showing the same pattern. These results are in line with the conclusions of the authors.

Comments on revisions:

The authors have comprehensively addressed my comments from the first round of review, and I consider most of their answers and the steps they have taken satisfactorily. Their insights prompted me to reflect further on my own knowledge and thinking regarding the ATL function.

I do, however, have an additional and hopefully constructive comment regarding the point made about the study focusing on the left instead of bilateral ATL. I appreciate the methodological complexities and the pragmatic reasons underlying this decision. Nevertheless, briefly incorporating the justification for this decision into the manuscript would have been beneficial for clarity and completeness. The presented argument follows an interesting logic; however, despite strong previous evidence supporting it, the approach remains based on an assumption. Given that the authors now provide the group-level fMRI results captured more comprehensively in Supplementary Figure 2, where the bilateral pattern of fMRI activation can be observed in the current data, the authors could have strengthened their argument by asserting that the activation related to the given semantic association task in this data was bilateral. This would imply that the TMS effects and associated changes in GABA should be similar for both sites. Furthermore, it is worth noting the approach taken by Pobric et al. (2007, PNAS), who stimulated a site located 10 mm posterior to the tip of the left temporal pole along the middle temporal gyrus (MTG) and not the bilateral ATL.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study focuses on the role of GABA in semantic memory and its neuroplasticity. The researchers stimulated the left ATL and control site (vertex) using cTBS, measured changes in GABA before and after stimulation using MRS, and measured changes in BOLD signals during semantic and control tasks using fMRI. They analyzed the effects of stimulation on GABA, BOLD, and behavioral data, as well as the correlation between GABA changes and BOLD changes caused by the stimulation. The authors also analyzed the relationship between individual differences in GABA levels and behavioral performance in the semantic task. They found that cTBS stimulation led to increased GABA levels and decreased BOLD activity in the ATL, and these two changes were highly correlated. However, cTBS stimulation did not significantly change participants' behavioral performance on the semantic task, although behavioral changes in the control task were found after stimulation. Individual levels of GABA were significantly correlated with individuals' accuracy on the semantic task, and the inverted U-shaped (quadratic) function provides a better fit than the linear relationship. The authors argued that the results support the view that GABAergic inhibition can sharpen activated distributed semantic representations. They also claimed that the results revealed, for the first time, a non-linear, inverted-U-shape relationship between GABA levels in the ATL and semantic function, by explaining individual differences in semantic task performance and cTBS responsiveness

Strengths:

The findings of the research regarding the increase of GABA and decrease of BOLD caused by cTBS, as well as the correlation between the two, appear to be reliable. This should be valuable for understanding the biological effects of cTBS.

We appreciated R1’s positive evaluation of our manuscript.

Weaknesses:

Regarding the behavioral effects of GABA on semantic tasks, especially its impact on neuroplasticity, the results presented in the article are inadequate to support the claims made by the authors. There are three aspects of results related to this: 1) the effects of cTBS stimulation on behavior, 2) the positive correlation between GABA levels and semantic task accuracy, and 3) the nonlinear relationship between GABA levels and semantic task accuracy. Among these three pieces of evidence, the clearest one is the positive correlation between GABA levels and semantic task accuracy. However, it is important to note that this correlation already exists before the stimulation, and there are no results supporting that it can be modulated by the stimulation. In fact, cTBS significantly increases GABA levels but does not significantly improve performance on semantic tasks. According to the authors' interpretation of the results in Table 1, cTBS stimulation may have masked the practice effects that were supposed to occur. In other words, the stimulation decreased rather than enhanced participants' behavioral performance on the semantic task.

The stimulation effect on behavioral performance could potentially be explained by the nonlinear relationship between GABA and performance on semantic tasks proposed by the authors. However, the current results are also insufficient to support the authors' hypothesis of an inverted U-shaped curve. Firstly, in Figure 3C and Figure 3D, the last one-third of the inverted U-shaped curve does not have any data points. In other words, as the GABA level increases the accuracy of the behavior first rises and then remains at a high level. This pattern of results may be due to the ceiling effect of the behavioral task's accuracy, rather than an inverted U-shaped ATL GABA function in semantic memory. Second, the article does not provide sufficient evidence to support the existence of an optimal level of GABA in the ATL. Fortunately, this can be tested with additional data analysis. The authors can estimate, based on pre-stimulus data from individuals, the optimal level of GABA for semantic functioning. They can then examine two expectations: first, participants with pre-stimulus GABA levels below the optimal level should show improved behavioral performance after stimulation-induced GABA elevation; second, participants with pre-stimulus GABA levels above the optimal level should exhibit a decline in behavioral performance after stimulation-induced GABA elevation. Alternatively, the authors can categorize participants into groups based on whether their behavioral performance improves or declines after stimulation, and compare the pre- and post-stimulus GABA levels between the two groups. If the improvement group shows significantly lower pre-stimulus GABA levels compared to the decline group, and both groups exhibit an increase in GABA levels after stimulation, this would also provide some support for the authors' hypothesis.

Another issue in this study is the confounding of simulation effects and practice effects. According to the results, there is a significant improvement in performance after the simulation, at least in the control task, which the authors suggest may reflect a practice effect. The authors argue that the results in Table 1 suggest a similar practice effect in the semantic task, but it is masked by the simulation of the ATL. However, since no significant effects were found in the ANOVA analysis of the semantic task, it is actually difficult to draw a conclusion. This potential confound increases the risk in data analysis and interpretation. Specifically, for Figure 3D, if practice effects are taken into account, the data before and after the simulation should not be analyzed together.

We thank for the R1’s thoughtful comments. Due to the limited dataset, it is challenging to determine the optimal level of ATL GABA. Here, we re-grouped the participants into the responders and non-responders to address the issues R1 raised. It is important to note that we applied cTBS over the ATL, an inhibitory protocol, which decreases cortical excitability within the target region and semantic task performance (Chiou et al., 2014; Jung and Lambon Ralph, 2016). Therefore, responders and non-responders were classified according to their semantic performance changes after the ATL stimulation: subjects showing a decrease in task performance at the post ATL cTBS compared to the baseline were defined as responders; whereas subjects showing no changes or an increase in their task performance after the ATL cTBS were defined as non-responders. Here, we used the inverse efficiency (IE) score (RT/1-the proportion of errors) as individual semantic task performance to combine accuracy and RT. Accordingly, we had 7 responders and 10 non-responders.

Recently, we demonstrated that the pre-stimulation neurochemical profile of the ATL was associated with cTBS responsiveness on semantic processing (Jung et al., 2022). Specifically, the baseline GABA and Glx levels in the ATL predicted cTBS induced semantic task performance changes: individuals with higher GABA and lower Glx in the ATL would show bigger inhibitory effects and responders who decreased semantic task performance after ATL stimulation. Importantly, the baseline semantic task performance was significantly better in responders compared to non-responders. Thus, we expected that responders would show better semantic task performance along with higher ATL GABA levels in their pre-stimulation session relative to non-responders. We performed the planned t-tests to examine the difference in task performance and ATL GABA levels in pre-stimulation session. The results revealed that responders had lower IE (better task performance, t = -1.756, p = 0.050) and higher ATL GABA levels (t = 2.779, p = 0.006) in the pre-stimulation session (Figure 3).

In addition, we performed planned paired t-test to investigate the cTBS effects on semantic task performance and regional ATL GABA levels according to the groups (responders and non-responders). Responders showed significant increase of IE (poorer performance, t = -1.937, p = 0.050) and ATL GABA levels (t = -2.203, p = 0.035) after ATL cTBS. Non-responders showed decreased IE (better performance, t = 2.872, p = 0.009) and increased GABA levels in the ATL (t = -3.912, p = 0.001) after the ATL stimulation. The results were summarised in Figure 3.

It should be noted that there was no difference between the responders and non-responders in the control task performance at the pre-stimulation session. Both groups showed better performance after the ATL stimulation – practice effects (Author response image 1 below).

Author response image 1.

As we expected, our results replicated the previous findings (Jung et al., 2022) that responders who showed the inhibitory effects on semantic task performance after the ATL stimulation had higher GABA levels in the ATL than non-responders at their baseline, the pre-stimulation session. Importantly, cTBS increased ATL GABA levels in both responders and non-responders. These findings support our hypothesis – the inverted U-shaped ATL GABA function for cTBS response (Figure 4B). cTBS over the ATL resulted in the inhibition of semantic task performance among individuals initially characterized by higher concentrations of GABA in the ATL, indicative of better baseline semantic capacity. Conversely, the impact of cTBS on individuals with lower semantic ability and relatively lower GABA levels in the ATL was either negligible or exhibited a facilitatory effect. This study posits that individuals with elevated GABA levels in the ATL tend to be more responsive to cTBS, displaying inhibitory effects on semantic task performance (responders). On the contrary, those with lower GABA concentrations and reduced semantic ability were less likely to respond or even demonstrated facilitatory effects following ATL cTBS (non-responders). Moreover, our findings suggest the critical role of the baseline neurochemical profile in individual responsiveness to cTBS in the context of semantic memory. This highlights substantial variability among individuals in terms of semantic memory and its plasticity induced by cTBS.

Our analyses with responders and non-responders have highlighted significant inter-individual variability in both pre- and post-ATL stimulation sessions, including behavioural outcomes and ATL GABA levels. Responders showed distinctive neurochemical profiles in the ATL, associating with their task performance and responsiveness to cTBS in semantic memory. Our findings suggest that responders may possess an optimal level of ATL GABA conducive to efficient semantic processing. This results in enhanced semantic task performance and increased responsiveness to cTBS, leading to inhibitory effects on semantic processing following an inverted U-shaped function. On the contrary, non-responders, characterized by relatively lower ATL GABA levels, exhibited poorer semantic task performance compared to responders at the baseline. The cTBS-induced increase in GABA may contribute to their subsequent improvement in semantic performance. These results substantiate our hypothesis regarding the inverted U-shape function of ATL GABA and its relationship with semantic behaviour.

To address the confounding of simulation effects and practice effects in behavioural data, we used the IE and computed cTBS-induced performance changes (POST-PRE). Employing a 2 x 2 ANOVA with stimulation (ATL vs. Vertex) and task (Semantic vs. Control) as within subject factors, we found a significant task effect (F_{1, 15} = 6.656, p = 0.021) and a marginally significant interaction between stimulation and task (F_{1, 15} = 4.064, p = 0.061). Post hoc paired t-test demonstrated that ATL stimulation significantly decreased semantic task performance (positive IE) compared to both vertex stimulation (t = 1.905, p = 0.038) and control task (t = 2.814, p = 0.006). Facilitatory effects (negative IE) were observed in the control stimulation and control task. Please, see the Author response image 2 below. Thus, we believe that ATL cTBS induced task-specific inhibitory effects in semantic processing.

Author response image 2.

Accordingly, we have revised the Methods and Materials (p 25, line 589), Results (p8, line 188, p9-11, line 202- 248), Discussion (p19, line 441) and Figures (Fig. 2-3 & all Supplementary Figures).

Reviewer #2 (Public Review):

Summary:

The authors combined inhibitory neurostimulation (continuous theta-burst stimulation, cTBS) with subsequent MRI measurements to investigate the impact of inhibition of the left anterior temporal lobe (ATL) on task-related activity and performance during a semantic task and link stimulation-induced changes to the neurochemical level by including MR spectroscopy (MRS). cTBS effects in the ATL were compared with a control site in the vertex. The authors found that relative to stimulation of the vertex, cTBS significantly increased the local GABA concentration in the ATL. cTBS also decreased task-related semantic activity in the ATL and potentially delayed semantic task performance by hindering a practice effect from pre to post. Finally, pooled data from their previous MRS study suggest an inverted U-shape between GABA concentration and behavioral performance. These results help to better understand the neuromodulatory effects of non-invasive brain stimulation on task performance.

Strengths:

Multimodal assessment of neurostimulation effects on the behavioral, neurochemical, and neural levels. In particular, the link between GABA modulation and behavior is timely and potentially interesting.

We appreciated R2’s positive evaluation of our manuscript.

Weaknesses:

The analyses are not sound. Some of the effects are very weak and not all conclusions are supported by the data since some of the comparisons are not justified. There is some redundancy with a previous paper by the same authors, so the novelty and contribution to the field are overall limited. A network approach might help here.

Thank you for your thoughtful critique. We have taken your comments into careful consideration and have made efforts to address them.

We acknowledge the limitations regarding the strength of some effects and the potential lack of justification for certain conclusions drawn from the data. In response, we have reviewed our analyses and performed new analyses to address the behavioural discrepancies and strengthened the justifications for our conclusions.

Regarding the redundancy with a previous paper by the same authors, we understand your concern about the novelty and contribution to the field. We aim to clarify the unique contributions of our current study compared to our previous work. The main novelty lies in uncovering the neurochemical mechanisms behind cTBS-induced neuroplasticity in semantic representation and establishing a non-linear relationship between ATL GABA levels and semantic representation. Our previous work primarily demonstrated the linear relationship between ATL GABA levels and semantic processing. In the current study, we aimed to address two key objectives: 1) investigate the role of GABA in the ATL in short-term neuroplasticity in semantic representation, and 2) explore a biologically more plausible function between ATL GABA levels and semantic function using a larger sample size by combining data from two studies.

Additionally, we appreciate your suggestion regarding a network approach. We have explored the relationship between ATL GABA and cTBS-induced functional connectivity changes in our new analysis. However, there was no significant relationship between them. In the current study, our decision to focus on the mechanistic link between ATL GABA, task-induced activity, and individual semantic task performance reflects our intention to provide a detailed exploration of the role of GABA in the ATL and semantic neuroplasticity.

We have addressed the specific weaknesses raised by Reviewer #2 in detail in our response to 'Reviewer #2 Recommendations For The Authors'.

Reviewer #3 (Public Review):

Summary:

The authors used cTBS TMS, magnetic resonance spectroscopy (MRS), and functional magnetic resonance imaging (fMRI) as the main methods of investigation. Their data show that cTBS modulates GABA concentration and task-dependent BOLD in the ATL, whereby greater GABA increase following ATL cTBS showed greater reductions in BOLD changes in ATL. This effect was also reflected in the performance of the behavioural task response times, which did not subsume to practice effects after AL cTBS as opposed to the associated control site and control task. This is in line with their first hypothesis. The data further indicates that regional GABA concentrations in the ATL play a crucial role in semantic memory because individuals with higher (but not excessive) GABA concentrations in the ATLs performed better on the semantic task. This is in line with their second prediction. Finally, the authors conducted additional analyses to explore the mechanistic link between ATL inhibitory GABAergic action and semantic task performance. They show that this link is best captured by an inverted U-shaped function as a result of a quadratic linear regression model. Fitting this model to their data indicates that increasing GABA levels led to better task performance as long as they were not excessively low or excessively high. This was first tested as a relationship between GABA levels in the ATL and semantic task performance; then the same analyses were performed on the pre and post-cTBS TMS stimulation data, showing the same pattern. These results are in line with the conclusions of the authors.

Strengths:

I thoroughly enjoyed reading the manuscript and appreciate its contribution to the field of the role of the ATL in semantic processing, especially given the efforts to overcome the immense challenges of investigating ATL function by neuroscientific methods such as MRS, fMRI & TMS. The main strengths are summarised as follows:

• The work is methodologically rigorous and dwells on complex and complementary multimethod approaches implemented to inform about ATL function in semantic memory as reflected in changes in regional GABA concentrations. Although the authors previously demonstrated a negative relationship between increased GABA levels and BOLD signal changes during semantic processing, the unique contribution of this work lies within evidence on the effects of cTBS TMS over the ATL given by direct observations of GABA concentration changes and further exploring inter-individual variability in ATL neuroplasticity and consequent semantic task performance.

• Another major asset of the present study is implementing a quadratic regression model to provide insights into the non-linear relationship between inhibitory GABAergic activity within the ATLs and semantic cognition, which improves with increasing GABA levels but only as long as GABA levels are not extremely high or low. Based on this finding, the authors further pinpoint the role of inter-individual differences in GABA levels and cTBS TMS responsiveness, which is a novel explanation not previously considered (according to my best knowledge) in research investigating the effect of TMS on ATLs.

• There are also many examples of good research practice throughout the manuscript, such as the explicitly stated exploratory analyses, calculation of TMS electric fields, using ATL optimised dual echo fRMI, links to open source resources, and a part of data replicates a previous study by Jung et. al (2017).

We appreciated R3’s very positive evaluation of our manuscript.

Weaknesses:

• Research on the role of neurotransmitters in semantic memory is still very rare and therefore the manuscript would benefit from more context on how GABA contributes to individual differences in cognition/behaviour and more justification on why the focus is on semantic memory. A recommendation to the authors is to highlight and explain in more depth the particular gaps in evidence in this regard.

This is an excellent suggestion. Accordingly, we have revised our introduction, highlighting the role of GABA on individual differences in cognition and behaviour and research gap in this field.

Introduction p3, line 77   

“Research has revealed a link between variability in the levels of GABA in the human brain and  individual differences in cognitive behaviour (for a review, see 5). Specifically, GABA levels in the sensorimotor cortex were found to predict individual performance in the related tasks: higher GABA levels were correlated with a slower reaction time in simple motor tasks (12) as well as improved motor control (13) and sensory discrimination (14, 15). Visual cortex GABA concentrations were positively correlated with a stronger orientation illusion (16), a prolonged binocular rivalry (17), while displaying a negative correlation with motion suppression (17). Individuals with greater frontal GABA concentrations demonstrated enhanced working memory capacity (18, 19). Studies on learning have reported the importance of GABAergic changes in the motor cortex for motor and perceptual learning: individuals showing bigger decreases in local GABA concentration can facilitate this plasticity more effectively (12, 20-22). However, the relationship between GABAergic inhibition and higher cognition in humans remains unclear. The aim of the study was to investigate the role of GABA in relation to human higher cognition – semantic memory and its neuroplasticity at individual level.”

• The focus across the experiments is on the left ATL; how do the authors justify this decision? Highlighting the justification for this methodological decision will be important, especially given that a substantial body of evidence suggests that the ATL should be involved in semantics bilaterally (e.g. Hoffman & Lambon Ralph, 2018; Lambon Ralph et al., 2009; Rice et al., 2017; Rice, Hoffman, et al., 2015; Rice, Ralph, et al., 2015; Visser et al., 2010).

This is an important point, which we thank R3 for. Supporting the bilateral ATL systems in semantic representation, previous rTMS studies delivered an inhibitory rTMS in the left and right ATL and both ATL stimulation significantly decreased semantic task performance (Pobric et al., 2007 PNAS; 2010 Neuropsychologia; Lambon Ralph et al., 2009 Cerebral Cortex). Importantly, there was no significant difference on rTMS effects between the left and right ATL stimulation. Therefore, we assume that either left or right ATL stimulation could produce similar, intended rTMS effects on semantic processing. In the current study, we combined the cTBS with multimodal imaging to examine the cTBS effects in the ATL. Due to the design of the study (having a control site, control task, and control stimulation) and limitation of scanning time, we could have a target region for the simulation and chose the left ATL, which was the same MRS VOI of our precious study (Jung et al., 2017). This enabled us to combine the datasets to explore GABAergic function in the ATL.

• When describing the results, (Pg. 11; lines 233-243), the authors first show that the higher the BOLD signal intensity in ATL as a response to the semantic task, the lower the GABA concentration. Then, they state that individuals with higher GABA concentrations in the ATL perform the semantic task better. Although it becomes clearer with the exploratory analysis described later, at this point, the results seem rather contradictory and make the reader question the following: if increased GABA leads to less task-induced ATL activation, why at this point increased GABA also leads to facilitating and not inhibiting semantic task performance? It would be beneficial to acknowledge this contradiction and explain how the following analyses will address this discrepancy.

We apologised that our description was not clear. As R1 also commented this issue, we re-analysed behavioural results and demonstrated inter-individual variability in response to cTBS (Please, see the reply to R1 above).

