Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

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

We thank the reviewer for this important point. We agree that our experimental conditions do not fully recapitulate the in vivo architecture of either breast or bronchial epithelia. As the reviewer points out, the two cell lines need typical culture conditions to grow in an in-vivo like architecture, such as acinar structures for mammary tissue, and a pseudostratified architecture for the bronchial tissue, and it certainly would be interesting to subject the cell lines in these organotypic architectures and study the fate of oncogenic mutant cells. However, this would be an independent study on its own and is out of the scope of the current manuscript. Here, we intend to compare these two well-established epithelial lines from mammary and bronchial epithelial tissues, with distinct intrinsic mechanical and organisational properties, in minimal culture conditions, and study how just the context of having two different sources of epithelial cells can change the fate of oncogenic cells present in the wild-type population. We have now also performed experiments with the MDCK cell line, which is not like the BEAS2B line, and has well-defined cell-cell adhesions [Supplementary figure. 4a], and epithelial morphology, and shown that the fate of HRasV¹² mutants is different here as well, as compared to the MCF10A cell line.

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

We agree with the reviewer and in line with this suggestion, we have repeated the key experiments using Madin-Darby Canine Kidney (MDCK) cells, a well-established model epithelial cell line. Our results show that even though MDCK cells show significantly distinct properties compared to BEAS2B cells (MDCK being more epithelial like than BEAS2B), the dynamics of the HRasV¹² clusters in both these systems are similar [Supplementary figure. 4b], and distinctly different from the mammary epithelial cells (MCF10A). We did not observe the formation of an actin belt around HRasV¹² clusters in MDCK monolayers, which indeed forms in MCF10A monolayers. Additionally, in MDCK cells, the HRasV¹² mutant clusters are not under compaction or jamming, instead, they form protrusions similar to the ones seen in BEAS2B monolayers. These results solidify our hypothesis of tissue-specific differences in the mechanics of cancer initiation.

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

We thank the reviewer for this insightful comment. As correctly noted, Brodland’s 2002 work provided a foundational formulation of the Differential Interfacial Tension Hypothesis (DITH), which frames tissue organization in terms of effective interfacial tensions.

While in its original form, DITH emphasised segregation as a consequence of global differences in the intrinsic (bulk) tensions of juxtaposed tissues, our results specifically show that segregation is determined by local interfacial mechanics between transformed- and host cells. These local interfacial dynamics, however, is related to global contractility of cells- From our experiments with blebbistatin, we have observed a loss in the efficiency of segregation upon reducing global contractility, consequently inhibiting the formation of the interfacial actomyosin belt, which serves as the source of the interfacial tension between healthy and mutant populations. Therefore, the differences in local interfacial mechanics stem from intrinsic global contractility of cells in discussion here.

We have also clarified this distinction more clearly in the discussion and have explicitly stated that while DITH provided the foundation for conceptualizing tissue mechanics, our findings on transformed cell- healthy cell interactions specifically demonstrate that a higher efficiency of segregation is driven by high heterotypic interfacial tension at the tissue boundary.

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

We agree that a detailed visualisation of actomyosin distribution would strengthen our conclusions. We have now added a few more images of the interface to the Supplementary Data [Supplementary figure. 5], which show that cortical actin accumulates in individual cells, at the wild type cell-mutant cell interface, and actin levels go up in both wild type and mutant populations at the interface. This is also clear from the quantifications of different region of interests [Figure 2e], which is done by segmenting individual cells in these regions and quantifying actin intensity in each cell.

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

We thank the reviewer for raising this important point. While a direct experimental dissection of how HRasV¹² mutation affects actin levels in BEAS2B and MCF10A cells individually is beyond the scope of the present study, we do not rule out the possibility that a HRasV¹² mutation may exert cell-type-specific biochemical effects on actin regulation in these two epithelial systems.

Although the difference in actin between the mutants and the wild-type cells has not been incorporated into the model presented in the manuscript, we have now shown how actin levels change in response to the interfacial tension formed between the mutant and wildtype cells by adding a mechanochemical feedback to the model. Rather than prescribing intrinsic differences in actin levels between mutant and wild-type cells, we asked whether the feedback between the actin cytoskeleton and mechanical stress alone is sufficient to generate the observed actin reorganization. To address this, we incorporate a mechanochemical feedback loop (MCFL-I), originally developed in our earlier work [35], into the vertex model framework. This feedback captures the experimentally observed coupling between cell shape, actomyosin organization, and mechanical stress (i.e., heterotypic interfacial tension), and has previously been shown to reproduce biologically realistic epithelial behaviours such as dynamic cell shapes and heterogeneous actomyosin distributions [35].

In this framework, actin is not introduced as an explicit or intrinsic variable. Instead, changes in actomyosin organization emerge dynamically in response to mechanical stresses. Specifically, MCFL-I allows the preferred area and preferred perimeter of cells to evolve depending on cell shape and actomyosin binding, rather than remaining fixed. From these evolving parameters, we compute the normalized contractility, , which we interpret as a proxy for bulk actin, and normalized line tension which we interpret as a proxy for junctional actin. These normalized quantities provide size-independent measures of actomyosin organization across the tissue. 

The equations for MCFL-I can be written as:

Thus, with MCFLs, the vertex model does not have fixed 𝐴₀ and 𝑃₀. The cells dynamically change these parameters depending on the vertex model dynamics. The constitutive relations for the and are given below [1]:

Here, is the fraction of myosin bound to actin as a function of cell area 𝐴. This nonlinear dependence arises from the load or strain-dependent binding of myosin to actin, and is a model parameter which is proportional to the binding affinity of myosin to actin in the absence of any strain. We consider to the be the same for both mutant and wild-type . Importantly, both mutant and wild-type cells obey identical mechanochemical rules in the model. Differences in actin organization arise solely due to differences in mechanical stress generated by differential interfacial tension. Positive differential interfacial tension compresses mutant cells within clusters. This will lead to different and P<sub>0>/sub> across the monolayer via MCFL-I, and thus reduced bulk actin and increased junctional actin [Appendix figure. 4], consistent with experimental observations. Conversely, when differential interfacial tension is weak or negative, mutant and wild-type cells experience similar stresses, and the model predicts minimal differences in actin organization [Appendix figure. 5].

Thus, while HRasV¹²-dependent biochemical effects may indeed differ between BEAS2B and MCF10A cells, our results demonstrate that mechanical interactions at mutant– wild-type interfaces are sufficient to generate distinct actin signatures in the two tissues, without invoking cell-type-specific actin regulation. We have added the details of the mechanochemical feedback loop in the model to the Appendix to emphasize that the model tests the sufficiency of mechanics-driven actin reorganization rather than excluding additional biochemical contributions. 

Although it looks that even for Λ > 0 we see that the normalized line tension seems to be negative. This is however just an artefact of the colorbar limits we have used to compare with the Λ < 0 case. If we plot with different colorbar limits, we see that the interface has as shown in Author response image 1.

Author response image 1.

Reviewer #2 (Public review):

(1) It is unclear what the mechanistic origin of the shape-tension coupling is, which is used in the vertex model, and how important that coupling is for the presented results. The authors claim that the shape-tension coupling is due to the anisotropic distribution of stress fibers when cells are under external stress. It is unclear why the stress fibers should affect an effective line tension on the cell boundaries and why the stress fibers should be sensitive to the magnitude of the internal isotropic cell pressure. In experiments, it makes sense that stress fibers form when cells are stretched. Similar stress fibers form when the cytoskeleton or polymer networks are stretched. It is unclear why the stress fibers should be sensitive to the magnitude of internal isotropic cell pressure. If all the surrounding cells have the same internal pressure, then the cell would not be significantly deformed due to that pressure, and stress fibers would not form. The authors should better justify the use of the shape-tension coupling in the model and also present simulation results without that coupling. I expect that most of the observed behavior is already captured by the differential tension, even if there is no shape-tension coupling.

The reviewer is correct in stating that most of the observed behaviour is already captured by the differential tension, without the shape-tension coupling. However, the shape tension coupling has been used here in accordance with the experimental observation that the cells at the interface are aligned and elongated along the interface [Fig. 2h], which can not be captured without the shape-tension coupling. The difference between shape indices of cells at the interface and away from the boundary is plotted versus the interfacial tension in the case of no shape-tension coupling [Appendix figure 2]. The red dashed line represents the experimental value of the shape index difference. The blue line is the shape index difference between two randomly chosen groups of cells (half of the total number of cells in each group is taken). At zero line-tension, the difference in shape index between interface cells and cells away from the interface is same as that between randomly chosen groups of cells, which is expected since there should be no interface at zero line-tension. The no shape-tension data presented here are averaged over 19 seeds. Although the results without shape-tension coupling reaches experimental values at high enough differential tension [Appendix figure 3], a closer inspection of the simulation results show that the cells are just squeezed and are aligned perpendicular to the interface, which is contrary to what is seen in experiments [Fig. 2h].

Calculating the average of the absolute value of the dot product of the nematic director and the interface edge for simulations with and without shape-tension coupling [Appendix figure 3] clearly shows that with shape-tension coupling, the cells align and elongate along the interface as is seen in experiment, given by an interface dot product value > 0.5 at high enough line-tension values. Further, shape-tension coupling or biased edge tension has been used before to model for cell elongation during embryo elongation [45] and here we use it as an active line-tension force, which elongates cells along the interface, in addition to the differential tension which is passive. This additional quantification of the alignment and elongation of cells along the interface will be added to the Appendix.