• There is an inconsistency in reporting behavioural outcomes from the performance on the semantic task. While experiment 1 (cTBS modulates regional GANA concentrations and task-related BOLD signal changes in the ATL) reports the effects of cTBS TMS on response times, experiment 2 (Regional GABA concentrations in the ATL play a crucial role in semantic memory) and experiment 3 (The inverted U-shaped function of ATL GABA concentration in semantic processing) report results on accuracy. For full transparency, the manuscript would benefit from reporting all results (either in the main text or supplementary materials) and providing further explanations on why only one or the other outcome is sensitive to the experimental manipulations across the three experiments.

Regarding the inconsistency of behavioural outcome, first, there were inter- individual differences in our behavioural data (see the Figure below). Our new analyses revealed that there were responders and non-responders in terms of cTBS responsiveness (please, see the reply to R1 above. It should be noted that the classification of responders and non-responders was identical when we used semantic task accuracy). In addition, RT was compounded by practice effects (faster in the post-stimulation sessions), except for the ATL-post session. Second, we only found the significant relationship between semantic task accuracy and ATL GABA concentrations in both previous (Jung et al., 2017) and current study. ATL GABA levels were not correlated with semantic RT (Jung et al., 2017: r = 0.34, p = 0.14, current study: r = 0.26, p = 0.14). It should be noted that there were no significant correlations between ATL GABA levels and semantic inverse efficiency (IE) in both studies (Jung et al., 2017: r = 0.13, p = 0.62, current study: r = 0.22, p = 0.44). As a result, we found no significant linear and non-linear relationship between ATL GABA levels and RT (linear function R² = 0.21, p =0.45, quadratic function: R² = 0.17, p = 0.21) and between ATL GABA levels and IE (linear function R² = 0.24, p =0.07, quadratic function: R² = 2.24, p = 0.12). Thus, our data suggests that GABAergic action in the ATL may sharpen activated distributed semantic representations through lateral inhibition, leading to more accurate semantic performance (Isaacson & Scanziani., 2011; Jung et al., 2017).

We agreed with R3’s suggestion to report all results. The results of control task and control stimulation were included in Supplementary information (Figure S1, S4-5).

Overall, the most notable impact of this work is the contribution to a better understanding of individual differences in semantic behaviour and the potential to guide therapeutic interventions to restore semantic abilities in neurological populations. While I appreciate that this is certainly the case, I would be curious to read more about how this could be achieved.

Thank you once again to R3 for the positive evaluation of our study. We acknowledge your interest in understanding the practical implications of our findings. It is crucial to highlight the substantial variability in the effectiveness of rTMS and TBS protocols among individuals. Previous studies in healthy subjects have reported response rates ranging from 40% to 70% in the motor cortex, and in patients, the remission rate for rTMS treatment in treatment-resistant depression is around 29%. Presently, the common practice in rTMS treatment is to apply the same protocol uniformly to all patients.

Our study demonstrated that 40% of individuals in our sample were classified as responders to ATL cTBS. Notably, we observed differences in ATL GABA levels before stimulation between responders and non-responders. Responders exhibited higher baseline ATL GABA levels, along with better semantic performance at the baseline (as mentioned in our response to R1). This suggests that establishing the optimal level of ATL GABA by assessing baseline GABA levels before stimulation could enable the tailoring of an ideal protocol for each individual, thereby enhancing their semantic capability. To achieve this, more data is needed to delineate the proposed inverted U-shaped function of ATL GABA in semantic memory.

Our ongoing efforts involve collecting additional data from both healthy aging and dementia cohorts using the same protocol. Additionally, future pharmacological studies aim to modulate GABA, providing a deeper understanding of the individual variations in semantic function. These initiatives contribute to the potential development of personalized therapeutic interventions for individuals with semantic impairments.

Reviewer #1 (Recommendations For The Authors):

My major suggestion is to include an analysis regarding the "existence of an optimal GABA level". This would be the most direct test for the authors' hypothesis on the relationship between GABA and semantic memory and its neuroplasticity. Please refer to the public review section for details.

Here are some other suggestions and questions.

(1) The sample size of this study is relatively small. Although the sample size was estimated, a small sample size can bring risks to the generalizability of the results to the population. How did the author consider this risk? Is it necessary to increase the sample size?

We agreed with R1’s comments. However, the average of sample size in healthy individuals was 17.5 in TMS studies on language function (number of studies = 26, for a review, see Qu et al, 2022 Frontiers in Human Neuroscience), 18.3 in the studies employing rTMS and fMRI on language domain (number of studies = 8, for a review, see Hartwigsen & Volz., 2021 NeuroImage), and 20.8 in TMS combined MRS studies (number of studies = 11, for a review, see Cuypers & Marsman., 2021 NeuroImage). Notably, only two studies utilizing rTMS, fMRI, and MRS had sample sizes of N = 7 (Grohn et al., 2019 Frontiers in Neuroscience) and N = 16 (Rafique & Steeves. 2020 Brain and Behavior). Despite having 19 participants in our current study, it is noteworthy that our sample size aligns closely with studies employing similar approaches and surpasses those employing the same methodology.

As a result of the changes in a scanner and the relocation of the authors to different institutes, it is impossible to increase the sample size for this study.

(2) How did the authors control practice effects? How many practice trials were arranged before the experiment? Did you avoid the repetition of stimuli in tasks before and after the stimuli?

At the beginning of the experiment, participants performed the practice session (20 trials) for each tasks outside of the scanner. Stimuli in tasks were not repeated before and after stimulation sessions.

(3) In Figures 2D and E, does the vertical axis of the BOLD signal refer to the semantic task itself or the difference between the semantic and control tasks? Could you provide the respective patterns of the BOLD signal before and after the stimuli in the semantic and control tasks in a figure?

We apologised that the names of axis of Figure 2 were not clear. In Fig 2D-E, the BOLD signal changes refer to the semantic task itself. Accordingly, we have revised the Fig. 2.

(4) Figure 1A shows that MRS ATL always comes before MRS Vertex. Was the order of them counterbalanced across participants?

The order of MRS acquisition was not counterbalanced across participants.

(5) I am confused by the statement "Our results provide strong evidence that regional GABA levels increase following inhibitory cTBS in the human associative cortex, specifically in the ATL, a representational semantic hub. Notably, the observed increase was specific to the ATL and semantic processing, as it was not observed in the control region (vertex) and not associated with control processing (visuospatial processing)". GABA levels are obtained in the MRS, and this stage does not involve any behavioral tasks. Why do the authors state that the increase in GABA levels was specific to semantic processing and was not associated with control processing?

Following R1’s suggestion, we have re-analysed behavioural data and showed cTBS-induced suppression in semantic task performance after ATL stimulation only (please, see the reply above). There were no cTBS effects in the control task performance, control site (vertex) and no correlations between the ATL GABA levels and control task performance. The Table was added to the Supplementary Information as Table S3.

(6) In Figure 3, the relationship between GABA levels in the ATL and performance on semantic tasks is presented. What is the relationship between GABA levels at the control site and performance on semantic tasks? Should a graph be provided to illustrate this?

As the vertex was not involved in semantic processing (no activation during semantic processing), we did not perform the analysis between vertex GABA levels and semantic task performance. Following R3’s suggestion, we performed a linear regression between vertex GABA levels and semantic task performance in the pre-stimulation session, accounting for GM volume, age, and sex. As we expected that there was no significant relationship between them. (R² = 0.279, p = 0.962).

(7) The author claims that GABA can sharpen distributed semantic representations. However, even though there is a positive correlation between GABA levels and semantic performance, there is no direct evidence supporting the inference that this correlation is achieved through sharpening distributed semantic representations. How did the author come to this conclusion? Are there any other possibilities?

We showed that ATL GABA concentrations in pre-stimulation was ‘negatively’ correlated with task-induced regional activity in the ATL and ‘positively’ correlated with semantic task performance. In our semantic task, such as recognizing a camel (Fig. 1), the activation of all related information in the semantic representation (e.g., mammal, desert, oasis, nomad, humps, & etc.) occurs. To respond accurately to the task (a cactus), it becomes essential to suppress irrelevant meanings through an inhibitory mechanism. Therefore, the inhibitory processing linked to ATL GABA levels may contribute to more efficient processing in this task.

Animal studies have proposed a related hypothesis in the context of the close interplay between activation and inhibition in sensorimotor cortices (Isaacson & Scanziani., 2011). Liu et al (2011, Neuron) demonstrated that the rise of excitatory glutamate in the visual cortex is followed by the increase of inhibitory GABA in response to visual stimuli. Tight coupling of these paired excitatory-inhibitory functions results in a sharpening of the activated representation. (for a review, see Isaacson & Scanziani., 2011 Neuron How Inhibition Shapes Cortical Activity). In human, Kolasinski et al (2017, Current Biology) revealed that higher sensorimotor GABA levels are associated with more selective cortical tuning measured fMRI, which in turn is associated with enhanced perception (better tactile discrimination). They claimed that the relationship between inhibition and cortical tuning could result from GABAergic signalling, shaping the selective response profiles of neurons in the primary sensory regions of the brain. This process is crucial for the topographic organization (task-induced fMRI activation in the sensorimotor cortex) vital to sensory perception.

Building on these findings, we suggest a similar mechanism may operate in higher-order association cortices, including the ATL semantic hub. This suggests a process that leads to more sharply defined semantic representations associated with more selective task-induced activation in the ATL and, consequently, more accurate semantic performance (Jung et al., 2017).

Reviewer #2 (Recommendations For The Authors):

Major issues:

(1) It wasn't completely clear what the novel aspect of this study relative to their previous one on GABAergic modulation in semantic memory issue, this should be clarified. If I understand correctly, the main difference from the previous study is that this study considers the TMS-induced modulation of GABA?

We apologise that the novelty of study was not clear. The main novelty lies in uncovering the neurochemical mechanisms behind cTBS-induced neuroplasticity in semantic representation and establishing a non-linear relationship between ATL GABA levels and semantic representation. Our previous work firstly demonstrated the linear relationship between the ATL GABA levels and semantic processing. In the current study, we aimed to address two key objectives: 1) investigate the role of GABA in the ATL in short-term neuroplasticity in semantic representation, and 2) explore a biologically more plausible function between ATL GABA levels and semantic function using a larger sample size by combining data from two studies.

The first part of the experiment in this study mirrored our previous work, involving multimodal imaging during the pre-stimulation session. We conducted the same analysis as in our previous study to replicate the findings in a different cohort. Subsequently, we combined the data from both studies to examine the potential inverted U-shape function between ATL GABA levels and semantic function/neuroplasticity.

Accordingly, we have revised the Introduction by adding the following sentences.

“The study aimed to investigate the neural mechanisms underlying cTBS-induced neuroplasticity in semantic memory by linking cortical neurochemical profiles, task-induced regional activity, and variability in semantic memory capability within the ATL.”

“Furthermore, to address and explore the relationship between regional GABA levels in the ATL and semantic memory function, we combined data from our previous study (Jung et al., 2017) with the current study’s data.”

(2) I found the scope of the study very narrow. I guess everyone agrees that TMS induces network effects, but the authors selectively focus on the modulation in the ATL. This is unfortunate since semantic memory requires the interaction between several brain regions and a network perspective might add some novel aspect to this study which has a strong overlap with their previous one. I am aware that MRS can only measure pre-defined voxels but even these changes could be related to stimulation-induced effects on task-related activity at the whole brain level.

We appreciate R2's thoughtful comments and acknowledge the concern about the perceived narrow scope of the study. We agreed with the notion that cTBS induces network-level changes. In our investigation, we did observe cTBS over the ATL influencing task-induced regional activity in other semantic regions and functional connectivity within the semantic system. Specifically, ATL cTBS increased activation in the right ATL after ATL stimulation compared to pre-stimulation, along with increased functional connectivity between the left and right ATL, between the left ATL and right semantic control regions (IFG and pMTG), and between the left ATL and right angular gyrus. These results were the replication of Jung & Lambon Ralph (2016) Cerebral Cortex.

However, it is important to note that we did not find any significant correlations between ATL GABA changes and cTBS-induced changes in the functional connectivity. Consequently, we are currently preparing another paper that specifically addresses the network-level changes induced by ATL cTBS. In the current study, our decision to focus on the mechanistic link between ATL GABA, task-induced activity, and individual semantic task performance reflects our intention to provide a detailed exploration of the role of GABA in the ATL and semantic neuroplasticity.

(3) On a related note, I think the provided link between GABAergic modulation and behavioral changes after TMS is somehow incomplete because it ignores the stimulation effects on task-related activity. Could these be linked in a regression analysis with two predictors (with behavior or GABA level as a criterion and the other two variables as predictors)?

In response to R2’s suggestion, we performed a multiple regression analysis, by modelling cTBS-induced ATL GABA changes (POST-PRE), task-related BODL signal changes (POST-PRE), and semantic task performance (IE) changes (POST-PRE). The model with GABA changes (POST-PRE) as a criterion was significant (F_{2, 14} = 8.77, p = 0.003), explaining 56% of cTBS-induced ATL GABA changes (adjusted R²) with cTBS-related ATL BOLD signal changes and semantic task performance changes. However, the model with semantic task performance change (POST-PRE) as a criterion was not significant (F = 0.26, p = 0.775). Therefore, cTBS-induced changes in ATL BOLD signals and semantic task performance significantly predicted the cTBS-induced ATL GABA changes. It was found that cTBS-induced ATL BOLD signal changes significantly predicted cTBS-induced GABA changes in the ATL (β = -4.184, p = 0.001) only, aligning with the results of our partial correlation analysis.

Author response table 1.

(4) Several statements in the intro and discussion need to be rephrased or toned down. For example, I would not agree that TBS "made healthy individuals mimic semantic dementia patients". This is clearly overstated. TMS protocols slightly modulate brain functions, but this is not similar to lesions or brain damage. Please rephrase. In the discussion, it is stated that the results provide "strong evidence". I disagree based on the overall low values for most comparisons.

Hence, we have revised both the Introduction and the Discussion.

“Perturbing the ATL with inhibitory repetitive transcranial magnetic stimulation (rTMS) and theta burst stimulation (TBS) resulted in healthy individuals exhibiting slower reaction times during semantic processing.”

“Our results demonstrated an increase in regional GABA levels following inhibitory cTBS in human associative cortex, specifically in the ATL, a representational semantic hub.”

(5) Changes in the BOLD signal in the ATL: There is a weak interaction between stimulation and VOI and post hoc comparisons with very low values reported. Are these corrected for multiple comparisons? I think that selectively reporting weak values with small-volume corrections (if they were performed) does not provide strong evidence. What about whole-brain effects and proper corrections for multiple comparisons?

There was no significant interaction between the stimulation (ATL vs. Vertex) and session (pre vs post) in the ATL BOLD signal changes (p = 0.29). Our previous work combining rTMS with fMRI (Binney et al., 2015; Jung & Lambon Ralph, 2016) demonstrated that there was no significant rTMS effects on the whole brain analysis and only ROI analyses revealed the subtle but significant rTMS effects in the target site (reduction of task-induced ATL activity). In the current study, we focused our hypothesis on the anticipated decrease in task-induced regional activity in the ATL during semantic processing following the inhibitory cTBS. Accordingly, we conducted planned paired t-tests specifically within the ATL for BOLD signal changes without applying multiple comparison corrections. It's noted that these results were derived from regions of interest (ROIs) and not from small-volume corrections. Furthermore, no significant findings emerged from the comparison of the ATL post-session vs. Vertex post-session and the ATL pre-session vs. ATL post-session in the whole-brain analysis (see Supplementary figure 2).

Accordingly, we have added the Figure S2 in the Supplementary Information.

(6) Differences between selected VOIs: Numerically, the activity (BOLD signal effect) is higher in the vertex than the ATL, even in the pre-TMS session (Figure 2D). What does that mean? Does that indicate that the vertex also plays a role in semantic memory?

We apologise that the figure was not clear. Fig. 2D displays the BOLD signal changes in the ATL VOI for the ATL and Vertex stimulation. As there was no activation in the vertex during semantic processing, we did not present the fMRI results of vertex VOI (please, see Author response image 3 below). Accordingly, we have revised the label of Y axis of the Figure 2D – ATL BOLD signal change.

Author response image 3.

The cTBS effects within the Vertex VOI during semantic processing

(7) Could you provide the e-field for the vertex condition?

We have added it in the Supplementary Information as Supplementary Figure 6.

(8) Stimulation effects on performance (RTs): There is a main effect of the session in the control task. Post-hoc tests show that control performance is faster in the post-pre comparison, while the semantic task is not faster after ATL TMS (as it might be delayed). I think you need to perform a 3-way ANOVA here including the factor task if you want to show task specificity (e.g., differences for the control but not semantic task) and then a step-down ANOVA or t-tests.

Thanks for R2’s suggestion. We have addressed this issue in reply to R1. Please, see the reply to R1 for semantic task performance analysis.

Minor issue:

In the visualization of the design, it would be helpful to have the timing/duration of the different measures to directly understand how long the experiment took.

We have added the duration of the experiment design in the Figure 1.

Reviewer #3 (Recommendations For The Authors):

Further Recommendations:

• Pg. 6; lines 138-147: There is a sense of uncertainty about the hypothesis conveyed by expressions such as 'may' or 'could be'. A more confident tone would be beneficial.

Thanks for R3’s thoughtful suggestion. We have revised the Introduction.

• Pg. 6; line 155: left or bilateral ATL, please specify.

We have added ‘left’ in the manuscript.

• Pg. 8; line 188: Can the authors provide a table with peak activations to complement the figure?

We have added the Table for the fMRI results in the Supplementary Information (Table S1).

• Pg 9; Figure 2C: The ATL activation elicited by the semantic task seems rather medial. What are the exact peak coordinates for this cluster, and how can the authors demonstrate that the electric fields induced by TMS, which seem rather lateral (Figure 2A), also impacted this area? Please explain.

We apologise that the Figure was not clear. cTBS was delivered to the peak coordinate of the left ventral ATL [-36, -15, -30] determined by previous fMRI studies (Binney et al., 2010; Visser et al., 2012). To confirm the cTBS effects at the target region, we conducted ROI analysis centred in the ventral ATL [-36, -15, -30] and the results demonstrated a reduced ATL activity after ATL stimulation during semantic processing (t = -2.43, p = 0.014) (please, see Author response image 4 below). Thus, cTBS successfully modulated the ATL activity reaching to the targe coordinate.

Author response image 4.

• Pg.23; line 547: What was the centre coordinate of the ROI (VOI), and was it consistent across all participants? Please specify.

We used the ATL MRS VOI (a hexahedron with 4cm x 2cm x 2cm) for our regions of interest analysis and the central coordinate was around -45, -12, -20 (see Author response image 5). As we showed in Fig. 1C, the location of ATL VOI was consistent across all participants.

Author response image 5.

• Pg. 24; line 556-570: What software was used for performing the statistical analyses? Please specify.

We have added the following sentence.

“Statistical analyses were undertaken using Statistics Package for the Social Sciences (SPSS, Version 25, IBM Cary, NC, USA) and RStudio (2023).”

• Pg. 21; line 472-480: It is not clear if and how neuronavigation was used (e.g. were T1scans or an average MNI template used, what was the exact coordinate of stimulation and how was it decided upon). Please specify.

We apologised the description was not clear. We have added a paragraph describing the procedure.

“The target site in the left ATL was delineated based on the peak coordinate (MNI -36 -15 -30), which represents maximal peak activation observed during semantic processing in previous distortion-corrected fMRI studies (38, 41). This coordinate was transformed to each individual’s native space using Statistical Parametric Mapping software (SPM8, Wellcome Trust Centre for Neuroimaging, London, UK). T1 images were normalised to the MNI template and then the resulting transformations were inverted to convert the target MNI coordinate back to the individual's untransformed native space coordinate. These native-space ATL coordinates were subsequently utilized for frameless stereotaxy, employing the Brainsight TMS-MRI co-registration system (Rogue Research, Montreal, Canada). The vertex (Cz) was designated as a control site following the international 10–20 system.”

• Miscellaneous

- line 57: insert 'about' to the following sentence: '....little is known the mechanisms linking'

- line 329: 'Previous, we demonstrated'....should be Previously we demonstrated....

We thank for R3’s thorough evaluation our manuscript. We have revised them.

Furthermore, it would be an advantage to make the data freely available for the benefit of the broader scientific community.

We appreciate Reviewer 3’s suggestion. Currently, this data is being used in other unpublished work. However, upon acceptance of this manuscript, we will make the data freely available for the benefit of the broader scientific community.

Chiou R, Sowman PF, Etchell AC, Rich AN (2014) A conceptual lemon: theta burst stimulation to the left anterior temporal lobe untangles object representation and its canonical color. J Cogn Neurosci 26:1066-1074.

Jung J, Lambon Ralph MA (2016) Mapping the Dynamic Network Interactions Underpinning Cognition: A cTBS-fMRI Study of the Flexible Adaptive Neural System for Semantics. Cereb Cortex 26:3580-3590.

Jung J, Williams SR, Sanaei Nezhad F, Lambon Ralph MA (2017) GABA concentrations in the anterior temporal lobe predict human semantic processing. Sci Rep 7:15748.

Jung J, Williams SR, Nezhad FS, Lambon Ralph MA (2022) Neurochemical profiles of the anterior temporal lobe predict response of repetitive transcranial magnetic stimulation on semantic processing. Neuroimage 258:119386.

eLife Assessment

This valuable study investigates the immune system's role in pre-eclampsia. The authors map the immune cell landscape of the human placenta and find an increase in macrophages and Th17 cells in patients with pre-eclampsia. Following mouse studies, the authors suggest that the IGF1-IGF1R pathway might play a role in how macrophages influence T cells, potentially driving the pathology of pre-eclampsia. There is convincing evidence in this study that will be of interest to immunologists and developmental biologists.

Reviewer #1 (Public review):

Summary:

This study explores the immune microenvironment of the placenta in preeclampsia (PE), which is often accompanied by gestational diabetes mellitus (GDM). Using CyTOF, they found that placentas from PE cases showed increased frequencies of memory-like Th17 cells, memory-like CD8⁺ T cells, and pro-inflammatory macrophages, alongside decreased levels of anti-inflammatory macrophages and granulocyte myeloid-derived suppressor cells (gMDSCs) compared to normal pregnancies. Further analysis revealed a positive correlation between pro-inflammatory macrophages and the expanded T cell populations, and a negative correlation with gMDSCs. Single-cell RNA sequencing provided mechanistic insights: transferring a specific subset of pro-inflammatory macrophages (F4/80⁺CD206⁻ with a distinct gene expression profile) from the uterus of PE mice to normal pregnant mice induced the formation of pathogenic memory-like Th17 cells via the IGF1-IGF1R pathway. This cellular interplay not only contributed to the development but also to the recurrence of PE. Additionally, these macrophages promoted the production of memory-like CD8⁺ T cells while inhibiting gMDSCs at the maternal-fetal interface, culminating in PE-like symptoms in mice. In conclusion, the study identifies a PE-specific immune cell network regulated by pro-inflammatory macrophages, offering new insights into the pathogenesis of preeclampsia.

Strengths:

Utilization of both human placental samples and multiple mouse models to explore the mechanisms linking inflammatory macrophages and T cells to preeclampsia (PE).<br /> Incorporation of cutting-edge and complementary techniques such as CyTOF, scRNA-seq, bulk RNA-seq, and flow cytometry.

Identification of specific immune cell populations and their roles in PE.<br /> Demonstration of the adverse effects of pro-inflammatory macrophages and T cells on pregnancy outcomes through in vivo manipulations.

Comments on revised version:

Several weaknesses were addressed during revision by conducting additional experiments, clarifying the manuscript's text, and incorporating new data that was not initially included.

Reviewer #2 (Public review):

Summary:

Fei, Lu, Shi, et al. present a thorough evaluation of the immune cell landscape in pre-eclamptic human placentas by single-cell multi-omics methodologies compared to normal control placentas. Based on their findings of elevated frequencies of inflammatory macrophages and memory-like Th17 cells, they employ adoptive cell transfer mouse models to interrogate the coordination and function of these cell types in pre-eclampsia immunopathology. They demonstrate the putative role of the IGF1-IGF1R axis as the key pathway by which inflammatory macrophages in the placenta skew CD4+ T cells towards an inflammatory IL-17A-secreting phenotype that may drive tissue damage, vascular dysfunction, and elevated blood pressure in pre-eclampsia, leaving researchers with potential translational opportunities to pursue this pathway in this indication.

They present a major advance to the field in their profiling of human placental immune cells from pre-eclampsia patients where most extant single-cell atlases focus on term versus preterm placenta, or largely examine trophoblast biology with a much rarer subset of immune cells. While the authors present vast amounts of data at both the protein and RNA transcript level, we, the reviewers, feel this manuscript is still in need of much more clarity in its main messaging, and more discretion in including only key data that supports this main message most effectively.

Strengths:

(1) This study combines human and mouse analyses and allows for some amount of mechanistic insight into the role of pro-inflammatory and anti-inflammatory macrophages in the pathogenesis of pre-eclampsia (PE), and their interaction with Th17 cells.

(2) Importantly, they do this using matched cohorts across normal pregnancy and common PE comorbidities like gestation diabetes (GDM).

(3) The authors have developed clear translational opportunities from these "big data" studies by moving to pursue potential IGF1-based interventions.

[Editors' note: the authors have provided responses to the previously identified weaknesses]

Author response:

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

Public Reviews:

Reviewer #1(Public review):

Strengths:

Utilization of both human placental samples and multiple mouse models to explore the mechanisms linking inflammatory macrophages and T cells to preeclampsia (PE).<br /> Incorporation of advanced techniques such as CyTOF, scRNA-seq, bulk RNA-seq, and flow cytometry.

Identification of specific immune cell populations and their roles in PE, including the IGF1-IGF1R ligand-receptor pair in macrophage-mediated Th17 cell differentiation.<br /> Demonstration of the adverse effects of pro-inflammatory macrophages and T cells on pregnancy outcomes through transfer experiments.

Weaknesses:

Comment 1. Inconsistent use of uterine and placental cells, which are distinct tissues with different macrophage populations, potentially confounding results.

Response1: We thank the reviewers' comments. We have done the green fluorescent protein (GFP) pregnant mice-related animal experiment, which was not shown in this manuscript. The wild-type (WT) female mice were mated with either transgenic male mice, genetically modified to express GFP, or with WT male mice, in order to generate either GFP-expressing pups (GFP-pups) or their genetically unmodified counterparts (WT-pups), respectively. Mice were euthanized on day 18.5 of gestation, and the uteri of the pregnant females and the placentas of the offspring were analyzed using flow cytometry. The majority of macrophages in the uterus and placenta are of maternal origin, which was defined by GFP negative. In contrast, fetal-derived macrophages, distinguished by their expression of GFP, represent a mere fraction of the total macrophage population. We have added the GFP pregnant mice-related data in uterine and placental cells (Line204-212).

Comment 2. Missing observational data for the initial experiment transferring RUPP-derived macrophages to normal pregnant mice.

Response 2: We thank the reviewers' comments. We have added the observational data (Figure 4-figure supplement 1D, 1E） and a corresponding description of the data (Line 198-203).

Comment 3. Unclear mechanisms of anti-macrophage compounds and their effects on placental/fetal macrophages.

Response 3: We thank the reviewers' comments. PLX3397, the inhibitor of CSF1R, which is needed for macrophage development (Nature. 2023, PMID: 36890231; Cell Mol Immunol. 2022, PMID: 36220994), we have stated that on Line 227-230. However, PLX3397 is a small molecule compound that possesses the potential to cross the placental barrier and affect fetal macrophages. We have discussed the impact of this factor on the experiment in the Discussion section (Line457-459).

Comment 4. Difficulty in distinguishing donor cells from recipient cells in murine single-cell data complicates interpretation.

Response 4: We thank the reviewers' comments. Upon analysis, we observed a notable elevation in the frequency of total macrophages within the CD45⁺ cell population. Then we subsequently performed macrophage clustering and uncovered a marked increase in the frequency of Cluster 0, implying a potential correlation between Cluster 0 and donor-derived cells. RNA sequencing revealed that the F480⁺CD206^- pro-inflammatory donor macrophages exhibited a Folr2⁺Ccl7⁺Ccl8⁺C1qa⁺C1qb⁺C1qc⁺ phenotype, which is consistent with the phenotype of cluster 0 in macrophages observed in single-cell RNA sequencing (Figure 4D and Figure 5E). Therefore, we believe that the donor cells should be cluster 0 in macrophages.

Comment 5. Limitation of using the LPS model in the final experiments, as it more closely resembles systemic inflammation seen in endotoxemia rather than the specific pathology of PE.

Response 5: We thank the reviewers' comments. Firstly, our other animal experiments in this manuscript used the Reduction in Uterine Perfusion Pressure (RUPP) mouse model to simulate the pathology of PE. However, the RUPP model requires ligation of the uterine arteries in pregnant mice on day 12.5 of gestation, which hinders T cells returning from the tail vein from reaching the maternal-fetal interface. In addition, this experiment aims to prove that CD4⁺ T cells are differentiated into memory-like Th17 cells through IGF-1R receptor signaling to affect pregnancy by clearing CD4⁺ T cells in vivo with an anti-CD4 antibody followed by injecting IGF-1R inhibitor-treated CD4⁺ T cells. And we proved that injection of RUPP-derived memory-like CD4⁺ T cells into pregnant mice induces PE-like symptoms (Figure 6F-6H). In summary, the application of the LPS model in the final experiments does not affect the conclusions.

Reviewer #2 (Public review):

Strengths:

(1) This study combines human and mouse analyses and allows for some amount of mechanistic insight into the role of pro-inflammatory and anti-inflammatory macrophages in the pathogenesis of pre-eclampsia (PE), and their interaction with Th17 cells.

(2) Importantly, they do this using matched cohorts across normal pregnancy and common PE comorbidities like gestation diabetes (GDM).

(3) The authors have developed clear translational opportunities from these "big data" studies by moving to pursue potential IGF1-based interventions.

Weaknesses:

(1) Clearly the authors generated vast amounts of multi-omic data using CyTOF and single-cell RNA-seq (scRNA-seq), but their central message becomes muddled very quickly. The reader has to do a lot of work to follow the authors' multiple lines of inquiry rather than smoothly following along with their unified rationale. The title description tells fairly little about the substance of the study. The manuscript is very challenging to follow. The paper would benefit from substantial reorganizations and editing for grammatical and spelling errors. For example, RUPP is introduced in Figure 4 but in the text not defined or even talked about what it is until Figure 6. (The figure comparing pro- and anti-inflammatory macrophages does not add much to the manuscript as this is an expected finding).

Response 1: We thank the reviewers' comments. According to the reviewer's suggestion, we have made the necessary revisions. Firstly, the title of the article has been modified to be more specific. We also introduce the RUPP mouse model when interpreted Figure 4-figure supplement 1. Thirdly, We have moved the images of Figure 7 to the Figure 6-figure supplement 2 make them easier to follow. Finally, we diligently corrected the grammatical and spelling errors in the article. As for the figure comparing pro- and anti-inflammatory macrophages, the Editor requested a more comprehensive description of the macrophage phenotype during the initial submission. As a result, we conducted the transcriptome RNA-seq of both uterine-derived pro-inflammatory and anti-inflammatory macrophages and conducted a detailed analysis of macrophages in scRNA-seq.

Comment 2. The methods lack critical detail about how human placenta samples were processed. The maternal-fetal interface is a highly heterogeneous tissue environment and care must be taken to ensure proper focus on maternal or fetal cells of origin. Lacking this detail in the present manuscript, there are many unanswered questions about the nature of the immune cells analyzed. It is impossible to figure out which part of the placental unit is analyzed for the human or mouse data. Is this the decidua, the placental villi, or the fetal membranes? This is of key importance to the central findings of the manuscript as the immune makeup of these compartments is very different. Or is this analyzed as the entirety of the placenta, which would be a mix of these compartments and significantly less exciting?

Response 2: We thank the reviewers' comments. Placental villi rather than fetal membranes and decidua were used for CyToF in this study. This detail about how human placenta samples were processed have been added to the Materials and Methods section (Line564-576).

Comment 3. Similarly, methods lack any detail about the analysis of the CyTOF and scRNAseq data, much more detail needs to be added here. How were these clustered, what was the QC for scRNAseq data, etc? The two small paragraphs lack any detail.

Response 3: We thank the reviewers' comments. The details about the analysis of the CyTOF (Line577-586) and scRNAseq (Line600-615) data have been added in the Materials and Methods section.

Comment 4. There is also insufficient detail presented about the quantities or proportions of various cell populations. For example, gdT cells represent very small proportions of the CyTOF plots shown in Figures 1B, 1C, & 1E, yet in Figures 2I, 2K, & 2K there are many gdT cells shown in subcluster analysis without a description of how many cells are actually represented, and where they came from. How were biological replicates normalized for fair statistical comparison between groups?

Response 4: We thank the reviewers' comments. In our study, approximately 8×10^⁵ cells were collected per group for analysis using CyTOF. Of these, about 10% (8×10^⁴ cells per group) were utilized to generate Figure 1B. As depicted in Figure 1B, gdT cells constitute roughly 1% of each group, with specific percentages as follows: NP group (1.23%), PE group (0.97%), GDM group (0.94%), and GDM&PE group (1.26%), which equates to approximately 800 cells per group. For the subsequent gdT cell analysis presented in Figure 2I, we employed data from all cells within each group to construct the tSNE maps, comprising approximately 8000 cells per group. Consequently, it may initially appear that the number of gdT cells is significantly higher than what is shown in Figure 1B. To clarify this, we have included pertinent explanations in the figure legend. Given the relatively low proportions of gdT cells, we did not pursue further investigations of these cells in subsequent experiments. Following your suggestion, we have relocated this result to the supplementary materials, where it is now presented as Figure 2-figure supplement 1D-E.

The number of biological replicates (samples) is consistent with Figure 1, and this information has been added to the figure legend.

Comment 5. The figures themselves are very tricky to follow. The clusters are numbered rather than identified by what the authors think they are, the numbers are so small, that they are challenging to read. The paper would be significantly improved if the clusters were clearly labeled and identified. All the heatmaps and the abundance of clusters should be in separate supplementary figures.

Response 5: We thank the reviewers' comments. Based on your suggestions, we have labeled and defined the Clusters (Figure 2A, 2F, Figure 3A, Figure 5C and Figure 6A). Additionally, we have moved most of the heatmaps to the supplementary materials.

Comment 6. The authors should take additional care when constructing figures that their biological replicates (and all replicates) are accurately represented. Figure 2H-2K shows N=10 data points for the normal pregnant (NP) samples when clearly their Table 1 and test denote they only studied N=9 normal subjects.

Response 6: We thank the reviewers' careful checking. During our verification, we found that one sample in the NP group had pregnancy complications other than PE and GDM. The data in Figure 2H-2K was not updated in a timely manner. We have promptly updated this data and reanalyze it.

Comment 7. There is little to no evaluation of regulatory T cells (Tregs) which are well known to undergird maternal tolerance of the fetus, and which are well known to have overlapping developmental trajectory with RORgt+ Th17 cells. We recommend the authors evaluate whether the loss of Treg function, quantity, or quality leaves CD4+ effector T cells more unrestrained in their effect on PE phenotypes. References should include, accordingly: PMCID: PMC6448013 / DOI: 10.3389/fimmu.2019.00478; PMC4700932 / DOI: 10.1126/science.aaa9420.

Response 7: We thank the reviewers' comments. We have done the Treg-related animal experiment, which was not shown in this manuscript. We have added the Treg-related data in Figure 6F-6H. The injection of CD4⁺CD44⁺ T cells derived from RUPP mouse, characterized by a reduced frequency of Tregs, could induce PE-like symptoms in pregnant mice (Line297-304). Additionally, we have added a necessary discussion about Tregs and cited the literature you mentioned (Line433-439).

Comment 8. In discussing gMDSCs in Figure 3, the authors have missed key opportunities to evaluate bona fide Neutrophils. We recommend they conduct FACS or CyTOF staining including CD66b if they have additional tissues or cells available. Please refer to this helpful review article that highlights key points of distinguishing human MDSC from neutrophils: https://doi.org/10.1038/s41577-024-01062-0. This will both help the evaluation of potentially regulatory myeloid cells that may suppress effector T cells as well as aid in understanding at the end of the study if IL-17 produced by CD4+ Th17 cells might recruit neutrophils to the placenta and cause ROS immunopathology and fetal resorption.

Response 8: We thank the reviewers' comments. Although we do not have additional tissues or cells available to conduct FACS or CyTOF staining, including for CD66b, we have utilized CD15 and CD66b antibodies for immunofluorescence stain of placental tissue, and our findings revealed a pronounced increase in the proportion of neutrophils among PE patients, fostering the hypothesis that IL-17A produced by Th17 cells might orchestrate the migration of neutrophils towards the placental milieu (Figure 6-figure supplement 2F; Line 325-328). We have cited these references and discussed them in the Discussion section (Line 459-465).

Comment 9. Depletion of macrophages using several different methodologies (PLX3397, or clodronate liposomes) should be accompanied by supplementary data showing the efficiency of depletion, especially within tissue compartments of interest (uterine horns, placenta). The clodronate piece is not at all discussed in the main text. Both should be addressed in much more detail.

Response 9: We thank the reviewers' comments. We already have the additional data on the efficiency of macrophage depletion involving PLX3397 and clodronate liposomes, which were not present in this manuscript, and we'll add it to the Figure 4-figure supplement 2A,2B. The clodronate piece is mentioned in the main text (Line236-239), but only briefly described, because the results using clodronate we obtained were similar to those using PLX3397.

Comment 10. There are many heatmaps and tSNE / UMAP plots with unhelpful labels and no statistical tests applied. Many of these plots (e.g. Figure 7) could be moved to supplemental figures or pared down and combined with existing main figures to help the authors streamline and unify their message.

Response 10: We thank the reviewers' comments. We have moved the images of Figure 7 to the Figure 6-figure supplement 2. We also have moved most of the heatmaps to the supplementary materials.

Comment 11. There are claims that this study fills a gap that "only one report has provided an overall analysis of immune cells in the human placental villi in the presence and absence of spontaneous labor at term by scRNA-seq (Miller 2022)" (lines 362-364), yet this study itself does not exhaustively study all immune cell subsets...that's a monumental task, even with the two multi-omic methods used in this paper. There are several other datasets that have performed similar analyses and should be referenced.

Response 11: We thank the reviewers' comments. We have search for more literature and reference additional studies that have conducted similar analyses (Line382-393).

Comment 12. Inappropriate statistical tests are used in many of the analyses. Figures 1-2 use the Shapiro-Wilk test, which is a test of "goodness of fit", to compare unpaired groups. A Kruskal-Wallis or other nonparametric t-test is much more appropriate. In other instances, there is no mention of statistical tests (Figures 6-7) at all. Appropriate tests should be added throughout.

Response 12: We thank the reviewers' comments. As stated in the Statistical Analysis section (lines 672-676), the Kruskal-Wallis test was used to compare the results of experiments with multiple groups. Comparisons between the two groups in Figures 5 were conducted using Student's t-test. The aforementioned statistical methods have been included in the figure legends.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Overall, the study has several strengths, including the use of human samples and animal models, as well as the incorporation of multiple cutting-edge techniques. However, there are some significant issues with the murine model experiments that need to be addressed:

Comment 1. The authors are not consistent in their use of or focus on uterine and placental cells. These are distinct tissues, and numerous prior reports have indicated differences in the macrophage populations of these tissues, due in part to the predominantly maternal origin of macrophages in the uterus and the largely fetal origin of those in the placenta. The rationale for switching between uterine and placental cells in different experiments is not clear, and the inclusion of cells from both (such as in the bulk RNAseq experiments) could be potentially confounding.