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

The difference in shape indices between the interfacial and bulk cells in simulations has now been calculated over 11 different seed values. The observed differences in simulations, along with the standard deviations have been plotted in Figure 4b. This figure will be updated to include the standard deviations. The nonzero difference in shape index in the absence of differential line tension for low values of stress threshold is due to the shape-tension coupling acting even at low differential tension. Thus, a non-zero, sufficiently high value of the stress threshold is required in our model with shape-tension coupling. This has also been stated in section 4 of the paper. The importance of the shape-tension coupling has been stated in response to the previous point.

(3) The authors should also analyze the cell line tension data in simulations and make a comparison with experiments.

The line tension for each edge can be calculated as .

Although the line tension distributions look similar to the ones obtained from Bayesian Force Inference, a better comparison is between the normalized line tension and actin seen in experiment as we have discussed under point (4) asked by Reviewer 1.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) The authors claim that the negative tension Lambda<0 resembles the Beas2b phenotype. This is not consistent with the expression of actin in Figure 2f, which seems very similar in all four regions of interest (ROIs). Also, the segregation index data for Beas2b in Figure 1h looks very different from the demixing parameter in Figure 4f for the negative value of Lambda.

In the model presented in the previous version of the manuscript, actin differences have not been incorporated. We have only added an interfacial line tension, which might arise only at the interface between cells. In response to comment (4) from Reviewer 1, we have considered a vertex model with mechanochemical feedback and interfacial line tension to understand how actin distribution in the tissue is affected by interfacial tension. The results presented match very well with experimental images.

The reviewer has rightly pointed out that the segregation index (SI) data presented in Fig. 1h have a different trend compared to those in Fig. 4f. However, it is essential to note that in the simulation, the initial condition is one in which the mutant cluster is already fully segregated, and thus, at the initial time point. This is not the case in experiments, and at initial time points. Thus, the two plots are not directly comparable and only show how SI changes in our simulations. It is more effective to compare the final time points in Fig. 2f with those in Fig. 4e, where we observe that Mcf10a has a higher SI compared to Beas2b, and the case with Λ > 0 has a higher SI than the case with Λ < 0. This supports our claim that Λ < 0 resembles the Beas2b phenotype and Λ > 0 resembles the Mcf10a phenotype.

(2) It is unclear how the threshold pressure Pi_0 is implemented for the shape-tension coupling in the vertex model. Is the value of the additional tension gamma_ij equal to 0 if the internal pressure is below that threshold?

The stress threshold is implemented for the shape-tension in the vertex model in the following way. The line tension forces can be written as:

where, and . If the stress on the cell is below the threshold, then for those cells.

(3) In vertex model simulations, the authors use identical parameters for wild-type and mutant cells. This does not seem to be consistent with experimental observations in Figure 2, where the expression of actin is different, and also, cell shape indices are different for the wild-type and mutant cells. The authors should comment on how that choice affects their simulation results.

We thank the reviewer for this comment. As noted in our response to comment 4 from  reviewer 1, we have now attempted our simulations after adding a mechanochemical feedback to the model. Here, both wild-type and mutant cells follow identical mechanochemical rules within the vertex model. This choice does not imply that the cells are mechanically identical in the tissue; rather, it allows us to test whether differences in cell shape and actin organization can emerge purely from mechanical interactions.

By incorporating the mechanochemical feedback loop (MCFL-I), the model captures how heterotypic interfacial tension redistributes mechanical stresses between mutant and wild-type cells. These stresses lead to differences in cell area, perimeter, and shape, which are then translated via MCFL-I into distinct bulk and junctional actin signatures. Consequently, even though the intrinsic parameters are the same, the emergent mechanical environment reproduces the experimentally observed differences in actin intensity and cell shape indices (as shown in Figure 2).

Thus, our approach demonstrates that the experimentally observed heterogeneity between mutant and wild-type cells can arise solely from interface-driven mechanical effects, without prescribing any cell-type-specific parameters in the model.

(4) Also provide data for cell line tensions in the vertex model, which can then be compared with the experimental data in Figure 2. This is especially important because the differential cell line tension at the interface of mutants and wild-type cells seems to be playing a very important role.

The cell tensions from the vertex model have been plotted in the response to main comment (3) from Reviewer 2. Since the interfacial tension has been included as an extra term in the vertex model by hand, it is not trivial to simply compare the line tensions from the vertex model to the experimental data. However, we can understand how the tensions are by looking at the normalised tension and normalised contractility plotted as a response to comment (4) from Reviewer 1. Those plots are from a vertex model with mechanochemical feedback and the plots match well with experimental actin images.

(5) In Figure 2j, the authors should report the relative cell pressure and line tension for all four ROIs. The data is only shown for the wild-type cells and for mutants in clusters, even though the figure caption states that the data is presented for all four ROIs. It would also be useful to report the cell tension at the interface between the mutant cells and wild-type cells since this is the key parameter for the vertex model simulations.

We agree and have updated the graph [Figure 2j].

(6) The tangential motion of cells around oncogenic clusters only shows up towards the end of Supplementary Video 3. It is unclear whether this is a transient effect or whether this tangential motion would persist for a longer time.

We thank the reviewer for raising this point. In our experiments, tangential cell motion in the wild type population along the boundary of oncogenic cluster consistently emerges as the oncogenic cluster becomes compacted. We have plotted tangential velocity in interfacial wild type cells over time (Supplementary Fig. 6b), and show that such a motion persist at the cluster-wild-type interface, until the end of time-lapse recordings in all cases. 

(7) It is very awkward that the authors are representing an integral of the tangential velocity over different loops in Figures 3c and 4i. Thus, it is very hard to separate how much of the increase in the integrated velocity is due to larger loops and how much is due to changes in the average tangential velocity. Since different loops have different perimeters, it would have been better to report the average tangential velocity by dividing the integrated tangential velocity by the perimeter length of each loop. In the methods, the authors state that the concentric circles go from the center to a point twice the radius of the mutant cluster, but this is not consistent with the image in Figure 3c, where the concentric circles seem to go only to the boundary of the mutant cluster.

We thank the reviewer for raising the point regarding the dependence of the loop-integrated tangential velocity on the perimeter length. While the circulation (loop-integrated tangential velocity) indeed scales with loop size, it increases with radius only if tangential velocity components are directionally coherent along the loop.

In our data, concentric-loop analysis centered on mutant clusters reveals a systematic increase in tangential motion with radius, with the largest values occurring at the outermost loops corresponding to the cluster–tissue interface. In contrast, applying the identical analysis to randomly selected wild-type regions does not yield any monotonic increase with radius, despite the increasing perimeter of the loops, and instead shows fluctuations around zero. This control demonstrates that the observed increase around mutant clusters is not a trivial geometric consequence of larger loop size but reflects the emergence of coherent tangential motion specifically at the mutant cluster boundary.

To further address the reviewer’s concern, we additionally computed the mean tangential velocity by normalizing the loop-integrated tangential velocity by the loop perimeter. As shown in Supplementary figure. 6a, this normalization preserves the same qualitative trend: tangential motion peaks near the periphery of mutant clusters, whereas no such trend is observed in wild-type regions. We therefore conclude that both metrics capture the same physical phenomenon: enhanced tangential cell motion localized to the mutant cluster boundary, consistent with the behavior observed in the time-lapse videos.

Author response image 2.

From simulation data

(8) The authors should comment on how jamming and unjamming are related to shape indices because some readers may not be familiar with them.

We have updated the same in the text of Results 2.

(9) In the captions of Figure 3, the authors state that the bronchial epithelium gets kinetically arrested. This is not evident from the data in Figure 3d, where the velocity magnitude drops just a little bit for the bronchial epithelium, and it remains much higher compared to the mammary epithelium at long times.

We agree with this comment, and that using the word, kinetically arrested, for Beas2b cells is misleading, since their motion is much higher, even after the initial drop. We have updated the text in the caption accordingly.

(10) It is unclear why the authors have used the segregation index for analyzing experiments and the demixing parameter for analyzing simulations. Both parameters are trying to quantify the same thing, so it would have been better to use the same quantity for both experiments and simulations to enable easier comparison.

We agree that using the same quantity for both experiments and simulation would enable easier comparison. Thus, we have replaced the demixing parameter with segregation index in Figure 4. 

(11) It is unclear what experimental data were used for shape indices in Figure 4c. Was it the data from Mcf10a or Beas2b? It is also unclear which ROIs were used because different ROIs have very different shape indices in experiments, according to Figure 2e,f.

We have used the experimental ∆(𝑆ℎ𝑎𝑝𝑒 𝑖𝑛𝑑𝑒𝑥) = 0.75, which is a rough estimate of the difference between the shape indices for ROI 2 (interface), and ROI 1, ROI 3 and ROI 4 (away from interface) from Fig. 2 e for MCFL10a. 

(12) The authors find that the differences in shape indices are non-zero even for Lambda=0 for some threshold pressure parameters Pi_0 in Figure 4c. This should not happen because all the cells are identical in that case. This suggests that either there are not enough statistics from the simulations or that something is wrong with the simulations. How is this simulation data obtained? Is it from a single simulation, or is this averaged over a certain number of simulations? Authors should perform multiple simulations and report both the mean values and the standard deviation.

We have addressed this in the response under main comments (1) and (2) from Reviewer 2.

(13) It is unclear how the cell extrusion was simulated in the vertex model.

Extrusion probability calculation: Simulations with just a single mutant cell were run for a range of differential interfacial line tension values (Λ = 0, 0.1, 0.4, 0.8, 1.2, 1.6) with shape tension coupling. The simulation was run till the area of the mutant cell fell below a threshold area = 0.1, after which we consider the mutant cell to be extruded. 9 different random initial seeds were run and analysed. Each seed gives a binary result – either extruded or not. This was used to calculate the extrusion probability. We have added this section to the Appendix.

(14) The authors claim that HRas^V12 clusters in bronchial epithelium grew on top of one another, but it is not clear how this can be observed in Figure 2b or in any other Figure.

We thank the reviewer for raising this point. Our original statement that cells were growing on top of each other was based on observations from the Z-stack images, which allowed us to resolve cell positions along the apico–basal axis. However, since these Zstack data are not included in the current manuscript, we agree that this claim cannot be directly supported by the figures shown. We have therefore removed this statement from the text and restricted our conclusions to what is directly supported by the presented data.

(15) In the main text, the authors state that bronchial epithelial cells exhibited higher F-actin intensities compared to mammary bronchial cells, but this difference is not statistically significant according to Figure 5e.

We agree with the reviewer and have thus changed the text because even though the Factin intensities seemed higher in bronchial epithelium visually, the difference was not statistically significant.

(16) The definition of eccentricity is incorrect in the text. The authors state that the eccentricity is quantified as the ratio of the length of the minor axis to the major axis of an ellipse. According to this definition, the eccentricity would be 1 for a circle and not 0.

We have updated the definition of eccentricity in the text to the correct one, including the correct equation.

(17) It is unclear whether the active force F_act is used in the vertex model simulations. The active force is defined, but then its value is never specified. Note that the motility force is also an active force, so it is unclear why the motility and active forces were separated.

In our model, the line tension force arising from the shape tension coupling is the active force. We agree that the motility force is also an active force, however, in the absence of any directional movement for instance, the homeostatic tissues in discussion here, we have discounted the role of motility force in our mode, presented here. 

(18) The authors use inconsistent naming for different types of epithelia throughout the manuscript. Mcf10a cells are referred to as either mammary epithelium or breast epithelium, and Beas2b cells are referred to as either lung epithelium or bronchial epithelium. Because of the very broad spectrum of journal readers, it may not be obvious to all readers that different names refer to the same cell types.

We have updated the text to keep the naming consistent throughout.

(19) Many references to individual figure panels in the main text are incorrect. The authors should carefully check all the references to figures.

We apologize for these errors. We have updated the incorrect references after carefully reviewing the entire manuscript.

(20) In Figure 5, panel b is incorrectly labeled as d.

We have corrected the same.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The aim of this work is to directly image collagen in tissue using a new MRI method with positive contrast. The work presents a new MRI method that allows very short, powerful radio frequency (RF) pulses and very short switching times between transmission and reception of radio frequency signals.

Strengths:

The experiments with and without the removal of 1H hydrogen, which is not firmly bound to collagen, on tissue samples from tendons and bones, are very well suited to prove the detection of direct hydrogen signals from collagen. The new method has great potential value in medicine, as it allows for better investigation of ageing processes and many degenerative diseases in which functional tissue is replaced by connective tissue (collagen).

Weaknesses:

It is clear that, due to the relatively long time intervals between RF excitation and signal readout, standard hardware in whole-body MRI systems can only be used to examine surrounding water and not hydrogen bound to collagen molecules.

We agree that this is a regrettable situation (see also Discussion section). We are hoping that current and future efforts of MRI manufacturers towards improved hardware will eventually enable the technique for broader application.

Reviewer #2 (Public review):

Summary:

This work presents direct magnetic resonance imaging (MRI) of collagen, which is not possible with conventional MRI or other tomographic imaging modalities.

Strengths:

The experimental work is impressive, and the presentation of results is clear and convincing. Through a series of thoughtfully prepared experiments, I found the evidence that the images reflect direct measurements of collagen to be highly compelling.

Due to the technical demands, direct collagen imaging is unlikely to become widespread for routine clinical work, at least not anytime soon. That said, this work is nonetheless transformative and will likely be highly significant for research and perhaps clinical trials.

Reviewer #3 (Public review):

The paper is well written and well presented. The topic is important, and its significance is explained succinctly and accurately. I am only capable of reviewing the clinical aspects of this work, which is very largely technical in nature. Several clinical points are worth considering:

(1) Tendons typically display large magic angle effects as a result of their highly ordered collagen structure (cortical bone much less so), and so it would have been of interest to know what orientation the tendons had to B 0 (in vitro and in vivo). This could affect the signal level at the longer echo time and thus the signal on the subtracted images.

We have added arrows in the images showing the direction of the main magnetic field. For the in vivo case, the subject lay in the superman position, with B0 pointing from the hand towards the shoulder.

(2) The in vivo transverse image looks about mid-forearm, where tendons are not prominent. A transverse image of the lower forearm, where there is an abundance of tendons, might have been preferable.

We have added a distal view of the forearm, where more tendon structures are observed.

(3) The in vivo images show the interosseous membrane as a high signal on both the shorter and longer TE images. The structure contains ordered collagen with fibres at different oblique angles to the radius and ulnar, and thus potentially to B 0. Collagen fibres may have been at an orientation towards the magic angle, and this may account for the high signal on the longer TE image and the low signal on the subtracted image.

This is certainly an interesting take. While the magic angle effect is well established for collagen bound water, the orientation effects on the macromolecular collagen signal are still to be investigated. Our initial experiences so far suggest that the direct collagen signal is not as sensitive to orientation as the bound water.  

Regarding the described observation for the interosseous membrane, we expect the high signal coming from collagen-bound water (yet not quite at the magic angle), which hardly decays between the two TEs, as their difference is small as compared to the T2* of this signal. Hence, this signal is removed in the subtraction image, and only the macromolecular collagen signal remains, which appears to be very low. Working with samples of the interosseus membrane may provide further insights into why this is the case.

(4) Some of the signals attributed to the muscle may be from an attachment of the muscle to the aponeurosis.

We have added the aponeurosis as a possible signal contributor in the muscle tissue.

(5) There is significant collagen in subcutaneous tissues, so the designation "skin" may more correctly be "skin and subcutaneous tissue".

We have updated the label accordingly.

(6) Cortical bone is very heterogeneous, with boundaries between hard bone and soft tissue with significant susceptibility differences between the two across a small distance. This might be another mechanism for ultrashort T 2 * tissue values in addition to the presence of collagen. The two effects might be distinguished by also including a longer TE spin echo acquisition.

Solid cortical bone may also have an ultrashort T 2 * in its own right.

The described effect is clearly of importance for bone water but plays a negligible effect for the macromolecular signal. We would like to support this by a brief, coarse estimation. 𝑇₂* can be approximated by 1/𝑇₂* = 1/𝑇₂ + 1⁄𝑇₂′, where 1⁄𝑇₂′ \= 𝛾∆𝐵 = 𝛾∆𝜒𝐵₀ (Ref. 1).

The susceptibilty difference reported for the interface between bone and water is ∆𝜒 = 2.5 ppm (Refs. 2 and 3), which at 3T leads to a 𝑇₂′ ≈ 3000 𝜇𝑠. From our recorded FIDs, we use a 𝑇₂* of 10 μs and thus obtain 𝑇₂ \= 10.03 𝜇𝑠.

As can be seen, the change in the transverse relaxation constant due to susceptibility is negligible compared to the intrinsic decay of the macromolecular collagen signal. Notably, this is not the case for the pore water signal where T₂s are on the order of milliseconds (Ref. 2).

A footnote was added in the Introduction section regarding this topic.

(7) It may be worth noting that in disease T 2 * may be increased. As a result, the subtraction image may make abnormal tissue less obvious than normal tissue. Magic angle effects may also produce this appearance.

This is an important point regarding image interpretation. For this reason, it is advantageous that also the original anatomical images prior to subtraction are available, which will show such effects. They can be used in conjuction with the collagen-specific image to provide further insights regarding tissue disease. Increased T₂* of diseased tissue has so far been reported for the bound water components due to a reduction of dipolar interactions between bound water and collagen (Ref. 4). A potential related change in T₂ for the macromolecular collagen component itself is certainly of interest and an avenue to explore in future work.

(8) It may be worth distinguishing fibrous connective tissue (loose or dense), which may be normal or abnormal, from fibrosis, which is an abnormal accumulation of fibrous connective tissue in damaged tissue. Fibrosis typically has a longer T 2 initially and decreases its T 2 * over time. In places, the context suggests that fibrous connective tissue may be more appropriate than fibrosis.

We are aware of this important distinction. We therefore checked the manuscript for references to fibrosis, making sure that the meaning is as intended.

Overall, the paper appears very well constructed and describes thoughtful and important work.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) It should be stated that various methods with very short echo times (e.g. SWIFT by Garwood et al.) have been described in the past. This work shows for the first time that direct signals from collagen and be systematically detected in tissue samples.

We have expanded a sentence in the introduction and reference selected publications studying short-T₂ water signal in collagen, including SWIFT.

(2) It should be noted that the 1H atoms bound to collagen are located at different sites (at different amino acids of the protein) of the molecule and have different frequencies, and that further signal analyses are of interest.