Response 1: We thank the reviewers' comments. We have done the green fluorescent protein (GFP) pregnant mice-related animal experiment, which was not shown in this manuscript. The wild-type (WT) female mice were mated with either transgenic male mice, genetically modified to express GFP, or with WT male mice, in order to generate either GFP-expressing pups (GFP-pups) or their genetically unmodified counterparts (WT-pups), respectively. Mice were euthanized on day 18.5 of gestation, and the uteri of the pregnant females and the placentas of the offspring were analyzed using flow cytometry. The majority of macrophages in the uterus and placenta are of maternal origin, which was defined by GFP negative. In contrast, fetal-derived macrophages, distinguished by their expression of GFP, represent a mere fraction of the total macrophage population, signifying their inconsequential or restricted presence amidst the broader cellular landscape. We have added the GPF pregnant mice-related data in Figure 4-figure supplement 1D-1E to explain the different macrophage populations in the uterine and placental cells.

Comment 2. The observational data for the initial experiment transferring RUPP-derived macrophages to normal pregnant mice (without any other manipulations) seems to be missing. They do not seem to be presented in Figure 4 where they are expected based on the results text.

Response 2: We thank the reviewers' comments. We thank the reviewers' comments. We have added the observational data (Figure 4-figure supplement 1D, 1E） and a corresponding description of the data (Line 198-203).

Comment 3. The action of the anti-macrophage compounds is not well explained, nor are their mechanisms validated as affecting or not affecting the placental/fetal macrophage populations. It is important to clarify whether the macrophages are depleted or merely inhibited by these treatments, and it is absolutely critical to determine whether these treatments are affecting placental/fetal macrophage populations (the latter indicative of placental transfer), given the focus on placental macrophages.

Response 3: We thank the reviewers' comments. PLX3397, the inhibitor of CSF1R, which is needed for macrophage development (Nature. 2023, PMID: 36890231; Cell Mol Immunol. 2022, PMID: 36220994), we have stated that on Line227-230. However, PLX3397 is a small molecule compound that possesses the potential to cross the placental barrier and affect fetal macrophages. We will discuss the impact of this factor on the experiment in the Discussion section (Line457-459).

Comment 4. The interpretation of the murine single-cell data is hampered by the lack of means for distinguishing donor cells from recipient cells, which is important when seeking to identify the influence of the donor cells.

Response 4: We thank the reviewers' comments. Upon analysis, we observed a notable elevation in the frequency of total macrophages within the CD45⁺ cell population. Then we subsequently per formed macrophage clustering and uncovered a marked increase in the frequency of Cluster 0, implying a potential correlation between Cluster 0 and donor-derived cells. RNA sequencing revealed that the F480⁺CD206^- pro-inflammatory donor macrophages exhibited a Folr2⁺Ccl7⁺Ccl8⁺C1qa⁺C1qb⁺C1qc⁺ phenotype, which is consistent with the phenotype of cluster 0 in macrophages observed in single-cell RNA sequencing (Figure 4D and Figure 5E). Therefore, the donor cells should be in cluster 0 in macrophages.

Comment 5. The switch to the LPS model in the final experiments is a limitation, as this model more closely resembles the systemic inflammation seen in endotoxemia rather than the specific pathology of preeclampsia (PE). While this is not an exhaustive list, the number of weaknesses in the experimental design makes it difficult to evaluate the findings comprehensively.

Response 5: We thank the reviewers' comments. Firstly, our other animal experiments in this manuscript used the RUPP mouse model to simulate the pathology of PE. However, the RUPP model requires ligation of the uterine arteries in pregnant mice on day 12.5 of gestation, which hinders T cells returning from the tail vein from reaching the maternal-fetal interface. In addition, this experiment aims to prove that CD4⁺ T cells are differentiated into memory-like Th17 cells through IGF-1R receptor signaling to affect pregnancy by clearing CD4⁺ T cells in vivo with an anti-CD4 antibody followed by injecting IGF-1R inhibitor-treated CD4⁺ T cells. We proved that injection of RUPP-derived memory-like CD4⁺ T cells into pregnant rats induces PE-like symptoms (Figure 6F-6H). In summary, applying the LPS model in the final experiments does not affect the conclusions.

Minor comments:

Comment 1. Introduction, Lines 67-74: The phrasing here is unclear as to the roles that each mentioned immune cell subset is playing in preeclampsia. Given the statement "Elevated levels of maternal inflammation...", does this imply that the numbers of all mentioned immune cell subsets are increased in the maternal circulation? If not, please consider rewording this.

Response 1: We thank the reviewers' comments. We have revised the manuscript as follows: Currently, the pivotal mechanism underpinning the pathogenesis of preeclampsia is widely acknowledged to involve an increased frequency of pro-inflammatory M1-like maternal macrophages, along with an elevation in Granulocytes capable of superoxide generation, CD56⁺ CD94⁺ natural killer (NK) cells, CD19⁺CD5⁺ B1 lymphocytes, and activated γδ T cells. Conversely, this pathological process is accompanied by a notable decrease in the frequency of anti-inflammatory M2-like macrophages and NKp46⁺ NK cells (Line67-77).

Comment 2. Introduction, Lines 67-80: Is the involvement of the described immune cell subsets largely ubiquitous to preeclampsia? Recent multi-omic studies suggest that preeclampsia is a heterogeneous condition with different subsets, some more biased towards systemic immune activation than others. Thus, it is important to clarify whether the involvement of specific immune subsets is generally observed or more specific.

Response 2: We thank the reviewers' comments. We have added a new paragraph as follows: Moreover, as PE can be subdivided into early- and late-onset PE diagnosed before 34 weeks or from 34 weeks of gestation, respectively. Research has revealed that among the myriad of cellular alterations in PE, pro-inflammatory M1-like macrophages and intrauterine B1 cells display an augmented presence at the maternal-fetal interface of both early-onset and late-onset PE patients. Decidual natural killer (dNK) cells and neutrophils emerge as paramount contributors, playing a more crucial role in the pathogenesis of early-onset PE than late-onset PE (Front Immunol. 2020. PMID: 33013837) (Line83-89).

Comment 3. Introduction, Lines 81-86: The point of this short paragraph is not clear; the authors mention two very specific cellular interactions without explaining why.

Response 3: In the previous paragraph, we uncovered a heightened inflammatory response among multiple immune cells in patients with PE, yet the intricate interplay between these individual immune cells has been seldom elucidated in the context of PE patient. This is precisely why we delve into the realm of specific immune cellular interactions in relation to other pregnancy complications in this paragraph (Line91-98).

Comment 4. Methods: What placental tissues (e.g., villous tree, chorionic plate, extraplacental membranes) were included for CyTOF analysis? Was any decidual tissue (e.g., basal plate) included? Please clarify.

Response 4: Placental villi rather than chorionic plate and extraplacental membranes were used for CyToF in this study. The relevant content has been incorporated into the "Materials and Methods" section (Line564-576).

Comment 5. Results, Table 1: The authors should clarify that all PE samples were not full term (i.e., were less than 37 weeks of gestation), which is to be expected. In addition, were the PE cases all late-onset PE?

Response 5: All PE samples enumerated in Table 1 demonstrate a late-onset preeclampsia, with placental specimens being procured from patients more than 35 weeks of gestation and less than the 38 weeks of pregnancy. The relevant content has been incorporated into the "Materials and Methods" section (Line574-576).

Comment 6. Results, Figure 1: Are the authors considering the identified Macrophage cluster as being largely fetal (e.g., Hofbauer cells)? This also depends on whether any decidual tissue was included in the placental samples for CyTOF.

Response 6: Firstly, the specimens subjected to CyToF analysis were devoid of decidual tissue and exclusively comprised placental villi. Secondly, the Macrophage cluster in Figure 1 undeniably encompasses Hofbauer cells, and we considering fetal-derived macrophages likely constituting the substantial proportion of the cellular population. However, a limitation of the CyToF technique lies in its inability to discern between maternal and fetal origins of these cells, thereby precluding a definitive distinction.

Comment 7. Results, Figure 2C: Did the authors validate other T-cell subset markers (e.g., Th1, Th2, Th9, etc.)?

Response 7: In this study, we did not validate additional T-cell subset markers presented in Figure 2C, recognizing the potential for deeper insights. As we embark on our subsequent research endeavors, we aim to meticulously explore and characterize the intricate changes in diverse T-cell populations at the maternal-fetal interface, with a particular focus on preeclampsia patients, thereby advancing our understanding of this complex condition.

Comment 8. Results, Figure 2D: Where were the detected memory-like T cells located in the placenta? Did they cluster in certain areas or were they widely distributed?

Response 8: Upon a thorough re-evaluation of the immunofluorescence images specific to the placenta, we observed a notable preponderance of memory-like T cells residing within the placental sinusoids (Line135-139).

Comment 9. Results, Figure 2E: I would suggest separating the two plots so that the Y-axis can be expanded for TIM3, as it is impossible to view the medians currently.

Response 9: We thank the reviewers' comments. We have made the adjustment to Figure 2E according to the reviewers' suggestions.

Comment 10. Results, Lines 138-140: Do the authors consider that the altered T-cells are largely resident cells of the placenta or newly invading/recruited cells? The clarification of distribution within the placental tissues as mentioned above would help answer this.

Response 10: Our analysis revealed the presence of memory-like T cells within the placental sinusoids, as evident from the immunofluorescence examination of placental tissues. Consequently, these T cells may represent recently recruited cellular entities, traversing the placental vasculature and integrating into this unique maternal-fetal microenvironment (Line135-139).

Comment 11. Results, Figure 3C: Has a reduction of gMDSCs (or MDSCs in general) been previously reported in PE?

Response 11: Myeloid-derived suppressor cells (MDSCs) constitute a diverse population of myeloid-derived cells that exhibit immunosuppressive functions under various conditions. Previous reports have documented a decrease in the levels of gMDSCs from peripheral blood or umbilical cord blood among patients with preeclampsia (Am J Reprod Immunol. 2020, PMID: 32418253; J Reprod Immunol. 2018, PMID: 29763854; Biol Reprod. 2023, PMID: 36504233). Nevertheless, there was no documented reports thus far on the alterations and specific characteristics in gMDSCs within the placenta of PE patients.

Comment 12. Results, Figure 3D-E: It is not clear what new information is added by the correlations, as the increase of both cluster 23 in CD11b+ cells and cluster 8 in CD4+ T cells in PE cases was already apparent. Are these simply to confirm what was shown from the quantification data?

Response 12: Despite the evident increase in both cluster 23 within CD11b⁺ cells and cluster 8 within CD4⁺ T cells in PE cases, the existence of a potential correlation between these two clusters remains elusive. To gain insight into this question, we conducted a Pearson correlation analysis, which is presented in Figure 3D-E, revealing a positive correlation between the two clusters.

Comment 13. Results, Figure 4A: Please clarify in the results text that the RNA-seq of macrophages from RUPP mice was performed prior to their injection into normal pregnant mice.

Response 13: We thank the reviewers' comments. We have updated Figure 4A according to the reviewers' suggestions.

Comment 14. Results / Methods, Figure 4: For the transfer of macrophages from RUPP mice into normal mice, why were the uterine tissues included to isolate cells? The uterine macrophages will be almost completely maternal, as opposed to the largely fetal placental macrophages, and despite the sorting for specific markers these are likely distinct subsets that have been combined for injection. This could potentially impact the differential gene expression analysis and should be accounted for. In addition, did murine placental samples include decidua? This should be clarified.

Response 14: We thank the reviewers' comments. For our experimental design involving human samples, we meticulously selected placental tissue as the primary focus. Initially, we aimed for uniformity by contemplating the utilization of mouse placenta. However, a pivotal revelation emerged from the GFP pregnant mice-related data in Figure 4-figure supplement 1D,1E: the uterus and placenta of mice are predominantly populated by maternal macrophages, with fetal macrophages virtually absent, marking a notable divergence from the human scenario. Furthermore, the uterine milieu exhibits a macrophage concentration exceeding 20% of total cellular composition, whereas in the placenta, this proportion dwindles to less than 5%, underscoring a distinct distribution pattern. Given these discrepancies and considerations, we incorporated mouse uterine tissues into our protocol to isolate cells, ensuring a more comprehensive and informative exploration that acknowledges the inherent differences between human and mouse placental biology.

Comment 15. Results, Lines 186-187: I think the figure citation should be Figure 4D here.

Response 15: We thank the reviewers' careful checking. We have revised and updated Figure 4 accordingly.

Comment 16. Results, Figure 4: Where are the results of the injection of anti-inflammatory and pro-inflammatory macrophages into normal mice? This experiment is mentioned in Figure 4A, but the only results shown in Figure 4 are with the PLX3397 depletion.

Response 16: The aim of this experiment in figure 4 is to conclusively ascertain the influence of pro-inflammatory and anti-inflammatory macrophages on the other immune cells within the maternal-fetal interface, as well as their implications for pregnancy outcomes. To achieve this, we employed a strategic approach involving the administration of PLX3397, a compound capable of eliminating the preexisting macrophages in mice. Subsequently, anti-inflam or pro-inflam macrophages were injected to these mice, thereby eliminating the confounding influence of the native macrophage population. This methodology allows for a more discernible observation of the specific effects these two types of macrophages exert on the immune landscape at the maternal-fetal interface and their ultimate impact on pregnancy outcomes.

Comment 17. Results, Lines 189-190: Does PLX3397 inhibit macrophage development/signaling/etc. or result in macrophage depletion? This is an important distinction. If depletion is induced, does this affect placental/fetal macrophages or just maternal macrophages?

Response 17: We thank the reviewers' comments. We have updated the additional data on the efficiency of macrophage depletion involving PLX3397 in Figure 4-figure supplement 2A. PLX3397 is a small molecule compound that possesses the potential to cross the placental barrier and affect fetal macrophages. We have discussed the impact of this factor on the experiment in the Discussion section (Line457-459).

Comment 18. Results, Lines 197-198: Similarly, does clodronate liposome administration affect only maternal macrophages, or also placental/fetal macrophages?

Response 18: We thank the reviewers' comments. We have updated the additional data on the efficiency of macrophage depletion involving Clodronate Liposomes in Figure 4-figure supplement 2B. Clodronate Liposomes, which are intricate vesicles encapsulating diverse substances, while only small molecule compounds possess the potential to cross the placental barrier. Consequently, we hold the view that the influence of these liposomes is likely confined to the maternal macrophages (Artif Cells Nanomed Biotechnol. 2023. PMID: 37594208).  

Comment 19. Results, Line 206: A minor point, but consider continuing to refer to the preeclampsia model mice as RUPP mice rather than PE mice.

Response 19: We thank the reviewers' comments. We have revised and updated this section accordingly.

Comment 20. Results / Methods, Figure 5: For these experiments, why did the authors focus on the mouse uterus?

Response 20: We have previously addressed this query in our Response 14. We incorporated mouse uterine tissues for cell isolation due to the profound differences in placental biology between humans and mice.

Comment 21. Results, Figure 5: Did the authors have a means of distinguishing the transferred donor cells from the recipient cells for their single-cell analysis? If the goal is to separate the effects of the macrophage transfer on other uterine immune cells, then it would be important to identify and separate the donor cells.

Response 21: We thank the reviewers' comments. Upon analysis, we observed a notable elevation in the frequency of total macrophages within the CD45⁺ cell population. Then we subsequently performed macrophage clustering and uncovered a marked increase in the frequency of Cluster 0, implying a potential correlation between Cluster 0 and donor-derived cells. RNA sequencing revealed that the F480⁺CD206^- pro-inflammatory donor macrophages exhibited a Folr2⁺Ccl7⁺Ccl8⁺C1qa⁺C1qb⁺C1qc⁺ phenotype, which is consistent with the phenotype of cluster 0 in macrophages observed in single-cell RNA sequencing (Figure 4D and Figure 5E). Therefore, the donor cells should be in cluster 0 in macrophages.

Comment 22. Results, Lines 247-248: While the authors have prudently noted that the observed T-cell phenotypes are merely suggestive of immunosuppression, any claims regarding changes in the immunosuppressive function after macrophage transfer would require functional studies of the T cells.

Response 22: We thank the reviewers' comments. Upon revisiting and meticulously reviewing the pertinent literature, we have refined our terminology, transitioning from 'immunosuppression' to 'immunomodulation', thereby enhancing the accuracy and precision of our Results (Line285-287).

Comment 23. Results, Figure 6G: The observation of worsened outcomes and PE-like symptoms after T-cell transfer is interesting, but other models of PE induced by the administration of Th1-like cells have already been reported. Are the authors' findings consistent with these reports? These findings are strengthened by the evaluation of second-pregnancy outcomes following the transfer of T cells in the first pregnancy.

Response 23: We thank the reviewers' comments. As we verified in Figure 6F-6H, the injection of CD4⁺CD44⁺ T cells derived from RUPP mouse, characterized by a reduced frequency of Tregs and an increased frequency of Th17 cells, could induce PE-like symptoms in pregnant mice. In line with other studies, which have implicated Th1-like cells in the manifestation of PE-like symptoms, we posit a novel hypothesis: beyond Th1 cells, Th17 cells also have the potential to induce PE-like symptoms.

Comment 24. Results, Lines 327-337: The disease model implied by the authors here is not clear. Given that the authors' human findings are in the placental macrophages, are the authors proposing that placental macrophages are induced to an M1 phenotype by placenta-derived EVs? Please elaborate on and clarify the proposed model.

Response 24 In the article authored by our team, titled "Trophoblast-Derived Extracellular Vesicles Promote Preeclampsia by Regulating Macrophage Polarization" published in Hypertension (Hypertension. 2022, PMID: 35993233), we employed trophoblast-derived extracellular vesicles isolated from PE patients as a means to induce an M1-like macrophage phenotype in macrophages from human peripheral blood in vitro. Consequently, in the present study, we have directly leveraged this established methodology to induce pro-inflammatory macrophages.

Comment 25. Results / Methods, Figure 8E-H: What is the reasoning for switching to an LPS model in this experiment? LPS is less specific to PE than the RUPP model.

Response 25: We thank the reviewers' comments. Firstly, our other animal experiments in this manuscript used the RUPP mouse model to simulate the pathology of PE. However, the RUPP model requires ligation of the uterine arteries in pregnant mice on day 12.5 of gestation, which hinders T cells returning from the tail vein from reaching the maternal-fetal interface. In addition, this experiment aims to prove that CD4⁺ T cells are differentiated into memory-like Th17 cells through IGF-1R receptor signaling to affect pregnancy by clearing CD4⁺ T cells in vivo with an anti-CD4 antibody followed by injecting IGF-1R inhibitor-treated CD4⁺ T cells. And we proved that injection of RUPP-derived memory-like CD4⁺ T cells into pregnant mice induces PE-like symptoms (Figure 6). In summary, the application of the LPS model in the final experiments does not affect the conclusions.

Comment 26. Discussion: What do the authors consider to be the origins of the inflammatory cells associated with PE onset? Are these maternal cells invading the placental tissues, or are these placental resident (likely fetal) cells?

Response 26: We thank the reviewers' comments. Numerous reports have consistently observed the presence of inflammatory cells and factors in the maternal peripheral blood and placenta tissues of PE patients, fostering the prevailing notion that the progression of PE is intricately linked to the maternal immune system's inflammatory response towards the fetus. Nevertheless, intriguing findings from single-cell RNA sequencing, analyzed through bioinformatic methods, have challenged this perspective (Elife. 2019. PMID: 31829938；Proc Natl Acad Sci U S A. 2017.PMID: 28830992). These studies reveal that the placenta harbors not just immune cells of maternal origin but also those of fetal origin, raising questions about whether these are maternal cells infiltrating placental tissues or resident (possibly fetal) placental cells. Further investigation is imperative to elucidate this complex interplay.