We have included additional information regarding distinct resonances of proton-binding sites of collagen in the introduction. The discrete observation of such signals requires advanced NMR methodology such as magic-angle spinning and RF decoupling, which is not a suitable approach for in vivo MRI. Without such methods, the broad lineshapes overlap strongly and are rather observed as a single decaying exponential with the dipolar oscillation as we observe in the FIDs.

(3) Is it certain that the bump at 30 microseconds comes from 'dipolar coupling'? Is the development time probably too short for chemical shift-induced interference or J-coupling effects?

30 microseconds is an extremely short interval to accumulate phase and requires large resonance offsets to observe significant changes. To investigate the nature of the bump, we also collected data on a Bruker 7T NMR spectrometer (see Author response image 1). Overall the same signal characteristics are observed as with 3T. In particular, the position of the bump is the same, excluding chemical shift as as source. However, with the higher field strength, chemical shift becomes significant for the signal phase, as observed by the change in the phase behavior at 50 microseconds, when the collagen component has decayed.

While J-coupling is independent of field strength, the typical ranges are single-digit to tens of Hertz. In contrast, dipolar coupling interacts on the order of thousands of Hertz, which coincides with the values extracted from our signal model.

To clarify this point, we extended the respective sentence in the Results section.

Author response image 1.

(4) It should be noted that short RF pulses have a relatively high energy content, and whether there are any particular stresses on patients during the examination (SAR, nerve stimulation?).

SAR is an important issue in ZTE MRI. Since imaging bandwidths are large and excitation is performed with the imaging gradient being on, broadband pulses are necessary. Hence, significant RF deposition occurs and in vivo the flip angle can often not be optimized for the maximum signal, but will be limited by the SAR limit. We have added an explanation in the Discussion section.

Peripheral nerve stimulation is generated by rapid switching of strong gradients. However, ZTE sequences are usually operated without switching gradients on and off, but with only minor adjustments of the gradient direction between TR intervals. Therefore, PNS is not a relevant issue.

(5) In the Results section, Part B, 'substantial signal intensity' should be written instead of 'substantial image intensity'.

We have changed this as suggested.

References

(1) Chavhan GB, Babyn PS, Thomas B, Shroff MM, Haacke EM. Principles, techniques, and applications of T2*-based MR imaging and its special applications. Radiographics. 2009 Sep-Oct;29(5):1433-49. doi: 10.1148/rg.295095034. PMID: 19755604; PMCID: PMC2799958.

(2) Seifert, AC, Wehrli, SL, and Wehrli, FW (2015), Bi-component T₂* analysis of bound and pore bone water fractions fails at high field strengths. NMR Biomed., 28, 861– 872. doi: 10.1002/nbm.3305.

(3) Hopkins JA, Wehrli FW. Magnetic susceptibility measurement of insoluble solids by NMR: magnetic susceptibility of bone. Magn Reson Med. 1997 Apr;37(4):494-500. doi: 10.1002/mrm.1910370404. PMID: 9094070.

(4) Loegering IF, Denning SC, Johnson KM, Liu F, Lee KS, Thelen DG. Ultrashort echo time (UTE) imaging reveals a shift in bound water that is sensitive to sub-clinical tendinopathy in older adults. Skeletal Radiol. 2021 Jan;50(1):107-113. doi: 10.1007/s00256-020-03538-1. Epub 2020 Jul 8. PMID: 32642791; PMCID: PMC7677198.

Author response:

Public Reviews:

Reviewer #1 (Public review):

(1) Based on the effects observed with OC vs. Ntf3 cKO, it is unclear whether OC is indeed exerting its non-cell-autonomous effects via Ntf3. Knocking out both Ntf3 and OC and comparing the effects to those seen with just OC cKO alone could provide more insight on this point.

In this study, we did not intend to demonstrate that Onecut transcription factors exert their non-cell autonomous action on spinal interneuron development by regulating Ntf3 expression, and we do not state in the manuscript that this is the case. We only show that Onecut factors and Ntf3, the expression of which they regulate, contribute to the non-cell autonomous regulation of spinal interneuron development by the motor neurons. We are convinced that Onecut factors could regulate multiple independent factors and pathways involved in extrinsic regulation of interneuron development, as supported by the regulation of multiple secreted factor or membrane protein expression in motor neurons detected in the reported RNA-sequencing experiment (this manuscript and [1]). This possibly also includes, as demonstrated in cell culture for multiple homeoproteins including human Onecut factors [2], the intercellular transfer of the Onecut homeoproteins during spinal cord development, a process that we are currently investigating. Knocking out both OC and Ntf3 in the motor neurons, beyond being technically extremely challenging (1/64 probability to obtain triple-mutant embryos), would not enable to address this question, as it will simply results in the addition of two different defects.

Also, a quantitative summary of the effects of Ntf3 overexpression in motor neurons in the chick is lacking.

A quantitative summary of the effects of Ntf3 overexpression in the chicken embryonic spinal cord is provided in Figure S2.

(2) How the authors assess changes in the spatial distribution of interneurons is unclear. In Figures 2 and 4, the control distributions (despite reporting the same populations in the same regions) look different, suggesting large sample-to-sample variance in distribution. Although the authors report that several sections in each level were taken from at least three animals for each condition, it's unclear how variance within WT or cKO sections was accounted for in the final statistical evaluation. It seems at a glance that a comparison between control samples in Figure 2 and Figure 4 could report statistically significant differences, which would be problematic. A more rigorous report of sample-to-sample variance and a more in-depth explanation of the statistical methods are needed.

The experimental procedure to analyze the spatial distribution of spinal interneurons at different stages of development is described in details in the “Statistical analyses” paragraph of the Materials and Methods section of the manuscript, and has been repeatedly used by ourselves [3,4] and by others (see for example [5-7]) to conduct similar analyses.

We also noticed that the distribution of the different analyzed interneuron populations in the control embryos showed some differences between the cOc1Oc^2-/- and the cNtf3^-/- lines. Several parameters can account for this observation. First, this study has been conducted over a period of 15 years, different investigators each contributing to different steps of the analysis. Second, the genetic background of these two lines is not identical, impacting both the duration of the gestation (hence, the embryonic stage of the performed analyses, even if the embryos were collected on the same gestation day) and possibly the distribution of some interneuron populations. Third, because of evolutions in the availability of the primary antibodies used to label the interneuron populations of interest, the same antibodies were not used throughout the study, as stated in the Materials and Methods section, although the same antibody was used by the same investigator to label the same interneuron population in each mouse line at each developmental stage.

A detailed description of the number of sections and embryos included in each analysis as well as the whole statistical workflow that was used for the distribution analyses, which takes into account variance within control or mutant samples, will be provided in the revised version of the manuscript.

Reviewer #2 (Public review):

(1) The study primarily quantifies interneuron numbers and distribution at different levels of the spinal cord and under different genetic manipulations. Experimental details are lacking, defining how many sections were analyzed (several are noted in the methods) and how the rostrocaudal levels of the spinal cord were precisely aligned.

A detailed description of the number of sections and embryos included in each analysis as well as the whole statistical workflow that was used for the distribution analyses will be provided in the revised version of the manuscript. The rostrocaudal levels of the spinal cord were precisely aligned using the distribution of Foxp1 in the Lateral Motor Columns (LMCs) at brachial or lumbar levels of the spinal cord [8,9], which will also be indicated in the revised version.

In different figures, the values and distributions shown for controls vary quite a lot. For example, in Figure 2B vs Figure 4B, the number of FoxP2+ V1 neurons at brachial levels is ~350 vs 125. Similarly, the control distributions in 2I and 4I are quite different. This makes it challenging to determine whether the conclusions regarding the impact of each genetic manipulation on interneuron numbers and distribution are valid.

Multiple factors may explain these observations. First, this study spans a 15-year period, with different researchers contributing to various stages of the analysis. Second, the genetic backgrounds of the two mouse lines are not identical, affecting both gestation length (thus influencing the embryonic stage at which analyses were performed, even when embryos were collected on the same gestational day) and potentially the distribution of certain interneuron populations. Third, due to changes in the availability of primary antibodies used to label the targeted interneuron populations, the same antibodies were not consistently employed throughout the study as noted in the Materials and Methods section though each investigator used the same antibody for a given interneuron population and developmental stage within each mouse line.

(2) The relationship between OC and NT3 deletion data is not entirely clear. Both deletions presumably lead to changes in interneuron distribution, but is there any reverse relationship between the two that relates to relative changes in NT3 levels? The authors do not directly compare NT3 and OC KO IN distributions. Similarly, one might expect a decrease in interneuron numbers in OC mutants, which is only reported for V2c neurons. However, the image presented in Figure 2G shows an equal number of V2c INs in control and mutant.

This study was not designed to demonstrate that Onecut transcription factors influence spinal interneuron development in a non-cell-autonomous manner through Ntf3 regulation, nor do we claim this in the manuscript. Instead, we show that Onecut factors and Ntf3, whose expression they control contribute to the non-cell-autonomous regulation of spinal interneuron development by motor neurons. We believe Onecut factors may regulate multiple independent factors and pathways involved in the extrinsic control of interneuron development. For instance, as noted earlier [2], we observed intercellular transfer of Onecut homeoproteins during spinal cord development, suggesting alternative mechanisms for non-cell-autonomous regulation.

The two mouse lines studied here consist, on the one side, in a combination of OC inactivation and Ntf3 increased expression, and, on the other side, in Ntf3 inactivation. Therefore, a reverse relationship between the changes in interneuron distribution is not expected. Furthermore, gain-of-function and loss-of-function experiments in mouse models frequently generate phenotypes that are not inverse to each other [10-13].