Comment 27. Discussion: Given the observed lack of changes in the GDM or GDM+PE groups, do the authors consider that GDM represents a distinct pathology that can lead to secondary PE, and thus is different from primary PE without GDM?

Response 27: It's possible. Though previous studies reported GDM is associated with aberrant maternal immune cell adaption the findings remained controversial. It seems that GDM does not induce significant alterations in placental immune cell profile in our study, which made us pay more attention to the immune mechanism in PE. However, it is confusing for the reasons why individuals with GDM&PE were protected from the immune alterations at the maternal fetal interface. Limited placental samples in the GDM&PE group can partly explain it, for it is hard to collect clean samples excluding confounding factors. A study reported that macrophages in human placenta maintained anti-inflammatory properties despite GDM (Front Immunol, 2017, PMID: 28824621).Barke et al. also found that more CD163⁺ cells were observed in GDM placentas compared to normal controls (PLoS One, 2014, PMID: 24983948). Thus, GDM is likely to have a protective property in the placental immune environment when the individuals are complicated with PE.

Reviewer #2 (Recommendations for the authors):

Comment 1. IF images need to be quantified.

Response 1: We thank the reviewers' comments. We have quantified and calculated the fluorescence intensity and added it in Figure 2D.

Comment 2. Cluster 12 in Figure 3 is labeled as granulocytes but listed under macrophages.

Response 2: We thank the reviewers' careful checking. We have revised and updated Figure 3A.

Comment 3. Figure 4 labels in the text and figure do not match, no 4G in the figure.

Response 3: We thank the reviewers' careful checking. The figure labels of Figure 4 have been revised and updated.

eLife Assessment

This study makes the important claims that people track, specifically, the elasticity of control (rather than the more general parameter of controllability) and that control elasticity is specifically impaired in certain types of psychopathology. These claims will have implications for the fields of computational psychiatry and computational cognitive neuroscience. However the evidence for the claim that people infer control elasticity is incomplete, given that it is not clear that the task allows the elasticity construct to be distinguished from more general learning processes, the chosen models aren't well justified, and it is unclear that the findings generalize to tasks that aren't biased to find overestimates of elasticity. Moreover, the claim about psychopathology relies on an invalid interpretation of CCA; a more straightforward analysis of the correlation between the model parameters and the psychopathology measures would provide stronger evidence.

Reviewer #1 (Public review):

Summary:

The authors investigated the elasticity of controllability by developing a task that manipulates the probability of achieving a goal with a baseline investment (which they refer to as inelastic controllability) and the probability that additional investment would increase the probability of achieving a goal (which they refer to as elastic controllability). They found that a computational model representing the controllability and elasticity of the environment accounted better for the data than a model representing only the controllability. They also found that prior biases about the controllability and elasticity of the environment were associated with a composite psychopathology score. The authors conclude that elasticity inference and bias guide resource allocation.

Strengths:

This research takes a novel theoretical and methodological approach to understanding how people estimate the level of control they have over their environment, and how they adjust their actions accordingly. The task is innovative and both it and the findings are well-described (with excellent visuals). They also offer thorough validation for the particular model they develop. The research has the potential to theoretically inform the understanding of control across domains, which is a topic of great importance.

Weaknesses:

An overarching concern is that this paper is framed as addressing resource investments across domains that include time, money, and effort, and the introductory examples focus heavily on effort-based resources (e.g., exercising, studying, practicing). The experiments, though, focus entirely on the equivalent of monetary resources - participants make discrete actions based on the number of points they want to use on a given turn. While the same ideas might generalize to decisions about other kinds of resources (e.g., if participants were having to invest the effort to reach a goal), this seems like the kind of speculation that would be better reserved for the Discussion section rather than using effort investment as a means of introducing a new concept (elasticity of control) that the paper will go on to test.

Setting aside the framing of the core concepts, my understanding of the task is that it effectively captures people's estimates of the likelihood of achieving their goal (Pr(success)) conditional on a given investment of resources. The ground truth across the different environments varies such that this function is sometimes flat (low controllability), sometimes increases linearly (elastic controllability), and sometimes increases as a step function (inelastic controllability). If this is accurate, then it raises two questions.

First, on the modeling front, I wonder if a suitable alternative to the current model would be to assume that the participants are simply considering different continuous functions like these and, within a Bayesian framework, evaluating the probabilistic evidence for each function based on each trial's outcome. This would give participants an estimate of the marginal increase in Pr(success) for each ticket, and they could then weigh the expected value of that ticket choice (Pr(success)*150 points) against the marginal increase in point cost for each ticket. This should yield similar predictions for optimal performance (e.g., opt-out for lower controllability environments, i.e., flatter functions), and the continuous nature of this form of function approximation also has the benefit of enabling tests of generalization to predict changes in behavior if there was, for instance, changes in available tickets for purchase (e.g., up to 4 or 5) or changes in ticket prices. Such a model would of course also maintain a critical role for priors based on one's experience within the task as well as over longer timescales, and could be meaningfully interpreted as such (e.g., priors related to the likelihood of success/failure and whether one's actions influence these). It could also potentially reduce the complexity of the model by replacing controllability-specific parameters with multiple candidate functions (presumably learned through past experience, and/or tuned by experience in this task environment), each of which is being updated simultaneously.

Second, if the reframing above is apt (regardless of the best model for implementing it), it seems like the taxonomy being offered by the authors risks a form of "jangle fallacy," in particular by positing distinct constructs (controllability and elasticity) for processes that ultimately comprise aspects of the same process (estimation of the relationship between investment and outcome likelihood). Which of these two frames is used doesn't bear on the rigor of the approach or the strength of the findings, but it does bear on how readers will digest and draw inferences from this work. It is ultimately up to the authors which of these they choose to favor, but I think the paper would benefit from some discussion of a common-process alternative, at least to prevent too strong of inferences about separate processes/modes that may not exist. I personally think the approach and findings in this paper would also be easier to digest under a common-construct approach rather than forcing new terminology but, again, I defer to the authors on this.

Reviewer #2 (Public review):

Summary:

In this paper, the authors test whether controllability beliefs and associated actions/resource allocation are modulated by things like time, effort, and monetary costs (what they call "elastic" as opposed to "inelastic" controllability). Using a novel behavioral task and computational modeling, they find that participants do indeed modulate their resources depending on whether they are in an "elastic," "inelastic," or "low controllability" environment. The authors also find evidence that psychopathology is related to specific biases in controllability.

Strengths:

This research investigates how people might value different factors that contribute to controllability in a creative and thorough way. The authors use computational modeling to try to dissociate "elasticity" from "overall controllability," and find some differential associations with psychopathology. This was a convincing justification for using modeling above and beyond behavioral output and yielded interesting results. Interestingly, the authors conclude that these findings suggest that biased elasticity could distort agency beliefs via maladaptive resource allocation. Overall, this paper reveals some important findings about how people consider components of controllability.

Weaknesses:

The primary weakness of this research is that it is not entirely clear what is meant by "elastic" and "inelastic" and how these constructs differ from existing considerations of various factors/calculations that contribute to perceptions of and decisions about controllability. I think this weakness is primarily an issue of framing, where it's not clear whether elasticity is, in fact, theoretically dissociable from controllability. Instead, it seems that the elements that make up "elasticity" are simply some of the many calculations that contribute to controllability. In other words, an "elastic" environment is inherently more controllable than an "inelastic" one, since both environments might have the same level of predictability, but in an "elastic" environment, one can also partake in additional actions to have additional control over achieving the goal (i.e., expend effort, money, time).

Reviewer #3 (Public review):

A bias in how people infer the amount of control they have over their environment is widely believed to be a key component of several mental illnesses including depression, anxiety, and addiction. Accordingly, this bias has been a major focus in computational models of those disorders. However, all of these models treat control as a unidimensional property, roughly, how strongly outcomes depend on action. This paper proposes---correctly, I think---that the intuitive notion of "control" captures multiple dimensions in the relationship between action and outcome is multi-dimensional. In particular, the authors propose that the degree to which outcome depends on how much *effort* we exert, calling this dimension the "elasticity of control". They additionally propose that this dimension (rather than the more holistic notion of controllability) may be specifically impaired in certain types of psychopathology. This idea thus has the potential to change how we think about mental disorders in a substantial way, and could even help us better understand how healthy people navigate challenging decision-making problems.

Unfortunately, my view is that neither the theoretical nor empirical aspects of the paper really deliver on that promise. In particular, most (perhaps all) of the interesting claims in the paper have weak empirical support.

Starting with theory, the elasticity idea does not truly "extend" the standard control model in the way the authors suggest. The reason is that effort is simply one dimension of action. Thus, the proposed model ultimately grounds out in how strongly our outcomes depend on our actions (as in the standard model). Contrary to the authors' claims, the elasticity of control is still a fixed property of the environment. Consistent with this, the computational model proposed here is a learning model of this fixed environmental property. The idea is still valuable, however, because it identifies a key dimension of action (namely, effort) that is particularly relevant to the notion of perceived control. Expressing the elasticity idea in this way might support a more general theoretical formulation of the idea that could be applied in other contexts. See Huys & Dayan (2009), Zorowitz, Momennejad, & Daw (2018), and Gagne & Dayan (2022) for examples of generalizable formulations of perceived control.

Turning to experiment, the authors make two key claims: (1) people infer the elasticity of control, and (2) individual differences in how people make this inference are importantly related to psychopathology.

Starting with claim 1, there are three sub-claims here; implicitly, the authors make all three. (1A) People's behavior is sensitive to differences in elasticity, (1B) people actually represent/track something like elasticity, and (1C) people do so naturally as they go about their daily lives. The results clearly support 1A. However, 1B and 1C are not supported.

Starting with 1B, the experiment cannot support the claim that people represent or track elasticity because the effort is the only dimension over which participants can engage in any meaningful decision-making (the other dimension, selecting which destination to visit, simply amounts to selecting the location where you were just told the treasure lies). Thus, any adaptive behavior will necessarily come out in a sensitivity to how outcomes depend on effort. More concretely, any model that captures the fact that you are more likely to succeed in two attempts than one will produce the observed behavior. The null models do not make this basic assumption and thus do not provide a useful comparison.

For 1C, the claim that people infer elasticity outside of the experimental task cannot be supported because the authors explicitly tell people about the two notions of control as part of the training phase: "To reinforce participants' understanding of how elasticity and controllability were manifested in each planet, [participants] were informed of the planet type they had visited after every 15 trips." (line 384).

Finally, I turn to claim 2, that individual differences in how people infer elasticity are importantly related to psychopathology. There is much to say about the decision to treat psychopathology as a unidimensional construct. However, I will keep it concrete and simply note that CCA (by design) obscures the relationship between any two variables. Thus, as suggestive as Figure 6B is, we cannot conclude that there is a strong relationship between Sense of Agency and the elasticity bias---this result is consistent with any possible relationship (even a negative one). The fact that the direct relationship between these two variables is not shown or reported leads me to infer that they do not have a significant or strong relationship in the data.

There is also a feature of the task that limits our ability to draw strong conclusions about individual differences in elasticity inference. As the authors clearly acknowledge, the task was designed "to be especially sensitive to overestimation of elasticity" (line 287). A straightforward consequence of this is that the resulting *empirical* estimate of estimation bias (i.e., the gamma_elasticity parameter) is itself biased. This immediately undermines any claim that references the directionality of the elasticity bias (e.g. in the abstract). Concretely, an undirected deficit such as slower learning of elasticity would appear as a directed overestimation bias.

When we further consider that elasticity inference is the only meaningful learning/decision-making problem in the task (argued above), the situation becomes much worse. Many general deficits in learning or decision-making would be captured by the elasticity bias parameter. Thus, a conservative interpretation of the results is simply that psychopathology is associated with impaired learning and decision-making.

Minor comments:

Showing that a model parameter correlates with the data it was fit to does not provide any new information, and cannot support claims like "a prior assumption that control is likely available was reflected in a futile investment of resources in uncontrollable environments." To make that claim, one must collect independent measures of the assumption and the investment.

Did participants always make two attempts when purchasing tickets? This seems to violate the intuitive model, in which you would sometimes succeed on the first jump. If so, why was this choice made? Relatedly, it is not clear to me after a close reading how the outcome of each trial was actually determined.

It should be noted that the model is heuristically defined and does not reflect Bayesian updating. In particular, it overestimates control by not using losses with less than 3 tickets (intuitively, the inference here depends on your beliefs about elasticity). I wonder if the forced three-ticket trials in the task might be historically related to this modeling choice.

Author response:

We thank the reviewers for their thorough reading and thoughtful feedback. Below, we provisionally address each of the concerns raised in the public reviews, and outline our planned revision that aims to further clarify and strengthen the manuscript.

In our response, we clarify our conceptualization of elasticity as a dimension of controllability, formalizing it within an information-theoretic framework, and demonstrating that controllability and its elasticity are partially dissociable. Furthermore, we provide clarifications and additional modeling results showing that our experimental design and modeling approach are well-suited to dissociating elasticity inference from more general learning processes, and are not inherently biased to find overestimates of elasticity. Finally, we clarify the advantages and disadvantages of our canonical correlation analysis (CCA) approach for identifying latent relationships between multidimensional data sets, and provide additional analyses that strengthen the link between elasticity estimation biases and a specific psychopathology profile.

Reviewer 1:

This research takes a novel theoretical and methodological approach to understanding how people estimate the level of control they have over their environment, and how they adjust their actions accordingly. The task is innovative and both it and the findings are well-described (with excellent visuals). They also offer thorough validation for the particular model they develop. The research has the potential to theoretically inform the understanding of control across domains, which is a topic of great importance.

We thank the reviewer for their favorable appraisal and valuable suggestions, which have helped clarify and strengthen the study’s conclusion. 

An overarching concern is that this paper is framed as addressing resource investments across domains that include time, money, and effort, and the introductory examples focus heavily on effort-based resources (e.g., exercising, studying, practicing). The experiments, though, focus entirely on the equivalent of monetary resources - participants make discrete actions based on the number of points they want to use on a given turn. While the same ideas might generalize to decisions about other kinds of resources (e.g., if participants were having to invest the effort to reach a goal), this seems like the kind of speculation that would be better reserved for the Discussion section rather than using effort investment as a means of introducing a new concept (elasticity of control) that the paper will go on to test.

We thank the reviewer for pointing out a lack of clarity regarding the kinds of resources tested in the present experiment. Investing additional resources in the form of extra tickets did not only require participants to pay more money. It also required them to invest additional time – since each additional ticket meant making another attempt to board the vehicle, extending the duration of the trial, and attentional effort – since every attempt required precisely timing a spacebar press as the vehicle crossed the screen. Given this involvement of money, time, and effort resources, we believe it would be imprecise to present the study as concerning monetary resources in particular. That said, we agree with the Reviewer that results might differ depending on the resource type that the experiment or the participant considers most. Thus, in our revision of the manuscript, we will make sure to clarify the kinds of resources the experiment involved, and highlight the open question of whether inferences concerning the elasticity of control generalize across different resource domains.

Setting aside the framing of the core concepts, my understanding of the task is that it effectively captures people's estimates of the likelihood of achieving their goal (Pr(success)) conditional on a given investment of resources. The ground truth across the different environments varies such that this function is sometimes flat (low controllability), sometimes increases linearly (elastic controllability), and sometimes increases as a step function (inelastic controllability). If this is accurate, then it raises two questions.

First, on the modeling front, I wonder if a suitable alternative to the current model would be to assume that the participants are simply considering different continuous functions like these and, within a Bayesian framework, evaluating the probabilistic evidence for each function based on each trial's outcome. This would give participants an estimate of the marginal increase in Pr(success) for each ticket, and they could then weigh the expected value of that ticket choice (Pr(success)*150 points) against the marginal increase in point cost for each ticket. This should yield similar predictions for optimal performance (e.g., opt-out for lower controllability environments, i.e., flatter functions), and the continuous nature of this form of function approximation also has the benefit of enabling tests of generalization to predict changes in behavior if there was, for instance, changes in available tickets for purchase (e.g., up to 4 or 5) or changes in ticket prices. Such a model would of course also maintain a critical role for priors based on one's experience within the task as well as over longer timescales, and could be meaningfully interpreted as such (e.g., priors related to the likelihood of success/failure and whether one's actions influence these). It could also potentially reduce the complexity of the model by replacing controllability-specific parameters with multiple candidate functions (presumably learned through past experience, and/or tuned by experience in this task environment), each of which is being updated simultaneously.

Second, if the reframing above is apt (regardless of the best model for implementing it), it seems like the taxonomy being offered by the authors risks a form of "jangle fallacy," in particular by positing distinct constructs (controllability and elasticity) for processes that ultimately comprise aspects of the same process (estimation of the relationship between investment and outcome likelihood). Which of these two frames is used doesn't bear on the rigor of the approach or the strength of the findings, but it does bear on how readers will digest and draw inferences from this work. It is ultimately up to the authors which of these they choose to favor, but I think the paper would benefit from some discussion of a common-process alternative, at least to prevent too strong of inferences about separate processes/modes that may not exist. I personally think the approach and findings in this paper would also be easier to digest under a common-construct approach rather than forcing new terminology but, again, I defer to the authors on this.

We thank the reviewer for suggesting this interesting alternative modeling approach. We agree that a Bayesian framework evaluating different continuous functions could offer advantages, particularly in its ability to generalize to other ticket quantities and prices. We will attempt to implement this as an alternative model and compare it with the current model.  

We also acknowledge the importance of avoiding a potential "jangle fallacy". We entirely agree with the Reviewer that elasticity and controllability inferences are not distinct processes. Specifically, we view resource elasticity as a dimension of controllability, hence the name of our ‘elastic controllability’ model. In response to this and other Reviewers’ comments, we now offer a formal definition of elasticity as the reduction in uncertainty about controllability due to knowing the amount of resources the agent is able and willing to invest (see further details in response to Reviewer 3 below).  

With respect to how this conceptualization is expressed in the modelling, we note that the representation in our model of maximum controllability and its elasticity via different variables is analogous to how a distribution may be represented by separate mean and variance parameters. Ultimately, even in the model suggested by the Reviewer, there would need to be a dedicated variable representing elasticity, such as the probability of sloped controllability functions. A single-process account thus allows that different aspects of this process would be differently biased (e.g., one can have an accurate estimate of the mean of a distribution but overestimate its variance). Therefore, our characterization of distinct elasticity and controllability biases (or to put it more accurately, ‘elasticity of controllability bias’ and ‘maximum controllability bias’) is consistent with a common construct account. 

That said, given the Reviewer’s comments, we believe that some of the terminology we used may have been misleading. In our planned revision, we will modify the text to clarify that we view elasticity as a dimension of controllability that can only be estimated in conjunction with controllability. 

Reviewer 2:

This research investigates how people might value different factors that contribute to controllability in a creative and thorough way. The authors use computational modeling to try to dissociate "elasticity" from "overall controllability," and find some differential associations with psychopathology. This was a convincing justification for using modeling above and beyond behavioral output and yielded interesting results. Interestingly, the authors conclude that these findings suggest that biased elasticity could distort agency beliefs via maladaptive resource allocation. Overall, this paper reveals some important findings about how people consider components of controllability.

We appreciate the Reviewer's positive assessment of our findings and computational approach to dissociating elasticity and overall controllability.

The primary weakness of this research is that it is not entirely clear what is meant by "elastic" and "inelastic" and how these constructs differ from existing considerations of various factors/calculations that contribute to perceptions of and decisions about controllability. I think this weakness is primarily an issue of framing, where it's not clear whether elasticity is, in fact, theoretically dissociable from controllability. Instead, it seems that the elements that make up "elasticity" are simply some of the many calculations that contribute to controllability. In other words, an "elastic" environment is inherently more controllable than an "inelastic" one, since both environments might have the same level of predictability, but in an "elastic" environment, one can also partake in additional actions to have additional control overachieving the goal (i.e., expend effort, money, time).