(3) It is not clear that the behavioral phenotypes seen in the olig2-cre mediated deletion of NT3 can be attributed to changes in interneuron development. How about a role of NT3 in oligodendrocytes? There is a big gap between the embryonic changes shown here and behavior, with no in-between circuit-level changes in locomotor circuits shown.

We agree, the motor behavior changes that we recorded in Ntf3 conditional mutant mice are, as stated, “consistent with the hypothesis that Ntf3 produced by MNs is required to generate locomotor circuits with properly coordinated activity” but do not demonstrate a direct causal relationship. However, investigating the intrinsic activity of the spinal locomotor circuits, independently from, for example, oligodendrocyte contribution may prove to be extremely challenging and was beyond the scope of this study. In addition, to our best knowledge, Ntf3 has not been shown to be expressed in healthy oligodendrocytes in vivo, and TrkC has not been reported to be displayed by these cells in the same conditions.

A more restricted manipulation would be deleting TrkC from specific interneuron populations. Related to this, although TrkC is shown to be broadly expressed in ventral interneurons, it is not shown specifically to colocalize with any of the interneuron markers. The authors should validate that the receptor is expressed in the subsets that they are investigating.

We agree, investigating the consequences of inactivating the TrkC receptor in specific interneuron populations would be extremely informative. However, this experiment is also very challenging to perform, as most of the driver lines available to target spinal interneuron populations additionally target multiple neuronal populations outside of the spinal cord that are also involved in the control of movements and could therefore induce confounding effects on motor behavior analyses [14-20].

We thank the reviewer for suggesting to investigate in more details the interneuron populations that display TrkC receptors, this will be include in the revised version of the manuscript.

(4) The rationale for following up on NT3 seems to be the chick electroporation experiments; however, no changes in distribution are shown in those experiments, and only a very minor decrease in Chx10 interneurons. Shouldn't NT3 overexpression lead to substantial decreases in IN numbers according to the authors' model? The "data not shown", which presumably refers to distribution, would be important to show here, to further support this rationale.

Chicken spinal cord electroporation only enables to study spinal cord development in a limited time-window, given the high mortality rate observed after longer incubation. At the stage we collected the electroporated embryos for analyses, interneuron migration has barely been initiated, and distribution cannot be studied yet. Consistently, we are not aware of any report of interneuron distribution analysis in electroporated chicken embryonic spinal cord, as compared to mouse embryos [3-7].

(5) The idea that NT3 downregulation causes an increase in IN numbers is not intuitive. Also, considering the DTA experiments in Figure 1, showing that MN ablation leads to a decrease in several IN subtypes and no changes in V2a neurons. It would be helpful for the reader if the authors could synthesize their results in the discussion and reconcile their experimental findings.

We agree, this will be included in the revise version of the manuscript.

Reviewer #3 (Public review):

(1) The manuscript relies heavily on quantifying numbers and the spatial distribution of interneuron populations. However, these do not seem to be consistent in control animals across experiments, making it difficult to interpret any changes observed in genetic manipulations. Specifically, in Figures 2 and 4, the same markers are being used to quantify V1, V2a, V2b, and V2c interneurons in controls vs. OC (Figure 2) or Ntf3 (Figure 4) conditional knockouts, but the numbers of neurons and their distribution in control animals are variable between these two figures. For example, there seems to be a mean of >300 V1 neurons in E12.5 brachial sections of Fig. 2 controls, but this number is <150 in Fig. 4 controls. The cell distribution scoring is similarly variable between these controls without any explanation. The same is true for E14.5 controls used in Figure S1 vs. Figure S3.

We indeed observed variations in the quantifications and distributions of the analyzed interneuron populations in control embryos between the cOc1/Oc2^⁻/⁻ and cNtf3^⁻/⁻ lines. Several factors may explain this discrepancy. First, the study was carried out over 15 years, with different investigators contributing to distinct stages of the analysis—meaning interneuron distribution was not assessed by the same researchers in both lines. Second, the genetic backgrounds of the two lines differ, affecting gestation length (and thus the embryonic stage at analysis, even when embryos were collected on the same gestational day) as well as potentially altering the distribution of certain interneuron populations. Third, changes in the availability of primary antibodies targeting the interneuron populations of interest led to inconsistencies in antibody use across the study, as detailed in the Materials and Methods section. However, each investigator consistently used the same antibody for a given interneuron population and developmental stage within each mouse line.

(2) Neurotrophic factors generally promote neuronal survival. However, in this study, the loss of Ntf3 leads to increased numbers of interneurons. This finding is in disagreement with previous observations in slice cultures of spinal cords, as stated in the discussion. This discrepancy makes it even more important that the cell counts reported in the figures discussed above are robust.

Considering that neurotrophic factors only support neuronal survival would strongly neglect their important function in neuronal differentiation, which has been broadly demonstrated. Severe immunotoxic ablation of motor neurons or anti-serum blockade of Ntf3 activity severely depleted inhibitory, but not excitatory, interneurons in a highly apoptotic-prone organotypic culture model of embryonic rat spinal cord slices, which was rescued by Ntf3 in the first model [21]. Opposite results were obtained in vivo by other researchers using mouse models lacking almost all MNs due to the elimination of skeletal muscles, where the number of spinal INs remained unaffected [22,23]. Combined to our results, these in vivo observations suggest that Ntf-3 is involved in interneuron differentiation rather in their survival. Consistently, Ntf3 has been shown to promote neuronal differentiation [24].

(3) The claim that phenotypes are non-cell autonomously driven by motor neurons is not well supported. In Olig2-Cre conditional knockouts of Onecut and Ntf3, there is no confirmation that the loss of these factors is specific to motor neurons. Therefore, it cannot be ruled out that other cell populations may be mediating the phenotypes.

Combined conditional inactivation of Oc1 and Oc2 has been reported in [1]. Conditional inactivation of Ntf3 only impacts motor neurons as it is the only cell population in the ventral spinal cord wherein this factor is produced (this study and [25-27]). Furthermore, Olig2-Cre has been shown to be active in motor neurons and in V3 interneurons (see for example [10]), which, for this reason, have not been studied in the frame of this project as stated in the manuscript.

(4) The claim that interneuron development is regulated by OC control of Ntf3 expression in motor neurons is not well supported. The authors show that loss of OC1/2 leads to an increase in Ntf3 expression in motor neurons. If this pathway were controlling interneurons, loss of OC function and overexpression of Ntf3 would have the same phenotype, which is not the case. Additionally, it would also be expected that loss of OC function and loss of Ntf3 function would have inverse phenotypes, which is also not the case. The phenotypes from OC loss of function and Ntf3 loss of function seem distinct from one another. The authors state that too little and too much Ntf3 are both bad for interneuron development, but there is no data to support their claim that OC1/2 mutants have altered interneuron development because of higher Ntf3 expression.

This study was not aimed at proving that Onecut transcription factors mediate their non-cell-autonomous effects on spinal interneuron development through Ntf3 regulation, nor do we make this claim in the manuscript. Rather, we demonstrate that Onecut factors and Ntf3, whose expression they control—participate in the non-cell-autonomous regulation of spinal interneuron development by motor neurons. We propose that Onecut factors likely modulate multiple independent factors and pathways involved in the extrinsic regulation of interneuron development, as evidenced by the regulation of various secreted factors and membrane proteins in motor neurons observed in our RNA-sequencing data (this study and [1]). This may also involve intercellular transfer of Onecut homeoproteins during spinal cord development—a mechanism previously shown in cell culture for several homeoproteins, including human Onecut factors [2] and which we are currently exploring.

(5) It is not clear that interneurons being studied express the Ntf3 receptor TrkC, which makes it difficult to assess whether changes in Ntf3 signaling are directly responsible for the phenotype.

Immunofluorescence experiment in Figure 3C shows that TrkC receptor is present in cell populations surrounding motor neurons at e12.5, a stage where only the pre-motor interneuron populations reported in the manuscript are present. However, we thank the reviewer for suggesting to investigate in more details the interneuron populations that display TrkC receptors, this will be include in the revised version of the manuscript.

(6) While the behavioral phenotypes are consistent with Ntf3 playing a role in motor circuits, there is no evidence to suggest that Ntf3's influence on premotor interneurons being studied is driving or contributing to this phenotype, as discussed by the authors.

We acknowledge that the motor behavior changes observed in Ntf3 conditional mutant mice—as noted—are “consistent with the hypothesis that MN-derived Ntf3 is necessary for the formation of locomotor circuits with properly coordinated activity,” but they do not establish a direct causal link. However, analyzing the intrinsic activity of spinal locomotor circuits was beyond the scope of this study.

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Author response:

General Statements

We would like to extend our gratitude to all reviewers for their supportive feedback, which acknowledges our study as well performed and of interest to investigators studying muscle development and diseases and supporting a role for the fly model in testing potential human disease gene variants. We also thank the reviewers for their valuable critical comments. We carefully considered all of them and made additional experiments and suggested text amendments.

We believe these modifications substantially improve the quality of our results and enhance general interest of our work.

Point-by-point description of the revisions

Reviewer #1:

In this manuscript, Zmojdzian et al. provide an analysis of ryanodine receptor (RyR) expression and function in Drosophila. They also use CRISPR to engineer into flies a RyR variant of unknown significance (VUS) found in a human myopathy patient and demonstrate that it is likely a pathogenic mutation. From studies of RyR expression in embryonic and larval stages, and effects of RyR knockdown or overexpression in various muscle groups, the authors show that, in addition to its known actions in calcium-dependent excitation-contraction coupling, RyR promotes myogenesis during development.

The key conclusions of the paper are convincing. I do not have suggestions for necessary additional experimental work, and my comments are minor. One conclusion, that RyR dysfunction may be involved in aging, is stated in multiple places, sometimes speculatively but once very forcefully. The latter is in the final paragraph of the Discussion, which states RyR "plays an instrumental anti-aging role in differentiated striated muscle". This conclusion must be tempered, as even if RyR knockdown phenotypes resemble some of those seen in aging flies, the study does not examine aged flies, and there is no mechanistic analysis that might link the two. I assume the authors would prefer to modify that sentence than initiate work with aging flies to prove the assertion.

We thank the Reviewer for this comment and remove from the concluding sentence hypothetical anti-aging role of RyR. The modified sentence reads as follow:

“To conclude, we report functional analysis of dRyR, the sole fruit fly RyR gene and show that in addition to ensuring contractile properties of differentiated striated muscle it plays a key pro-myogenic role during muscle development.”

Finally, the use of CRISPR to test a VUS is excellent and suggests a good way for testing of additional RyR variants in the future.

Minor comments:

(1) Figure 1A: In the Introduction it is stated that non-mammalian vertebrates have two RyR genes, alpha and beta. In Fig. 1A, a single chicken and single frog gene are listed under names different than alpha or beta. The figure also focuses on RyR2 genes, yet the Introduction states that the non-mammalian vertebrate genes are homologous to RyR1 and RyR3 in mammals. The dichotomy between the text and the figure is confusing. Finally, the font used in Fig. 1A should be enlarged for better visibility.

To avoid the dichotomy we modified our sentence concerning the non-mammalian vertebrate RYR genes in the Introduction section. As indicated, there are two RYR genes in chicken and frog, with one that shares homology with vertebrate RYR2 and is represented in the phylogenetic tree (Fig. 1A).  As requested by the reviewer, to ensure better visibility we enlarged the font in the revised Fig. 1A.

(2) Figure 3G-I: IF to Kettin is used to reveal sarcomeres but is not mentioned in the text. This protein is not present in vertebrates (I believe) and may not be familiar to many readers. It should be described in the text when it is used.

We are grateful for reminding us to provide information about Kettin, which represents the Drosophila counterpart of Titin. The following information has been added to the text on page 9: “ …which in turn correlated with shortening of Kettin/D-Titin-labelled sarcomeres…”

(3) Figure S2: The panels are labelled E, F, G. They should be A-D, as is used in the text.

In the revised version of Fig. S2 panel labels were amended and the panel E view enlarged. We also provide an additional control context (C57>LacZ).

(4) The dRyR16 allele is used in Figure 5 and S4. It is described as a hypomorph in the text on page 12 but as a null in the legend to Figure 5. Do the authors actually mean "homozygous" in the legend? The difference should be clarified.

The dRyR¹⁶ allele has been previously described as hypomorph. Indeed, in the legend of Fig. 5 we by mistake describe it as a “null”. As suggested by the Reviewer we modify it to « homozygous ».

(5) The Met codon that is mutated in the variant studied in Figure S5 and Figure 6 is position 488 in humans. It is referred to that way in the fly version also. Is that true, the actual amino acid number is identical in humans and flies? In Figure S5B, it might be worth showing the primary amino acid sequence surrounding Met488 to reveal the degree of local conservation (beyond the orange domain in that panel).

To provide more information about the conservation we include to the revised Fig. S5 an alignment of amino acid sequence surrounding the human RYR1 4881 variant position, which corresponds to position 4971 in the Drosophila dRyR.

Author response image 1 shows a snapshot from a larger portion of alignment encompassing variant mutation showing a high amino acids conservation around the variant position:

Author response image 1.

(6) At least two references cited in the text are not listed in the References section (Hadiatullah et al. and Nishimura et al.).

We double check reference citation and two indicated positions are now listed in the References section.

Reviewer #1 (Significance):

The paper is significant in that RyR is known to be a critical protein in calcium-dependent excitationcontraction coupling but its role in developmental myogenesis is poorly studied. This study demonstrates that it is expressed during, and is important for, embryonic and larval myogenesis in the fly. RyR is also understudied in this valuable model organism, even though a P element-based mutant has been available since 2000. The mechanistic basis for the functional observations is not explored here but the work is well performed and will be of interest to investigators studying muscle development (my own field) and diseases caused by RyR mutations.

To reinforce mechanistic/functional side of our studies we include to the revised Fig.5 a new panel G showing promyogenic role of another major cellular calcium regulator, ER calcium pump SERCA. The Lms targeted RNAi knockdown of SERCA leads to affected myotube growth resulting in a thin muscle fiber phenotype. This indicates that both dRyR-regulated cytosolic and SERCA-regulated ER store calcium levels are required to promote muscle development.

Reviewer #2:

Summary:

This paper presents data using the Drosophila model to analyze the effects of a rare human mutation in the gene encoding the ryanodine receptor (ryr). The authors present a nice, comprehensive phylogenetic analysis that shows the Drosophila version of Ryr to be most similar to human RYR2 and that the known "hot spots" for mutations in RYR2 coincide with highly conserved regions of the Drosophila Ryr. They characterize the functional effects of ryr knockdown and overexpression on both adult heart function and larval body wall muscle. They identified embryonic ryr expression in association with actin-stained muscle precursor cells and provide beautiful stains, which clearly showed that embryonic muscle cell development was disrupted in ryr mutants. In support of these findings, KD of Calmodulin in larva (an Ryr inhibitor) phenocopied Ryr OE. They recreated a human variant of unknown function (RyR1 p.Met4881Ile ) in the conserved region of the fly gene and tested the effect on larval muscle. Their data suggested that this variant was likely deleterious as it negatively affected most muscle parameters. This work supports a role for the fly model in testing potential human disease gene variants.

Major comments:

(1) Fig, 1 In G there is no data for the RNAi KD situation.

We are grateful to the Reviewer for pointing this out. We initially didn’t include these data because of large difference in crawling capacities of dRyR RNAi larvae. In the revised version of Fig. 1 we provide now dRyR-RNAi larva crawling data. Because of their inefficient crawling, the time scale in panel 1G was modified.

(2) Fig. 2 Authors should include Diastolic Diameters; they mention dilated cardiomyopathy but don't show the dilation. The authors should also show staining in hearts with RYR OE and RNAi. It would be nice to have some kind of quantification of disorganized myofibrils.

As requested, in the revised Fig. 2 we provide diastolic diameter measures. We also include systolic interval graph to show a full picture of cardiac parameters. We do not observe all signs of dilated cardiomyopathy in dRyR-RNAi context as there is systolic diameter increase but no significant change in diastolic diameter.

We modify our comments in the text accordingly (page 7).

“…As the diastolic diameter remained unchanged, we conclude that cardiac dRyR knockdown affects cardiac performance without causing dilated cardiomyopathy…”

Regarding circular myofibrils pattern, we do not observe irregularity of myofibrils orientation but rather a fuzzy and less distinctive sarcomeric pattern that is difficult to quantify. We specify this in the figure 2 legend (page 8).

“…circular fibers in Hand>dRyR RNAi (E) context showed a fuzzy pattern suggesting an affected sarcomeric organisation…”

Author response image 2 shows the entire view of the cardiac tube in dRyRRNAi context (stained with phalloidin) in which in spite of less distinctive circular myofibrils no obvious differences with wt are observed.

Author response image 2.

(3) To evaluate and reproduce the data on the larva muscle parameters the authors should provide more details on how sarcomere length was quantified in each larva (replicates, ROI size, etc). Similarly, how were # of nuclei quantified / normalized? Importantly for these measurements, did the authors know what the contraction state of the muscles were when fixed?

We add the requested information to the Materials and Methods section:

“Muscle characteristics measurements:

All analyses of muscle length and sarcomere size were performed on fixed larval muscle preparations in a relaxed state. Acquired confocal images were analysed in Fiji using the line tool. Analyze – Measure tool was then applied to obtain muscle length values and measurements were analysed with Prism. Sarcomere size and number were calculated using Analyze – Plot profile Fiji tool. The sarcomere size was measured between peaks corresponding to Z-disc (revealed with Z-line specific marker) on approximatively 100 µm of muscle length. Sarcomere measurements were then analysed with Prism.

DAPI-stained nuclei were counted in Z-stacks of confocal views of VL3 larval muscle and data analysed with Prism. About 30 larval muscles from 6-8 larval filets were analysed for each measurement. »  Statistics

All statistical analyses were performed using Prism (v9.5.1, GraphPad, Software, La Jolla, CA, USA). The t test was used to compare control to variant context and one-way ANOVA tests were used for comparisons with more than two datasets. Bar plot represent the mean and the standard deviation. On the figures, statistical comparisons of sample vs control are indicated as ****: P ≤ 0.0001; ***: P ≤ 0.001; **: P ≤ 0.01; *: P ≤ 0.05; ns > 0.05.

(4) Fig. 3, Are RNAi and OE in the same background? I only see one control in the graphs for the RNAi line background.