We thank the reviewer for highlighting the lack of clarity in our concept of elasticity. We first clarify that elasticity cannot be entirely dissociated from controllability because it is a dimension of controllability. If no controllability is afforded, then there cannot be elasticity or inelasticity. This is why in describing the experimental environments, we only label high-controllability, but not low-controllability, environments as ‘elastic’ or ‘inelastic’. For further details on this conceptualization of elasticity, and a planned revision of the text, see our response above to Reviewer 1. 

Second, we now clarify that controllability can also be computed without knowing the amount of resources the agent is able and willing to invest, for instance by assuming infinite resources available or a particular distribution of resource availabilities. However, knowing the agent’s available resources often reduces uncertainty concerning controllability. This reduction in uncertainty is what we define as elasticity. Since any action requires some resources, this means that no controllable environment is entirely inelastic if we also consider agents that do not have enough resources to commit any action. However, even in this case environments can differ in the degree to which they are elastic. For further details on this formal definition, see our response to Reviewer 3 below. We will make these necessary clarifications in the revised manuscript. 

Importantly, whether an environment is more or less elastic does not determine whether it is more or less controllable. In particular, environments can be more controllable yet less elastic. This is true even if we allow that investing different levels of resources (i.e., purchasing 0, 1, 2, or 3 tickets) constitute different actions, in conjunction with participants’ vehicle choices. Below, we show this using two existing definitions of controllability. 

Definition 1, reward-based controllability¹: If control is defined as the fraction of available reward that is controllably achievable, and we assume all participants are in principle willing and able to invest 3 tickets, controllability can be computed in the present task as:

where P(S' \= goal ∣ 𝑆, 𝐴, 𝐶 ) is the probability of reaching the treasure from present state 𝑆 when taking action A and investing C resources in executing the action. In any of the task environments, the probability of reaching the goal is maximized by purchasing 3 tickets (𝐶 = 3) and choosing the vehicle that leads to the goal (𝐴 = correct vehicle). Conversely, the probability of reaching the goal is minimized by purchasing 3 tickets (𝐶 = 3) and choosing the vehicle that does not lead to the goal (𝐴 = wrong vehicle). This calculation is thus entirely independent of elasticity, since it only considers what would be achieved by maximal resource investment, whereas elasticity consists of the reduction in controllability that would arise if the maximal available 𝐶 is reduced. Consequently, any environment where the maximum available control is higher yet varies less with resource investment would be more controllable and less elastic. 

Note that if we also account for ticket costs in calculating reward, this will only reduce the fraction of achievable reward and thus the calculated control in elastic environments.   

Definition 2, information-theoretic controllability²: Here controllability is defined as the reduction in outcome entropy due to knowing which action is taken:

I(S'; A, C | S) = H(S'|S) - H(S'|S, A, C)

where H(S'|S) is the conditional entropy of the distribution of outcomes S' given the present state 𝑆, and H(S'|S, A, C) is the conditional entropy of the outcome given the present state, action, and resource investment. 

To compare controllability, we consider two environments with the same maximum control:

• Inelastic environment: If the correct vehicle is chosen, there is a 100% chance of reaching the goal state with 1, 2, or 3 tickets. Thus, out of 7 possible action-resource investment combinations, three deterministically lead to the goal state (≥1 tickets and correct vehicle choice), three never lead to it (≥1 tickets and wrong vehicle choice), and one (0 tickets) leads to it 20% of the time (since walking leads to the treasure on 20% of trials).

• Elastic Environment: If the correct vehicle is chosen, the probability of boarding it is 0% with 1 ticket, 50% with 2 tickets, and 100% with 3 tickets. Thus, out of 7 possible actionresource investment combinations, one deterministically leads to the goal state (3 tickets and correct vehicle choice), one never leads to it (3 tickets and wrong vehicle choice), one leads to it 60% of the time (2 tickets and correct vehicle choice: 50% boarding + 50% × 20% when failing to board), one leads to it 10% of time (2 ticket and wrong vehicle choice), and three lead to it 20% of time (0-1 tickets).

Here we assume a uniform prior over actions, which renders the information-theoretic definition of controllability equal to another definition termed ‘instrumental divergence’3,4. We note that changing the uniform prior assumption would change the results for the two environments, but that would not change the general conclusion that there can be environments that are more controllable yet less elastic. 

Step 1: Calculating H(S'|S)

For the inelastic environment:

P(goal) = (3 × 100% + 3 × 0% + 1 × 20%)/7 = .46, P(non-goal) = .54  H(S'|S) = – [.46 × log₂(.46) + .54 × log₂(.54)] \= 1 bit

For the elastic environment:

P(goal) \= (1 × 100% + 1 × 0% + 1 × 60% + 1 × 10% + 3 × 20%)/7 \= .33, P(non-goal) \= .67  H(S'|S) = – [.33 × log₂(.33) + .67 × log₂(.67)] \= .91 bits

Step 2: Calculating H(S'|S, A, C)

Inelastic environment: Six action-resource investment combinations have deterministic outcomes entailing zero entropy, whereas investing 0 tickets has a probabilistic outcome (20%). The entropy for 0 tickets is: H(S'|C \= 0) \= -[.2 × log₂(.2) + 0.8 × log₂ (.8)] = .72 bits. Since this actionresource investment combination is chosen with probability 1/7, the total conditional entropy is approximately .10 bits

Elastic environment: 2 actions have deterministic outcomes (3 tickets with correct/wrong vehicle), whereas the other 5 actions have probabilistic outcomes:

2 tickets and correct vehicle (60% success): 

H(S'|A = correct, C = 2) = – [.6 × log₂(.6) + .4 × log₂(.4)] \= .97 bits 2 tickets and wrong vehicle (10% success): 

H(S'|A = wrong, C = 2) = – [.1 × ₂(.1) + .9 × ₂(.9)] \= .47 bits 0-1 tickets (20% success):

H(S'|C = 0-1) = – [.2 × ₂(.2) + .8 × ₂ .8)] \= .72 bits

Thus the total conditional entropy of the elastic environment is: H(S'|S, A, C) = (1/7) × .97 + (1/7) × .47 + (3/7) × .72 \= .52 bits

Step 3: Calculating I(S' | A, S)  

Inelastic environment: I(S'; A, C | S) = H(S'|S) – H(S'|S, A, C) = 1 – 0.1 = .9 bits 

Elastic environment: I(S'; A, C | S) = H(S'|S) – H(S'|S, A, C) = .91 – .52 = .39 bits

Thus, the inelastic environment offers higher information-theoretic controllability (.9 bits) compared to the elastic environment (.39 bits). 

Of note, even if each combination of cost and goal reaching is defined as a distinct outcome, then information-theoretic controllability is higher for the inelastic (2.81 bits) than for the elastic (2.30 bits) environment. 

In sum, for both definitions of controllability, we see that environments can be more elastic yet less controllable. We will amend the manuscript to clarify this distinction between controllability and its elasticity.

Reviewer 3:

A bias in how people infer the amount of control they have over their environment is widely believed to be a key component of several mental illnesses including depression, anxiety, and addiction. Accordingly, this bias has been a major focus in computational models of those disorders. However, all of these models treat control as a unidimensional property, roughly, how strongly outcomes depend on action. This paper proposes---correctly, I think---that the intuitive notion of "control" captures multiple dimensions in the relationship between action and outcome is multi-dimensional. In particular, the authors propose that the degree to which outcome depends on how much *effort* we exert, calling this dimension the "elasticity of control". They additionally propose that this dimension (rather than the more holistic notion of controllability) may be specifically impaired in certain types of psychopathology. This idea thus has the potential to change how we think about mental disorders in a substantial way, and could even help us better understand how healthy people navigate challenging decision-making problems.

Unfortunately, my view is that neither the theoretical nor empirical aspects of the paper really deliver on that promise. In particular, most (perhaps all) of the interesting claims in the paper have weak empirical support.

We appreciate the Reviewer's thoughtful engagement with our research and recognition of the potential significance of distinguishing between different dimensions of control in understanding psychopathology. We believe that all the Reviewer’s comments can be addressed with clarifications or additional analyses, as detailed below.  

Starting with theory, the elasticity idea does not truly "extend" the standard control model in the way the authors suggest. The reason is that effort is simply one dimension of action. Thus, the proposed model ultimately grounds out in how strongly our outcomes depend on our actions (as in the standard model). Contrary to the authors' claims, the elasticity of control is still a fixed property of the environment. Consistent with this, the computational model proposed here is a learning model of this fixed environmental property. The idea is still valuable, however, because it identifies a key dimension of action (namely, effort) that is particularly relevant to the notion of perceived control. Expressing the elasticity idea in this way might support a more general theoretical formulation of the idea that could be applied in other contexts. See Huys & Dayan (2009), Zorowitz, Momennejad, & Daw (2018), and Gagne & Dayan (2022) for examples of generalizable formulations of perceived control.

We thank the Reviewer for the suggestion that we formalize our concept of elasticity to resource investment, which we agree is a dimension of action. We first note that we have not argued against the claim that elasticity is a fixed property of the environment. We surmise the Reviewer might have misread our statement that “controllability is not a fixed property of the environment”. The latter statement is motivated by the observation that controllability is often higher for agents that can invest more resources (e.g., a richer person can buy more things). We will clarify this in our revision of the manuscript.

To formalize elasticity, we build on Huys & Dayan’s definition of controllability(1) as the fraction of reward that is controllably achievable, 𝜒 (though using information-theoretic definitions(2,3) would work as well). To the extent that this fraction depends on the amount of resources the agent is able and willing to invest (max 𝐶), this formulation can be probabilistically computed without information about the particular agent involved, specifically, by assuming a certain distribution of agents with different amounts of available resources. This would result in a probability distribution over 𝜒. Elasticity can thus be defined as the amount of information obtained about controllability due to knowing the amount of resources available to the agent: I(𝜒; max 𝐶). We will add this formal definition to the manuscript.  

Turning to experiment, the authors make two key claims: (1) people infer the elasticity of control, and (2) individual differences in how people make this inference are importantly related to psychopathology. Starting with claim 1, there are three sub-claims here; implicitly, the authors make all three. (1A) People's behavior is sensitive to differences in elasticity, (1B) people actually represent/track something like elasticity, and (1C) people do so naturally as they go about their daily lives. The results clearly support 1A. However, 1B and 1C are not supported. Starting with 1B, the experiment cannot support the claim that people represent or track elasticity because the effort is the only dimension over which participants can engage in any meaningful decision-making (the other dimension, selecting which destination to visit, simply amounts to selecting the location where you were just told the treasure lies). Thus, any adaptive behavior will necessarily come out in a sensitivity to how outcomes depend on effort. More concretely, any model that captures the fact that you are more likely to succeed in two attempts than one will produce the observed behavior. The null models do not make this basic assumption and thus do not provide a useful comparison.

We appreciate the reviewer's critical analysis of our claims regarding elasticity inference, which as detailed below, has led to an important new analysis that strengthens the study’s conclusions. However, we respectfully disagree with two of the Reviewer’s arguments. First, resource investment was not the only meaningful decision dimension in our task, since participant also needed to choose the correct vehicle to get to the right destination. That this was not trivial is evidenced by our exclusion of over 8% of participants who made incorrect vehicle choices more than 10% of the time. Included participants also occasionally erred in this choice (mean error rate = 3%, range [0-10%]). 

Second, the experimental task cannot be solved well by a model that simply tracks how outcomes depend on effort because 20% of the time participants reached the treasure despite failing to board their vehicle of choice. In such cases, reward outcomes and control were decoupled. Participants could identify when this was the case by observing the starting location, which was revealed together with the outcome (since depending on the starting location, the treasure location was automatically reached by walking). To determine whether participants distinguished between control-related and non-control-related reward, we have now fitted a variant of our model to the data that allows learning from each of these kinds of outcomes by means of a different free parameter. The results show that participants learned considerably more from control-related outcomes. They were thus not merely tracking outcomes, but specifically inferred when outcomes can be attributed to control. We will include this new analysis in the revised manuscript.

Controllability inference by itself, however, still does not suffice to explain the observed behavior. This is shown by our ‘controllability’ model, which learns to invest more resources to improve control, yet still fails to capture key features of participants’ behavior, as detailed in the manuscript. This means that explaining participants’ behavior requires a model that not only infers controllability—beyond merely outcome probability—but also assumes a priori that increased effort could enhance control. Building these a priori assumption into the model amounts to embedding within it an understanding of elasticity – the idea that control over the environment may be increased by greater resource investment. 

That being said, we acknowledge the value in considering alternative computational formulations of adaptation to elasticity. Thus, in our revision of the manuscript, we will add a discussion concerning possible alternative models.  

For 1C, the claim that people infer elasticity outside of the experimental task cannot be supported because the authors explicitly tell people about the two notions of control as part of the training phase: "To reinforce participants' understanding of how elasticity and controllability were manifested in each planet, [participants] were informed of the planet type they had visited after every 15 trips." (line 384).

We thank the reviewer for highlighting this point. We agree that our experimental design does not test whether people infer elasticity spontaneously. Our research question was whether people can distinguish between elastic and inelastic controllability. The results strongly support that they can, and this does have potential implications for behavior outside of the experimental task. Specifically, to the extent that people are aware that in some contexts additional resource investment improve control, whereas in other contexts it does not, then our results indicate that they would be able to distinguish between these two kinds of contexts through trial-and-error learning. That said, we agree that investigating whether and how people spontaneously infer elasticity is an interesting direction for future work. We will clarify the scope of the present conclusions in the revised manuscript.

Finally, I turn to claim 2, that individual differences in how people infer elasticity are importantly related to psychopathology. There is much to say about the decision to treat psychopathology as a unidimensional construct. However, I will keep it concrete and simply note that CCA (by design) obscures the relationship between any two variables. Thus, as suggestive as Figure 6B is, we cannot conclude that there is a strong relationship between Sense of Agency and the elasticity bias---this result is consistent with any possible relationship (even a negative one). The fact that the direct relationship between these two variables is not shown or reported leads me to infer that they do not have a significant or strong relationship in the data.

We agree that CCA is not designed to reveal the relationship between any two variables. However, the advantage of this analysis is that it pulls together information from multiple variables. Doing so does not treat psychopathology as unidimensional. Rather, it seeks a particular dimension that most strongly correlates with different aspects of task performance. This is especially useful for multidimensional psychopathology data because such data are often dominated by strong correlations between dimensions, whereas the research seeks to explain the distinctions between the dimensions. Similar considerations hold for the multidimensional task parameters, which although less correlated, may still jointly predict the relevant psychopathological profile better than each parameter does in isolation. Thus, the CCA enabled us to identify a general relationship between task performance and psychopathology that accounts for different symptom measures and aspects of controllability inference. 

Using CCA can thus reveal relationships that do not readily show up in two-variable analyses. Indeed, the direct correlation between Sense of Agency (SOA) and elasticity bias was not significant – a result that, for completeness, we will now report in the supplementary materials along with all other direct correlations. We note, however, that the CCA analysis was preregistered and its results were replicated. Furthermore, an auxiliary analysis specifically confirmed the contributions of both elasticity bias (Figure 6D, bottom plot) and, although not reported in the original paper, of the Sense of Agency score (SOA; p\=.03 permutation test) to the observed canonical correlation. Participants scoring higher on the psychopathology profile also overinvested resources in inelastic environments but did not futilely invest in uncontrollable environments (Figure 6A), providing external validation to the conclusion that the CCA captured meaningful variance specific to elasticity inference. The results thus enable us to safely conclude that differences in elasticity inferences are significantly associated with a profile of controlrelated psychopathology to which SOA contributed significantly.  

Finally, whereas interpretation of individual CCA loadings that were not specifically tested remains speculative, we note that the pattern of loadings largely replicated across the initial and replication studies (see Figure 6B), and aligns with prior findings. For instance, the positive loadings of SOA and OCD match prior suggestions that a lower sense of control leads to greater compensatory effort(7), whereas the negative loading for depression scores matches prior work showing reduced resource investment in depression(5-6).

We will revise the text to better clarify the advantageous and disadvantageous of our analytical approach, and the conclusions that can and cannot be drawn from it.

There is also a feature of the task that limits our ability to draw strong conclusions about individual differences in elasticity inference. As the authors clearly acknowledge, the task was designed "to be especially sensitive to overestimation of elasticity" (line 287). A straightforward consequence of this is that the resulting *empirical* estimate of estimation bias (i.e., the gamma_elasticity parameter) is itself biased. This immediately undermines any claim that references the directionality of the elasticity bias (e.g. in the abstract). Concretely, an undirected deficit such as slower learning of elasticity would appear as a directed overestimation bias. When we further consider that elasticity inference is the only meaningful learning/decisionmaking problem in the task (argued above), the situation becomes much worse. Many general deficits in learning or decision-making would be captured by the elasticity bias parameter. Thus, a conservative interpretation of the results is simply that psychopathology is associated with impaired learning and decision-making.

We apologize for our imprecise statement that the task was ‘especially sensitive to overestimation of elasticity’, which justifiably led to Reviewer’s concern that slower elasticity learning can be mistaken for elasticity bias. To make sure this was not the case, we made use of the fact that our computational model explicitly separates bias direction (λ) from the rate of learning through two distinct parameters, which initialize the prior concentration and mean of the model’s initial beliefs concerning elasticity (see Methods pg. 22). The higher the concentration of the initial beliefs (𝜖), the slower the learning. Parameter recovery tests confirmed that our task enables acceptable recovery of both the bias λ_elasticity (r=.81) and the concentration 𝝐_elasticity (r=.59) parameters. And importantly, the level of confusion between the parameters was low (confusion of 0.15 for 𝝐_elasticity→ λ_elasticity and 0.04 for λ_elasticity→ 𝝐_elasticity). This result confirms that our task enables dissociating elasticity biases from the rate of elasticity learning. 

Moreover, to validate that the minimal level of confusion existing between bias and the rate of learning did not drive our psychopathology results, we re-ran the CCA while separating concentration from bias parameters. The results (Author response image 1) demonstrate that differences in learning rate (𝜖) had virtually no contribution to our CCA results, whereas the contribution of the pure bias (𝜆) was preserved. 

We will incorporate these clarifications and additional analysis in our revised manuscript.

Author response image 1.

Showing that a model parameter correlates with the data it was fit to does not provide any new information, and cannot support claims like "a prior assumption that control is likely available was reflected in a futile investment of resources in uncontrollable environments." To make that claim, one must collect independent measures of the assumption and the investment.

We apologize if this and related statements seemed to be describing independent findings. They were merely meant to describe the relationship between model parameters and modelindependent measures of task performance. It is inaccurate, though, to say that they provide no new information, since results could have been otherwise. For instance, instead of a higher controllability bias primarily associating with futile investment of resources in uncontrollable environments, it could have been primarily associated with more proper investment of resources in high-controllability environments. Additionally, we believe these analyses are of value to readers who seek to understand the role of different parameters in the model. In our planned revision, we will clarify that the relevant analyses are merely descriptive. 

Did participants always make two attempts when purchasing tickets? This seems to violate the intuitive model, in which you would sometimes succeed on the first jump. If so, why was this choice made? Relatedly, it is not clear to me after a close reading how the outcome of each trial was actually determined.

We thank the reviewer for highlighting the need to clarify these aspects of the task in the revised manuscript. 

When participants purchased two extra tickets, they attempted both jumps, and were never informed about whether either of them succeeded. Instead, after choosing a vehicle and attempting both jumps, participants were notified where they arrived at. This outcome was determined based on the cumulative probability of either of the two jumps succeeding. Success meant that participants arrived at where their chosen vehicle goes, whereas failure meant they walked to the nearest location (as determined by where they started from). 

Though it is unintuitive to attempt a second jump before seeing whether the first succeed, this design choice ensured two key objectives. First, that participants would consistently need to invest not only more money but also more effort and time in planets with high elastic controllability. Second, that the task could potentially generalize to the many real-world situations where the amount of invested effort has to be determined prior to seeing any outcome, for instance, preparing for an exam or a job interview. 