We agree and to avoid potential bias between the RNAi versus OE genetic contexts we provide now in the revised version of Fig. 3 an additional OE control (C57>lacZ).

Thus, two controls, one for RNAi and one for OE contexts are now included.

(5) Fig. 3 How VL3 length was determined needs more detail, the Zhang ref is not adequate.

We are thanking the Reviewer for this comment and provide now more details about the method used to calculate VL3 length (new paragraph in Materials and Methods), see also our answer to point 3. Zhang et al. reference is in relation to the mitochondria pattern quantification.

(6) In order to be able to evaluate the data, the statistical tests used should be cited in the figure legends along with what *, ** ,*** stand for (or just provide p values).

We add now the information about the statistical tests to the Fig legends in addition to the specific paragraph in Materials and Methods section (answer to point 3).

Minor comments:

(1) Need more detail in the figures, e.g. add what colors go with which stain to the picture.

We provide this information in the revised version of the figure legends

(2) Page 13, (Fig. ?F, G).

We apologize for this mistake and add the number - Fig. 5

(3) Fig. 4 "partially co-localizing with actin".... this is confusing and probably an overstatement based on the staining pattern in a whole embryo and not on an optical section or a higher power image with a more restricted field of view.

We agree and remove this statement from the Fig.4 legend.

(4) Some of the graphs are a bit small, recommend reducing the statistical comparison brackets to straight lines, which eliminates a lot of white space and would allow the graphs to be enlarged.

We increased the size of graphs in revised Fig. S2 and Fig.5.

Reviewer #2 (Significance):

The authors nicely characterized the role of Ryr in muscle development and function and recreated a human variant of unknown function (RyR1 p.Met4881Ile ) in the conserved region of the fly gene. Their data suggested that this variant was likely deleterious as it negatively affected most muscle parameters. This work supports a role for the fly model in testing potential human disease gene variants. The reviewers field of expertise is in Drosophila genetics and in the use of the fly as a model system for understanding the genetic networks contributing to muscle structure and function at the cellular level.

Reviewer #3:

Summary

This paper examines the Drosophila Ryanodine Receptor (RyR or dRyR). Ryanodine receptors are enormous channel proteins that mediate calcium efflux from the endoplasmic reticulum and sarcoplasmic reticulum. One goal of the work is to describe salient developmental features of Drosophila RyR (i.e., where it localizes in the cell and how it contributes to muscle development and function) and to refine knowledge from prior reports. Many of the analyses toward that goal are well done; this reviewer especially likes the examination of how muscles develop (Fig. 5).

Another goal is to compare this information with what is known about mammalian RyRs. There seems to be a lot in common between Drosophila and mammalian RyRs. The paper finishes by taking a human ryanodine receptor variant of unknown significance and generating the corresponding amino-acid substitution in Drosophila RyR. The substitution has some phenotypic consequences for fly coordination, so the authors conclude that the human variant is likely to be pathogenic.

In terms of investigation, a refined description of RyR biology is welcome. Ryanodine receptors are critical contributors/mediators of intracellular calcium signaling processes. Understanding their properties can help to contextualize the results of studies where calcium dynamics are at play. This is true of for both Drosophila and non-Drosophila work. For this version of the paper, there are several statements that should be edited, both in terms of accuracy and in terms of reporting prior knowledge. Additionally, some experiments are missing controls or reagent verification. Importantly, the anti-RyR antibody needs supporting information regarding its specificity.

Main Comments

(1) The paper does not fully state what has been done before in terms of studying Drosophila ryanodine receptor expression. In comparing the work on ryanodine receptors in vertebrates versus Drosophila, the authors write, "By contrast, no systematic analyses have yet been performed to assess the expression of the sole Drosophila dRyR gene." I was a little surprised by this sentence, so I examined the literature. There are hundreds of Drosophila publications that mention the ryanodine receptor in some way, but they are not about gene expression . As stated, the sentence might depend on what the authors mean by "systematic analyses." Two early works are relevant here: the Hasan and Rosbash, 1992 paper and the Sullivan et al., 2000 paper. Both are cited in this study. And both of these early papers addressed RyR gene expression, so that fact should be acknowledged up front.

We agree with the Reviewer that there is a large number of publications that mention Drosophila ryanodine receptor with two of them identified by the Reviewer that provide information about Drosophila RyR expression. We refer to both of them and follow Reviewer’s suggestion to further acknowledge their work. The modified sentence in the text reads as follow:

“…in spite of early works by Hasan and Rosbash (1992) and Sullivan et al., (2000) no systematic analyses have yet been performed to assess the developmental expression pattern of the sole Drosophila dRyR gene…”

Concerning “systematic analyses” we mean the analyses of dRyR expression at both transcripts and protein levels during embryonic development and in differentiated muscles.

(2) (Related) I examined those two early papers to cross-check the extent of analysis done previously. The text of Hasan and Rosbash reports in situ examination of RyR transcript using a digoxigenin probe (though the online version of that 1992 paper seems to have left out the relevant mesodermal and muscle images referenced in the paper, in favor of duplicating Figure 5 three times - I emailed Development to alert them). More relevant, several experiments executed in the Sullivan paper agrees closely with the current paper. As such, it needs more complete referencing. The Sullivan paper showed short, round larvae in mutants (Fig. 1 of Sullivan); ubiquitous mRNA, strongly in muscle and mesoderm (Fig. 2 of Sullivan); impaired muscle function in mutants (Fig. 3 of Sullivan), and impaired larval heart rate (Fig. 4 of Sullivan).

Sullivan et al. paper is indeed a reference paper for Drosophila RyR. Our data are however largely novel and/or substantially extending those reported by Sullivan. Notably, we show for the first time developmental dRyR protein expression pattern in embryos and in larval filets, we also analyse dRyR isoform transcripts expression and provide for the first time embryonic muscle phenotype analyses that shed light on so far under investigated developmental function of dRyR.

We follow Reviewer’s suggestion and provide in the revised version additional citations of this work:

“…attenuation of dRyR (C57>dRyR RNAi) led to a significantly reduced larva body length (Fig. 3B, M) compared to control (Fig. 3A, Q), an observation that correlates with previously observed (Sullivan et al., 2000) reduced body size of dRyR¹⁶ mutant larvae…”.

“…our data extend previous observations of affected muscle contractility in RyR mutants (Sullivan et al., 2000)…”

“…Overall, observed dRyR loss-of-function heart phenotypes with a slow heart rate and increased arrhythmia correlate with impaired cardiac function in RyR mutant larvae (Sullivan et al., 2000)…”

(3) Fig. 1B-D (antibody staining): There are puzzles with this experiment. The first is with the anti-Dlg channel. Dlg is a core component of the NMJ postsynaptic density, and the antibody reveals a bright cage of Dlg around the boutons. But with the muscle images in Figure 1B, there are no boutons apparent (unless they are so far out of focus as to be invisible).

Indeed, Dlg also stains postsynaptic NMJs at the muscle surface. On the Fig. 1B showing more internal optical sections to reveal T tubules Dlg-positive NMJs are out of focus.

The second question centers on the dRyR antibody. The results state, "We first tested the expression of dRYR at the protein level." This sentence appears immediately after the sentence for gene expression from point 1. Technically, this antibody will help determine protein localization, not gene expression. But more importantly, there is no supporting/verifying information about this guinea pig anti-dRYR antibody. The methods state that it was provided by Robert Scott from NIMH. But there is no accompanying citation, no information about the antigen used to raise the antibody, and no negative control (either mutant or RNAi) to show that the staining is specific. If this is a published anti dRyR antibody that already meets the standards of specificity, that should be made clear, and the citation should be given. But if not, the information and data about the production of the antibody and the testing of its quality needs to be shared.

We apologize for this omitted citation. The anti-dRyR antibody has been previously described and its specificity tested in the article Gao et al., (2013). Corresponding author of this paper David J. Sandstrom left NIMH and anti-dRyR antibodies are currently curated by Rob Scott from Benjamin White’s lab at NIMH.

He generously sent us sample of this antibody. We add this information to the Material and Methods section.

(4) Fig. S1: Similar to the antibody, is there a negative control probe that does not reveal this expression pattern? There are any number of probes or secondary antibodies that non-specifically label Drosophila muscles in patterns just like this.

We are confident that the HCR probes are working properly as they reveal dRyR transcripts expression that is consistent with dRyR protein expression pattern. In parallel they show differential expression in embryos.

Author response image 3 shows the control HCR ISH experiment with a probe that detects Apterous transcripts (specific for a subset of embryonic muscles and not present in L3 larval muscles).

Author response image 3.

A comparison between Ap HCR (A, A’) and dRyR Ex23 HCR (E, E’) signals.

Minor Comments

(1) "Overall, observed dRYR loss-of-function heart phenotypes...are reminiscent of those associated with aging (Nishimura et al., 2010), indicating that dRyR RNAi-induced impairment of Ca2+ homeostasis contributes to cardiac aging..." The conclusion of the sentence does not logically follow from the first part. This is because the tests conducted here were on rhythm, not on calcium homeostasis and cardiac aging.

So, the tests cannot definitively say anything about those latter phenotypes.

To answer this reviewer’s coment we modify the concluding sentence as follow:

“…We hypothesize that dRyR RNAi-induced impairment of Ca2+ homeostasis could contribute to cardiac aging, for which Drosophila is a recognized model (Nishimura et al., 2011).”