It should be noted that the model is heuristically defined and does not reflect Bayesian updating. In particular, it overestimates control by not using losses with less than 3 tickets (intuitively, the inference here depends on your beliefs about elasticity). I wonder if the forced three-ticket trials in the task might be historically related to this modeling choice.

We apologize for not making this clear, but in fact losing with less than 3 tickets does reduce the model’s estimate of available control. It does so by increasing the elasticity estimates

(a_elastic≥1, a_elastic2 parameters), signifying that more tickets are needed to obtain the maximum available level of control, thereby reducing the average controllability estimate across ticket investment options. 

It would be interesting to further develop the model such that losing with less than 3 tickets would also impact inferences concerning the maximum available control, depending on present beliefs concerning elasticity, but the forced three-ticket purchases already expose participants to the maximum available control, and thus, the present data may not be best suited to test such a model. These trials were implemented to minimize individual differences concerning inferences of maximum available control, thereby focusing differences on elasticity inferences. We will discuss the Reviewer’s suggestion for a potentially more accurate model in the revised manuscript. 

References

(1) Huys, Q. J. M., & Dayan, P. (2009). A Bayesian formulation of behavioral control. Cognition, 113(3), 314– 328.

(2) Ligneul, R. (2021). Prediction or causation? Towards a redefinition of task controllability. Trends in Cognitive Sciences, 25(6), 431–433.

(3) Mistry, P., & Liljeholm, M. (2016). Instrumental divergence and the value of control. Scientific Reports, 6, 36295.

(4) Lin, J. (1991). Divergence measures based on the Shannon entropy. IEEE Transactions on Information Theory, 37(1), 145–151

(5) Cohen RM, Weingartner H, Smallberg SA, Pickar D, Murphy DL. Effort and cognition in depression. Arch Gen Psychiatry. 1982 May;39(5):593-7. doi: 10.1001/archpsyc.1982.04290050061012. PMID: 7092490.

(6) Bi R, Dong W, Zheng Z, Li S, Zhang D. Altered motivation of effortful decision-making for self and others in subthreshold depression. Depress Anxiety. 2022 Aug;39(8-9):633-645. doi: 10.1002/da.23267. Epub 2022 Jun 3. PMID: 35657301; PMCID: PMC9543190.

(7) Tapal, A., Oren, E., Dar, R., & Eitam, B. (2017). The Sense of Agency Scale: A measure of consciously perceived control over one's mind, body, and the immediate environment. Frontiers in Psychology, 8, 1552

eLife Assessment

This valuable retrospective analysis identified three independent components of glucose dynamics - "value," "variability," and "autocorrelation" - which may be used in predicting coronary plaque vulnerability. The study is solid and of interest to a wide range of investigators in the medical field who are interested in the role of glycemia on cardiometabolic health. However, the generalizability of the results needs further confirmation through experimental and prospective validation.

Reviewer #1 (Public review):

Summary:

This study identified three independent components of glucose dynamics-"value," "variability," and "autocorrelation", and reported important findings indicating that they play an important role in predicting coronary plaque vulnerability. Although the generalizability of the results needs further investigation due to the limited sample size and validation cohort limitations, this study makes several notable contributions: validation of autocorrelation as a new clinical indicator, theoretical support through mathematical modeling, and development of a web application for practical implementation. These contributions are likely to attract broad interest from researchers in both diabetology and cardiology and may suggest the potential for a new approach to glucose monitoring that goes beyond conventional glycemic control indicators in clinical practice.

Strengths:

The most notable strength of this study is the identification of three independent elements in glycemic dynamics: value, variability, and autocorrelation. In particular, the metric of autocorrelation, which has not been captured by conventional glycemic control indices, may bring a new perspective for understanding glycemic dynamics. In terms of methodological aspects, the study uses an analytical approach combining various statistical methods such as factor analysis, LASSO, and PLS regression, and enhances the reliability of results through theoretical validation using mathematical models and validation in other cohorts. In addition, the practical aspect of the research results, such as the development of a Web application, is also an important contribution to clinical implementation.

Weaknesses:

The most significant weakness of this study is the relatively small sample size of 53 study subjects. This sample size limitation leads to a lack of statistical power, especially in subgroup analyses, and to limitations in the assessment of rare events. In terms of validation, several challenges exist, including geographical and ethnic biases in the validation cohorts, lack of long-term follow-up data, and insufficient validation across different clinical settings. In terms of data representativeness, limiting factors include the inclusion of only subjects with well-controlled serum cholesterol and blood pressure and the use of only short-term measurement data. In terms of elucidation of physical mechanisms, the study is not sufficient to elucidate the mechanisms linking autocorrelation and clinical outcomes or to verify them at the cellular or molecular level.

Reviewer #2 (Public review):

Summary:

Sugimoto et al. explore the relationship between glucose dynamics - specifically value, variability, and autocorrelation - and coronary plaque vulnerability in patients with varying glucose tolerance levels. The study identifies three independent predictive factors for %NC and emphasizes the use of continuous glucose monitoring (CGM)-derived indices for coronary artery disease (CAD) risk assessment. By employing robust statistical methods and validating findings across datasets from Japan, America, and China, the authors highlight the limitations of conventional markers while proposing CGM as a novel approach for risk prediction. The study has the potential to reshape CAD risk assessment by emphasizing CGM-derived indices, aligning well with personalized medicine trends.

Strengths:

(1) The introduction of autocorrelation as a predictive factor for plaque vulnerability adds a novel dimension to glucose dynamic analysis.

(2) Inclusion of datasets from diverse regions enhances generalizability.

(3) The use of a well-characterized cohort with controlled cholesterol and blood pressure levels strengthens the findings.

(4) The focus on CGM-derived indices aligns with personalized medicine trends, showcasing the potential for CAD risk stratification.

Weaknesses:

(1) The link between autocorrelation and plaque vulnerability remains speculative without a proposed biological explanation.

(2) The relatively small sample size (n=270) limits statistical power, especially when stratified by glucose tolerance levels.

(3) Strict participant selection criteria may reduce applicability to broader populations.

(4) CGM-derived indices like AC_Var and ADRR may be too complex for routine clinical use without simplified models or guidelines.

(5) The study does not compare CGM-derived indices to existing advanced CAD risk models, limiting the ability to assess their true predictive superiority.

(6) Varying CGM sampling intervals (5-minute vs. 15-minute) were not thoroughly analyzed for impact on results.

Reviewer #3 (Public review):

Summary:

This is a retrospective analysis of 53 individuals over 26 features (12 clinical phenotypes, 12 CGM features, and 2 autocorrelation features) to examine which features were most informative in predicting percent necrotic core (%NC) as a parameter for coronary plaque vulnerability. Multiple regression analysis demonstrated a better ability to predict %NC from 3 selected CGM-derived features than 3 selected clinical phenotypes. LASSO regularization and partial least squares (PLS) with VIP scores were used to identify 4 CGM features that most contribute to the precision of %NC. Using factor analysis they identify 3 components that have CGM-related features: value (relating to the value of blood glucose), variability (relating to glucose variability), and autocorrelation (composed of the two autocorrelation features). These three groupings appeared in the 3 validation cohorts and when performing hierarchical clustering. To demonstrate how these three features change, a simulation was created to allow the user to examine these features under different conditions.

Review:

The goal of this study was to identify CGM features that relate to %NC. Through multiple feature selection methods, they arrive at 3 components: value, variability, and autocorrelation. While the feature list is highly correlated, the authors take steps to ensure feature selection is robust. There is a lack of clarity of what each component (value, variability, and autocorrelation) includes as while similar CGM indices fall within each component, there appear to be some indices that appear as relevant to value in one dataset and to variability in the validation. We are sceptical about statements of significance without documentation of p-values. While hesitations remain, the ability of these authors to find groupings of these many CGM metrics in relation to %NC is of interest. The believability of the associations is impeded by an obtuse presentation of the results with core data (i.e. correlation plots between CGM metrics and %NC) buried in the supplement while main figures contain plots of numerical estimates from models which would be more usefully presented in supplementary tables. Given the small sample size in the primary analysis, there is a lot of modeling done with parameters estimated where simpler measures would serve and be more convincing as they require less data manipulation. A major example of this is that the pairwise correlation/covariance between CGM_mean, CGM_std, and AC_var is not shown and would be much more compelling in the claim that these are independent factors. Lack of methodological detail is another challenge. For example, the time period of CGM metrics or CGM placement in the primary study in relation to the IVUS-derived measurements of coronary plaques is unclear. Are they temporally distant or proximal/ concurrent with the PCI? A patient undergoing PCI for coronary intervention would be expected to have physiological and iatrogenic glycemic disturbances that do not reflect their baseline state. This is not considered or discussed. The attempts at validation in external cohorts, Japanese, American, and Chinese are very poorly detailed. We could only find even an attempt to examine cardiovascular parameters in the Chinese data set but the outcome variables are unspecified with regard to what macrovascular events are included, their temporal relation to the CGM metrics, etc. Notably macrovascular event diagnoses are very different from the coronary plaque necrosis quantification. This could be a source of strength in the findings if carefully investigated and detailed but due to the lack of detail seems like an apples-to-oranges comparison. Finally, the simulations at the end are not relevant to the main claims of the paper and we would recommend removing them for the coherence of this manuscript.

Author response:

Reviewer #1 (Public review):

Summary:

This study identified three independent components of glucose dynamics-"value," "variability," and "autocorrelation", and reported important findings indicating that they play an important role in predicting coronary plaque vulnerability. Although the generalizability of the results needs further investigation due to the limited sample size and validation cohort limitations, this study makes several notable contributions: validation of autocorrelation as a new clinical indicator, theoretical support through mathematical modeling, and development of a web application for practical implementation. These contributions are likely to attract broad interest from researchers in both diabetology and cardiology and may suggest the potential for a new approach to glucose monitoring that goes beyond conventional glycemic control indicators in clinical practice.

Strengths:

The most notable strength of this study is the identification of three independent elements in glycemic dynamics: value, variability, and autocorrelation. In particular, the metric of autocorrelation, which has not been captured by conventional glycemic control indices, may bring a new perspective for understanding glycemic dynamics. In terms of methodological aspects, the study uses an analytical approach combining various statistical methods such as factor analysis, LASSO, and PLS regression, and enhances the reliability of results through theoretical validation using mathematical models and validation in other cohorts. In addition, the practical aspect of the research results, such as the development of a Web application, is also an important contribution to clinical implementation.

We appreciate reviewer #1 for the positive assessment and for the valuable and constructive comments on our manuscript.

Weaknesses:

The most significant weakness of this study is the relatively small sample size of 53 study subjects. This sample size limitation leads to a lack of statistical power, especially in subgroup analyses, and to limitations in the assessment of rare events.

We appreciate the reviewer’s concern regarding the sample size. We acknowledge that a larger sample size would increase statistical power, especially for subgroup analyses and the assessment of rare events.

We would like to clarify several points regarding the statistical power and validation of our findings. Our sample size determination followed established methodological frameworks, including the guidelines outlined by Muyembe Asenahabi, Bostely, and Peters Anselemo Ikoha. “Scientific research sample size determination.” (2023). These guidelines balance the risks of inadequate sample size with the challenges of unnecessarily large samples. For our primary analysis examining the correlation between CGM-derived measures and %NC, power calculations (a type I error of 0.05, a power of 0.8, and an expected correlation coefficient of 0.4) indicated that a minimum of 47 participants was required. Our sample size of 53 exceeded this threshold and allowed us to detect statistically significant correlations, as described in the Methods section. Moreover, to provide transparency about the precision of our estimates, we have included confidence intervals for all coefficients.

Furthermore, our sample size aligns with previous studies investigating the associations between glucose profiles and clinical parameters, including Torimoto, Keiichi, et al. “Relationship between fluctuations in glucose levels measured by continuous glucose monitoring and vascular endothelial dysfunction in type 2 diabetes mellitus.” Cardiovascular Diabetology 12 (2013): 1-7. (n=57), Hall, Heather, et al. “Glucotypes reveal new patterns of glucose dysregulation.” PLoS biology 16.7 (2018): e2005143. (n=57), and Metwally, Ahmed A., et al. “Prediction of metabolic subphenotypes of type 2 diabetes via continuous glucose monitoring and machine learning.” Nature Biomedical Engineering (2024): 1-18. (n=32).

Furthermore, the primary objective of our study was not to assess rare events, but rather to demonstrate that glucose dynamics can be decomposed into three main factors - mean, variance and autocorrelation - whereas traditional measures have primarily captured mean and variance without adequately reflecting autocorrelation. We believe that our current sample size effectively addresses this objective.

Regarding the classification of glucose dynamics components, we have conducted additional validation across diverse populations including 64 Japanese, 53 American, and 100 Chinese individuals. These validation efforts have consistently supported our identification of three independent glucose dynamics components.

However, we acknowledge the importance of further validation on a larger scale. To address this, we conducted a large follow-up study of over 8,000 individuals (Sugimoto, Hikaru, et al. “Stratification of individuals without prior diagnosis of diabetes using continuous glucose monitoring” medRxiv (2025)), which confirmed our main finding that glucose dynamics consist of mean, variance, and autocorrelation. As this large study was beyond the scope of the present manuscript due to differences in primary objectives and analytical approaches, it was not included in this paper; however, it provides further support for the clinical relevance and generalizability of our findings.

To address the sample size considerations, we will add the following sentences in the Discussion section:

Although our analysis included four datasets with a total of 270 individuals, and our sample size of 53 met the required threshold based on power calculations with a type I error of 0.05, a power of 0.8, and an expected correlation coefficient of 0.4, we acknowledge that the sample size may still be considered relatively small for a comprehensive assessment of these relationships. To further validate these findings, larger prospective studies with diverse populations are needed to improve the predictive utility and generalizability of our findings.

We appreciate the reviewer’s feedback and believe that these clarifications will strengthen the manuscript.

In terms of validation, several challenges exist, including geographical and ethnic biases in the validation cohorts, lack of long-term follow-up data, and insufficient validation across different clinical settings. In terms of data representativeness, limiting factors include the inclusion of only subjects with well-controlled serum cholesterol and blood pressure and the use of only short-term measurement data.

We appreciate the reviewer’s comment regarding the challenges associated with validation. In terms of geographic and ethnic diversity, our study includes validation cohorts from diverse populations, including 64 Japanese, 53 American and 100 Chinese individuals. These cohorts include a wide range of metabolic states, from healthy individuals to those with diabetes, ensuring validation across different clinical conditions. In addition, we recognize the limited availability of publicly available datasets with sufficient sample sizes for factor decomposition that include both healthy individuals and those with type 2 diabetes (Zhao, Qinpei, et al. “Chinese diabetes datasets for data-driven machine learning.” Scientific Data 10.1 (2023): 35.). The main publicly available datasets with relevant clinical characteristics have already been analyzed in this study using unbiased approaches.

However, we fully agree with the reviewer that expanding the geographic and ethnic scope, including long-term follow-up data, and validation in different clinical settings would further strengthen the robustness and generalizability of our findings. To address this, we conducted a large follow-up study of over 8,000 individuals with two years of follow-up (Sugimoto, Hikaru, et al. “Stratification of individuals without prior diagnosis of diabetes using continuous glucose monitoring” medRxiv (2025)), which confirmed our main finding that glucose dynamics consist of mean, variance, and autocorrelation. As this large study was beyond the scope of the present manuscript due to differences in primary objectives and analytical approaches, it was not included in this paper; however, it provides further support for the clinical relevance and generalizability of our findings.

Regarding the validation considerations, we will add the following sentences to the Discussion section:

Although our analysis included four datasets with a total of 270 individuals, and our sample size of 53 met the required threshold based on power calculations with a type I error of 0.05, a power of 0.8, and an expected correlation coefficient of 0.4, we acknowledge that the sample size may still be considered relatively small for a comprehensive assessment of these relationships. To further validate these findings, larger prospective studies with diverse populations are needed to improve the predictive utility and generalizability of our findings.

Although our LASSO and factor analysis indicated that CGM-derived measures were strong predictors of %NC, this does not mean that other clinical parameters, such as lipids and blood pressure, are irrelevant in T2DM complications. Our study specifically focused on characterizing glucose dynamics, and we analyzed individuals with well-controlled serum cholesterol and blood pressure to reduce confounding effects. While we anticipate that inclusion of a more diverse population would not alter our primary findings regarding glucose dynamics, it is likely that a broader data set would reveal additional predictive contributions from lipid and blood pressure parameters.

In terms of elucidation of physical mechanisms, the study is not sufficient to elucidate the mechanisms linking autocorrelation and clinical outcomes or to verify them at the cellular or molecular level.

We appreciate the reviewer’s point regarding the need for further elucidation of the physical mechanisms linking glucose autocorrelation to clinical outcomes. We fully agree with the reviewer that the detailed molecular and cellular mechanisms underlying this relationship are not yet fully understood, as noted in our Discussion section.

However, we would like to emphasize the theoretical basis that supports the clinical relevance of autocorrelation. Our results show that glucose profiles with identical mean and variability can exhibit different autocorrelation patterns, highlighting that conventional measures such as mean or variance alone may not fully capture inter-individual metabolic differences. Incorporating autocorrelation analysis provides a more comprehensive characterization of metabolic states. Consequently, incorporating autocorrelation measures alongside traditional diabetes diagnostic criteria - such as fasting glucose, HbA1c and PG120, which primarily reflect only the “mean” component - can improve predictive accuracy for various clinical outcomes. While further research at the cellular and molecular level is needed to fully validate these findings, it is important to note that the primary goal of this study was to analyze the characteristics of glucose dynamics and gain new insights into metabolism, rather than to perform molecular biology experiments.

Furthermore, our previous research has shown that glucose autocorrelation reflects changes in insulin clearance (Sugimoto, Hikaru, et al. “Improved Detection of Decreased Glucose Handling Capacities via Novel Continuous Glucose Monitoring-Derived Indices: AC_Mean and AC_Var.” medRxiv (2023): 2023-09.). The relationship between insulin clearance and cardiovascular disease has been well documented (Randrianarisoa, Elko, et al. “Reduced insulin clearance is linked to subclinical atherosclerosis in individuals at risk for type 2 diabetes mellitus.” Scientific reports 10.1 (2020): 22453.), and the mechanisms described in this prior work may potentially explain the association between glucose autocorrelation and clinical outcomes observed in the present study.

Rather than a limitation, we view these currently unexplored associations as an opportunity for further research. The identification of autocorrelation as a key glycemic feature introduces a new dimension to metabolic regulation that could serve as the basis for future investigations exploring the molecular mechanisms underlying these patterns.

While we agree that further research at the cellular and molecular level is needed to fully validate these findings, we believe that our study provides a strong theoretical framework to support the clinical utility of autocorrelation analysis in glucose monitoring, and that this could serve as the basis for future investigations exploring the molecular mechanisms underlying these autocorrelation patterns, which adds to the broad interest of this study. Regarding the physical mechanisms linking autocorrelation and clinical outcomes, we will add the following sentences in the Discussion section:

This study also provided evidence that autocorrelation can vary independently from the mean and variance components using simulated data. In addition, simulated glucose dynamics indicated that even individuals with high AC_Var did not necessarily have high maximum and minimum blood glucose levels. This study also indicated that these three components qualitatively corresponded to the four distinct glucose patterns observed after glucose administration, which were identified in a previous study (Hulman et al., 2018). Thus, the inclusion of autocorrelation in addition to mean and variance may improve the characterization of inter-individual differences in glucose regulation and improve the predictive accuracy of various clinical outcomes.

Despite increasing evidence linking glycemic variability to oxidative stress and endothelial dysfunction in T2DM complications (Ceriello et al., 2008; Monnier et al., 2008), the biological mechanisms underlying the independent predictive value of autocorrelation remain to be elucidated. Our previous work has shown that glucose autocorrelation is influenced by insulin clearance (Sugimoto et al., 2023), a process known to be associated with cardiovascular disease risk (Randrianarisoa et al., 2020). Therefore, the molecular pathways linking glucose autocorrelation to cardiovascular disease may share common mechanisms with those linking insulin clearance to cardiovascular disease. Although previous studies have primarily focused on investigating the molecular mechanisms associated with mean glucose levels and glycemic variability, our findings open new avenues for exploring the molecular basis of glucose autocorrelation, potentially revealing novel therapeutic targets for preventing diabetic complications.

Reviewer #2 (Public review):

Sugimoto et al. explore the relationship between glucose dynamics - specifically value, variability, and autocorrelation - and coronary plaque vulnerability in patients with varying glucose tolerance levels. The study identifies three independent predictive factors for %NC and emphasizes the use of continuous glucose monitoring (CGM)-derived indices for coronary artery disease (CAD) risk assessment. By employing robust statistical methods and validating findings across datasets from Japan, America, and China, the authors highlight the limitations of conventional markers while proposing CGM as a novel approach for risk prediction. The study has the potential to reshape CAD risk assessment by emphasizing CGM-derived indices, aligning well with personalized medicine trends.

Strengths:

(1) The introduction of autocorrelation as a predictive factor for plaque vulnerability adds a novel dimension to glucose dynamic analysis.

(2) Inclusion of datasets from diverse regions enhances generalizability.

(3) The use of a well-characterized cohort with controlled cholesterol and blood pressure levels strengthens the findings.

(4) The focus on CGM-derived indices aligns with personalized medicine trends, showcasing the potential for CAD risk stratification.

We appreciate reviewer #2 for the positive assessment and for the valuable and constructive comments on our manuscript.

Weaknesses:

(1) The link between autocorrelation and plaque vulnerability remains speculative without a proposed biological explanation.

We appreciate the reviewer’s point about the need for a clearer biological explanation linking glucose autocorrelation to plaque vulnerability. We fully agree with the reviewer that the detailed biological mechanisms underlying this relationship are not yet fully understood, as noted in our Discussion section.

However, we would like to emphasize the theoretical basis that supports the clinical relevance of autocorrelation. Our results show that glucose profiles with identical mean and variability can exhibit different autocorrelation patterns, highlighting that conventional measures such as mean or variance alone may not fully capture inter-individual metabolic differences. Incorporating autocorrelation analysis provides a more comprehensive characterization of metabolic states. Consequently, incorporating autocorrelation measures alongside traditional diabetes diagnostic criteria - such as fasting glucose, HbA1c and PG120, which primarily reflect only the “mean” component - can improve predictive accuracy for various clinical outcomes.

Furthermore, our previous research has shown that glucose autocorrelation reflects changes in insulin clearance (Sugimoto, Hikaru, et al. “Improved Detection of Decreased Glucose Handling Capacities via Novel Continuous Glucose Monitoring-Derived Indices: AC_Mean and AC_Var.” medRxiv (2023): 2023-09.). The relationship between insulin clearance and cardiovascular disease has been well documented (Randrianarisoa, Elko, et al. “Reduced insulin clearance is linked to subclinical atherosclerosis in individuals at risk for type 2 diabetes mellitus.” Scientific reports 10.1 (2020): 22453.), and the mechanisms described in this prior work may potentially explain the association between glucose autocorrelation and clinical outcomes observed in the present study.

Rather than a limitation, we view these currently unexplored associations as an opportunity for further research. The identification of autocorrelation as a key glycemic feature introduces a new dimension to metabolic regulation that could serve as the basis for future investigations exploring the molecular mechanisms underlying these patterns.

While we agree that further research at the cellular and molecular level is needed to fully validate these findings, we believe that our study provides a strong theoretical framework to support the clinical utility of autocorrelation analysis in glucose monitoring, and that this could serve as the basis for future investigations exploring the molecular mechanisms underlying these autocorrelation patterns, which adds to the broad interest of this study. Regarding the physical mechanisms linking autocorrelation and clinical outcomes, we will add the following sentences in the Discussion section:

This study also provided evidence that autocorrelation can vary independently from the mean and variance components using simulated data. In addition, simulated glucose dynamics indicated that even individuals with high AC_Var did not necessarily have high maximum and minimum blood glucose levels. This study also indicated that these three components qualitatively corresponded to the four distinct glucose patterns observed after glucose administration, which were identified in a previous study (Hulman et al., 2018). Thus, the inclusion of autocorrelation in addition to mean and variance may improve the characterization of inter-individual differences in glucose regulation and improve the predictive accuracy of various clinical outcomes.

Despite increasing evidence linking glycemic variability to oxidative stress and endothelial dysfunction in T2DM complications (Ceriello et al., 2008; Monnier et al., 2008), the biological mechanisms underlying the independent predictive value of autocorrelation remain to be elucidated. Our previous work has shown that glucose autocorrelation is influenced by insulin clearance (Sugimoto et al., 2023), a process known to be associated with cardiovascular disease risk (Randrianarisoa et al., 2020). Therefore, the molecular pathways linking glucose autocorrelation to cardiovascular disease may share common mechanisms with those linking insulin clearance to cardiovascular disease. Although previous studies have primarily focused on investigating the molecular mechanisms associated with mean glucose levels and glycemic variability, our findings open new avenues for exploring the molecular basis of glucose autocorrelation, potentially revealing novel therapeutic targets for preventing diabetic complications.

(2) The relatively small sample size (n=270) limits statistical power, especially when stratified by glucose tolerance levels.

We appreciate the reviewer’s concern regarding sample size and its potential impact on statistical power, especially when stratified by glucose tolerance level. We fully agree that a larger sample size would increase statistical power, especially for subgroup analyses.

We would like to clarify several points regarding the statistical power and validation of our findings. Our sample size determination followed established methodological frameworks, including the guidelines outlined by Muyembe Asenahabi, Bostely, and Peters Anselemo Ikoha. “Scientific research sample size determination.” (2023). These guidelines balance the risks of inadequate sample size with the challenges of unnecessarily large samples. For our primary analysis examining the correlation between CGM-derived measures and %NC, power calculations (a type I error of 0.05, a power of 0.8, and an expected correlation coefficient of 0.4) indicated that a minimum of 47 participants was required. Our sample size of 53 exceeded this threshold and allowed us to detect statistically significant correlations, as described in the Methods section. Moreover, to provide transparency about the precision of our estimates, we have included confidence intervals for all coefficients.

Furthermore, our sample size aligns with previous studies investigating the associations between glucose profiles and clinical parameters, including Torimoto, Keiichi, et al. “Relationship between fluctuations in glucose levels measured by continuous glucose monitoring and vascular endothelial dysfunction in type 2 diabetes mellitus.” Cardiovascular Diabetology 12 (2013): 1-7. (n=57), Hall, Heather, et al. “Glucotypes reveal new patterns of glucose dysregulation.” PLoS biology 16.7 (2018): e2005143. (n=57), and Metwally, Ahmed A., et al. “Prediction of metabolic subphenotypes of type 2 diabetes via continuous glucose monitoring and machine learning.” Nature Biomedical Engineering (2024): 1-18. (n=32).

Regarding the classification of glucose dynamics components, we have conducted additional validation across diverse populations including 64 Japanese, 53 American, and 100 Chinese individuals. These validation efforts have consistently supported our identification of three independent glucose dynamics components.

However, we acknowledge the importance of further validation on a larger scale. To address this, we conducted a large follow-up study of over 8,000 individuals with two years of follow-up (Sugimoto, Hikaru, et al. “Stratification of individuals without prior diagnosis of diabetes using continuous glucose monitoring” medRxiv (2025)), which confirmed our main finding that glucose dynamics consist of mean, variance, and autocorrelation. As this large study was beyond the scope of the present manuscript due to differences in primary objectives and analytical approaches, it was not included in this paper; however, it provides further support for the clinical relevance and generalizability of our findings.

To address the sample size considerations, we will add the following sentences in the Discussion section:

Although our analysis included four datasets with a total of 270 individuals, and our sample size of 53 met the required threshold based on power calculations with a type I error of 0.05, a power of 0.8, and an expected correlation coefficient of 0.4, we acknowledge that the sample size may still be considered relatively small for a comprehensive assessment of these relationships. To further validate these findings, larger prospective studies with diverse populations are needed to improve the predictive utility and generalizability of our findings.

(3) Strict participant selection criteria may reduce applicability to broader populations.

We appreciate the reviewer’s comment regarding the potential impact of strict participant selection criteria on the broader applicability of our findings. We acknowledge that extending validation to more diverse populations would improve the generalizability of our findings.

Our study includes validation cohorts from diverse populations, including 64 Japanese, 53 American and 100 Chinese individuals. These cohorts include a wide range of metabolic states, from healthy individuals to those with diabetes, ensuring validation across different clinical conditions. However, we acknowledge that further validation in additional populations and clinical settings would strengthen our conclusions. To address this, we conducted a large follow-up study of over 8,000 individuals (Sugimoto, Hikaru, et al. “Stratification of individuals without prior diagnosis of diabetes using continuous glucose monitoring” medRxiv (2025)), which confirmed our main finding that glucose dynamics consist of mean, variance, and autocorrelation. As this large study was beyond the scope of the present manuscript due to differences in primary objectives and analytical approaches, it was not included in this paper; however, it provides further support for the clinical relevance and generalizability of our findings.

We will add the following text to the Discussion section to address these considerations:

Although our analysis included four datasets with a total of 270 individuals, and our sample size of 53 met the required threshold based on power calculations with a type I error of 0.05, a power of 0.8, and an expected correlation coefficient of 0.4, we acknowledge that the sample size may still be considered relatively small for a comprehensive assessment of these relationships. To further validate these findings, larger prospective studies with diverse populations are needed to improve the predictive utility and generalizability of our findings.

Although our LASSO and factor analysis indicated that CGM-derived measures were strong predictors of %NC, this does not mean that other clinical parameters, such as lipids and blood pressure, are irrelevant in T2DM complications. Our study specifically focused on characterizing glucose dynamics, and we analyzed individuals with well-controlled serum cholesterol and blood pressure to reduce confounding effects. While we anticipate that inclusion of a more diverse population would not alter our primary findings regarding glucose dynamics, it is likely that a broader data set would reveal additional predictive contributions from lipid and blood pressure parameters.

(4) CGM-derived indices like AC_Var and ADRR may be too complex for routine clinical use without simplified models or guidelines.

We appreciate the reviewer’s concern about the complexity of CGM-derived indices such as AC_Var and ADRR for routine clinical use. We acknowledge that for these indices to be of practical use, they must be both interpretable and easily accessible to healthcare providers.

To address this concern, we have developed an easy-to-use web application that automatically calculates these measures, including AC_Var, mean glucose levels, and glucose variability. This tool eliminates the need for manual calculations, making these indices more practical for clinical implementation.

Regarding interpretability, we acknowledge that establishing specific clinical guidelines would enhance the practical utility of these measures. For example, defining a cut-off value for AC_Var above which the risk of diabetes complications increases significantly would provide clearer clinical guidance. However, given our current sample size limitations and our predefined objective of investigating correlations among indices, we have taken a conservative approach by focusing on the correlation between AC_Var and %NC rather than establishing definitive cutoffs. This approach intentionally avoids problematic statistical practices like p-hacking. It is not realistic to expect a single study to accomplish everything from proposing a new concept to conducting large-scale clinical trials to establishing clinical guidelines. Establishing clinical guidelines typically requires the accumulation of multiple studies over many years. Recognizing this reality, we have been careful in our manuscript to make modest claims about the discovery of new “correlations” rather than exaggerated claims about immediate routine clinical use.

To address this limitation, we conducted a large follow-up study of over 8,000 individuals in the next study (Sugimoto, Hikaru, et al. “Stratification of individuals without prior diagnosis of diabetes using continuous glucose monitoring” medRxiv (2025)), which proposed clinically relevant cutoffs and reference ranges for AC_Var and other CGM-derived indices. As this large study was beyond the scope of the present manuscript due to differences in primary objectives and analytical approaches, it was not included in this paper; however, by integrating automated calculation tools with clear clinical thresholds, we expect to make these measures more accessible for clinical use.

We will add the following text to the Discussion section to address these considerations:

While CGM-derived indices such as AC_Var and ADRR hold promise for CAD risk assessment, their complexity may present challenges for routine clinical implementation. To improve usability, we have developed a web-based calculator that automates these calculations. However, the definition of clinically relevant thresholds and reference ranges requires further validation in larger cohorts.

(5) The study does not compare CGM-derived indices to existing advanced CAD risk models, limiting the ability to assess their true predictive superiority.

We appreciate the reviewer’s comment regarding the comparison of CGM-derived indices with existing CAD risk models. Given that our study population consisted of individuals with well-controlled total cholesterol and blood pressure levels, a direct comparison with the Framingham Risk Score for Hard Coronary Heart Disease (Wilson, Peter WF, et al. “Prediction of coronary heart disease using risk factor categories.” Circulation 97.18 (1998): 1837-1847.) may introduce inherent bias, as these factors are key components of the score.

Nevertheless, to further assess the predictive value of the CGM-derived indices, we performed additional analyses using linear regression to predict %NC. Using the Framingham Risk Score, we obtained an R² of 0.04 and an Akaike Information Criterion (AIC) of 330. In contrast, our proposed model incorporating the three glycemic parameters - CGM_Mean, CGM_Std, and AC_Var - achieved a significantly improved R² of 0.36 and a lower AIC of 321, indicating superior predictive accuracy.

We will add the following text to the Result section:

The regression model including CGM_Mean, CGM_Std and AC_Var to predict %NC achieved an R² of 0.36 and an Akaike Information Criterion (AIC) of 321. Each of these indices showed statistically significant independent positive correlations with %NC. In contrast, the model using conventional glycemic markers (FBG, HbA1c, and PG120) yielded an R² of only 0.05 and an AIC of 340. Similarly, the model using the Framingham Risk Score for Hard Coronary Heart Disease (Wilson et al., 1998) showed limited predictive value, with an R² of 0.04 and an AIC of 330.

(6) Varying CGM sampling intervals (5-minute vs. 15-minute) were not thoroughly analyzed for impact on results.

We appreciate the reviewer’s comment regarding the potential impact of different CGM sampling intervals on our results. To assess the robustness of our findings across different sampling frequencies, we performed a down sampling analysis by converting our 5-minute interval data to 15-minute intervals. The AC_Var value calculated from 15-minute intervals was significantly correlated with that calculated from 5-minute intervals (R = 0.99, 95% CI: 0.97-1.00). Furthermore, the regression model using CGM_Mean, CGM_Std, and AC_Var from 15-minute intervals to predict %NC achieved an R² of 0.36 and an AIC of 321, identical to the model using 5-minute intervals. These results indicate that our results are robust to variations in CGM sampling frequency.

We will add this analysis to the Result section:

The AC_Var value calculated from 15-minute intervals was significantly correlated with that calculated from 5-minute intervals (R = 0.99, 95% CI: 0.97-1.00). Consequently, the regression model including CGM_Mean, CGM_Std and AC_Var from 15-minute intervals to predict %NC achieved an R² of 0.36 and an AIC of 321.

Reviewer #3 (Public review):

Summary:

This is a retrospective analysis of 53 individuals over 26 features (12 clinical phenotypes, 12 CGM features, and 2 autocorrelation features) to examine which features were most informative in predicting percent necrotic core (%NC) as a parameter for coronary plaque vulnerability. Multiple regression analysis demonstrated a better ability to predict %NC from 3 selected CGM-derived features than 3 selected clinical phenotypes. LASSO regularization and partial least squares (PLS) with VIP scores were used to identify 4 CGM features that most contribute to the precision of %NC. Using factor analysis they identify 3 components that have CGM-related features: value (relating to the value of blood glucose), variability (relating to glucose variability), and autocorrelation (composed of the two autocorrelation features). These three groupings appeared in the 3 validation cohorts and when performing hierarchical clustering. To demonstrate how these three features change, a simulation was created to allow the user to examine these features under different conditions.

We appreciate reviewer #3 for the valuable and constructive comments on our manuscript.

Review:

The goal of this study was to identify CGM features that relate to %NC. Through multiple feature selection methods, they arrive at 3 components: value, variability, and autocorrelation. While the feature list is highly correlated, the authors take steps to ensure feature selection is robust. There is a lack of clarity of what each component (value, variability, and autocorrelation) includes as while similar CGM indices fall within each component, there appear to be some indices that appear as relevant to value in one dataset and to variability in the validation.

We appreciate the reviewer’s comment regarding the classification of CGM-derived measures into the three components: value, variability, and autocorrelation. As the reviewer correctly points out, some measures may load differently between the value and variability components in different datasets. However, we believe that this variability reflects the inherent mathematical properties of these measures rather than a limitation of our study.

For example, the HBGI clusters differently across datasets due to its dependence on the number of glucose readings above a threshold. In populations where mean glucose levels are predominantly below this threshold, the HBGI is more sensitive to glucose variability (Fig. S7A). Conversely, in populations with a wider range of mean glucose levels, HBGI correlates more strongly with mean glucose levels (Fig. 3A). This context-dependent behavior is expected given the mathematical properties of these measures and does not indicate an inconsistency in our classification approach.

Importantly, our main findings remain robust: CGM-derived measures systematically fall into three components-value, variability, and autocorrelation. Traditional CGM-derived measures primarily reflect either value or variability, and this categorization is consistently observed across datasets. While specific indices such as HBGI may shift classification depending on population characteristics, the overall structure of CGM data remains stable.

To address these considerations, we will add the following text to the Discussion section:

Some indices, such as HBGI, showed variation in classification across datasets, with some populations showing higher factor loadings in the “value” component and others in the “variability” component. This variation occurs because HBGI calculations depend on the number of glucose readings above a threshold. In populations where mean glucose levels are predominantly below this threshold, the HBGI is more sensitive to glucose variability (Fig. S7A). Conversely, in populations with a wider range of mean glucose levels, the HBGI correlates more strongly with mean glucose levels (Fig. 3A). Despite these differences, our validation analyses confirm that CGM-derived indices consistently cluster into three components: value, variability, and autocorrelation.

We are sceptical about statements of significance without documentation of p-values.

We appreciate the reviewer’s concern regarding statistical significance and the documentation of p values.

First, given the multiple comparisons in our study, we used q values rather than p values, as shown in Figure S1. Q values provide a more rigorous statistical framework for controlling the false discovery rate in multiple testing scenarios, thereby reducing the likelihood of false positives.

Second, our statistical reporting follows established guidelines, including those of the New England Journal of Medicine (Harrington, David, et al. “New guidelines for statistical reporting in the journal.” New England Journal of Medicine 381.3 (2019): 285-286.), which recommend that “reporting of exploratory end points should be limited to point estimates of effects with 95% confidence intervals” and that “replace p values with estimates of effects or association and 95% confidence intervals”. According to these guidelines, p values should not be reported in this type of study. We determined significance based on whether these 95% confidence intervals excluded zero - a statistical method for determining whether an association is significantly different from zero (Tan, Sze Huey, and Say Beng Tan. "The correct interpretation of confidence intervals." Proceedings of Singapore Healthcare 19.3 (2010): 276-278.).

For the sake of transparency, we provide p values for readers who may be interested, although we emphasize that they should not be the basis for interpretation, as discussed in the referenced guidelines. Specifically, in Figure 1, the p values for CGM_Mean, CGM_Std, and AC_Var were 0.02, 0.02, and <0.01, respectively, while those for FBG, HbA1c, and PG120 were 0.83, 0.91, and 0.25, respectively. In Figure 3C, the p values for factors 1–5 were 0.03, 0.03, 0.03, 0.24, and 0.87, respectively, and in Figure S10B, the p values for factors 1–3 were <0.01, <0.01, and 0.20, respectively.

We appreciate the opportunity to clarify our statistical methodology and are happy to provide additional details if needed.

While hesitations remain, the ability of these authors to find groupings of these many CGM metrics in relation to %NC is of interest. The believability of the associations is impeded by an obtuse presentation of the results with core data (i.e. correlation plots between CGM metrics and %NC) buried in the supplement while main figures contain plots of numerical estimates from models which would be more usefully presented in supplementary tables.