(2) Fig. S2 (bar graph): "% of total" - Is this supposed to refer to the percentage of the total muscle area that is positive for ATP5a staining? That should be clarified.

We provide clarification in the Fig.S2 legend. “% of total” means the percentage of the measured muscle area that is positive for ATP5a staining”.

(3) Fig. 3M, should say length

Done

(4) Fig. 5A legend - See Sullivan; that paper concluded that RyR[16] was hypomorphic instead of null, based on RyR[16]/Df comparison to RyR[16]/RyR[16]. Intuitively, I agree; a lesion that rips out the start site would likely be null. The antibody could help with classifying the allele, depending on the part of RyR used as the antigen.

The RyR¹⁶ mutants were indeed described by Sullivan et al., as hypomorphic and not null. In the Fig. 5 legend we modify the comment to: “…homozygous dRyR¹⁶ mutant embryo…”

(5) Discussion: "This also suggests that all dRyR isoforms are collectively required for larval muscle function." That sentence does not logically follow the expression information. In order to test that idea, individual isoforms would need to be eliminated or knocked down.

We agree with this comment and modify our sentence accordingly.

“However, whether all dRyR isoforms are collectively required for larval muscle function requires further investigation.”

Reviewer #3 (Significance):

The idea that RyR is expressed in many kinds of muscle is put forth as a major conclusion. It is good that the authors report this fact, and the impacts on muscle development documented in Figure 5 are some of the best data in the paper. However, in terms of opening up a new understanding of RyR biology, the impact of this information seems modest. Prior Drosophila work and the work of others studying these channels show that ryanodine receptors are ubiquitous. The fact that there is only one Drosophila RyR gene would lead most scientists to hypothesize that it would be present on the ER surfaces of all kinds of tissues, including different types of muscle.Novel phenotypic information for Drosophila RyR is reported in the study, and this is good. But in terms of the model system, the strength of Drosophila is in using genetic combinations to make refined conclusions. That toolkit is not fully used here; therefore, the paper is mostly descriptive. This study is mostly a single-gene study (dRyR), with isolated exceptions, like Cam knockdown in Figure 5.

To improve the functional/mechanistic aspect of the manuscript in the revised version we include to Fig.5 the analysis of myogenic role of additional calcium regulator: ER calcium pump SERCA.

Author response:

General Statements

We thank the reviewers for their careful and supportive reviews of our manuscript. We have addresses all the reviewers comments and extensively revised the manuscript accordingly.

During our revisions, we discovered a bug in the code that calculated the linear genomic distance between the captured promoter regions (bait regions) and the promoter-interacting fragments (PIFs). The error inadvertently halved the distance measurements in the output tables. This has been corrected in the revised manuscript and has resulted in updates to Figure 1B and corrected values in the ‘interaction_distance’ and/or ‘interaction_type’ columns of Supplementary Tables 2, 3, 6 and 8. We thank the reviewers for the opportunity to correct this.

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

In this article, the authors conducted promoter-capture HiC experiments (pcHiC) in Mouse Cerebellar granule cell progenitors (GCps) and obtained a good set of 3D genome interactions map of protein-coding genes' promoters. This dataset was later integrated with ATAC-seq and ChIP-seq experiments to identify putative enhancer regions within promoter-interacting regions, and with higher base-pair resolution than what is obtained by pcHiC experiments. This set of enhancers is then compared to and presented as being more reliable than those present in VISTA enhancer database. In addition, ATAC-seq sites and RNA-seq datasets, both obtained in WT and CHD7 and KO conditions, are integrated to correlate expression of a set of genes to the chromatin accessibility of their distal enhancer(s) which is believed to be promoted by CHD7. The study is completed by focusing on transcription factor motif analysis on CHD7-regulated enhancers which shows an enrichment for proneural transcription factors, with special emphasis on Atoh1 found to be frequently co-recruited with CHD7. Data and methods are well detailed and correctly replicated and will be useful as a resource for the community. The overlap obtained between pcHiC experiments and auto-criticized by the authors is very common and expected in this kind of experiments. In general, the conclusions drawn the article are convincing but some aspects such as comparison to VISTA and the naming of 'enhancers' should be moderated.

We thank the reviewer for their positive and constructive comments. We have amended the manuscript as indicated in detail below.

(1) The comparison of pcHiC-identified enhancers vs. VISTA enhancers should be more balanced, as the two approaches have important conceptual differences. Although VISTA enhancers are based on functional annotation, their target genes might not necessarily be correctly assigned based on the distance. On the other hand, putative enhancer regions identified by pcHiC experiments do not rely on functional testing. So both type of information are useful but can be put in perspective.

We thank the reviewer for making this point. We have amended the text to present a more balanced view e.g. “Using VISTA-designated hindbrain enhancers as an example, we identify the genes most likely regulated directly by these enhancers and update their annotation accordingly.”

(2) To increase the strength of the paper, it would be preferable that authors include simple functional enhancer assays (e.g. CRISPR deletion of contacting enhancer, luciferase assay) to support their perspective since 3D conformation information in KO condition is lacking in the article. Although ideally these experiments should be better performed for a full demonstration, it would be acceptable to at least include a simple functional assay in the WT context to demonstrate that the regulatory regions obtained by crossing genomic data are real enhancers. This point is even more critical knowing that enhancers lacking classical histone marks (H3K27ac+H3K4me1) has been described. The same comment applies to promoter interacting fragments lacking these marks, that could be missing enhancers (i.e enhancers without these marks).

To address this point, we performed luciferase assays to show that putative enhancers identified with our integrated bioinformatic approach (pcHi-C + ATACseq + H3K4me1 + H3K27ac) do indeed exhibit enhancer activity. For these experiments, we tested these putative fragments in an immortalized cell line SHH-NPD, a GCp-derived cell line generated by Fults laboratory (Jenkins et al. 2014). The results of these experiments are included as Suppl. Fig. 1 in the revised manuscript.

Minor point

- Figure 5B is lacking labels.

We apologise for this oversight – labels have now been added.

Reviewer #1 (Significance):

This article, when completed with possible revision, will be be useful for the community in terms of useful resource of experimentally determined putative enhancers in Cerebellar granule cell progenitors. It also provides some insights into the association of CHD7 and Atoh1 in distal regulation in these cells.

We thank the reviewer for acknowledging the significance of our work.

Reviewer #2 (Evidence, reproducibility and clarity):

In this manuscript, the authors aim to identify active, long-range regulatory interactions in cerebellar granule cell progenitors (GCps). As such, the authors perform promoter capture Hi-C to map long-range interactions for all gene promoters, using cells isolated from P7 mouse brain samples. While the resolution of these maps is limited by the relatively large fragment sizes generated from a 6-bp cutter, the authors combine these interactions with other available published datasets, including from their own previous work, (e.g. ATAC-seq and ChIP-seq) to more precisely map putative enhancers within the long-range interacting regions of captured promoters. The paper further focuses on the importance of transcription factor Atoh1 and chromatin remodeler CHD7 in regulation of these putative enhancers in GCps. The authors suggest a direct interaction between CHD7 and Atoh1 by overexpression and co-immunoprecipitation in human embryonic kidney cells.

As stated by the authors, this study represents a valuable resource for researchers interested in the identification of enhancers in GCps cells, and their linked target genes. While broadly descriptive, the study does highlight some gene loci of interest and of biological relevance. For example, through integration of previously published datasets, the study resolves which putative regulatory elements at the Reln locus may regulate its activity.

We thank the reviewer for their supportive comments.

We provide a summary of our major and minor comments here.

Major comments:

(1) The main take-home messages of the manuscript could be more clearly stated in the introduction to help readers understand the main conclusions of the work.

We have added a sentence to the Introduction to clarify the key take-home messages:

“We report putative distal regulatory elements for >12,000 genes, identify CHD7- and Atoh1-regulated enhancer elements and show that these factors interact and likely co-regulate the expression of key genes in the GCp lineage.”

(2) In the discussion, a previous Hi-C dataset is referred to "Reddy et al. annotated 5,175 promoter-enhancer interactions in GCps using Hi-C without enrichment (Reddy, Majidi et al. 2021)." It would be beneficial to compare the interactions identified previously with the current study (5,175 vs 46,428 interactions).

To address this comment we have performed an additional analysis and include text and Suppl. Figure 3 and Suppl. Table 13 to demonstrate the extent the two datasets compare, overlap and diverge. We have also added additional text to the discussion to highlight the difference and technical considerations between the two approaches and how they complement each other.

The 5,174 enhancer-promoter (E-P) interactions identified by Reddy et al were downloaded and intersected with the 46,428 promoter-accessible PIF regions identified in our study. The new supplementary Figure 3A illustrates that 82% (843/1207) of genes that Reddy et al identifies long-range interacting regions for are represented in our pcHiC dataset. Our pcHiC data contains information on distal interacting regions and potential enhancer regions for an additional 11,511 protein coding genes. Suppl. Figure 3B provides an overview of the Reddy et al E-P interactions that are, and are not identified in the pcHiC. We replicate 38% of Reddy et al’s E-P findings, whilst 53% of the 3229 interactions unique to the Reddy data would not be detected in the pCHiC data due to technical reasons resulting from the capture design and analysis protocol. Of the remaining interactions that are specific to the Reddy data, we identify other distal regions interacting with those same promoters . Suppl. Table 13 details the full comparision of Reddy’s E-P interactions that are found within our dataset.

The differences between the two datasets and the increased number of interactions detected in the pcHiC dataset likely result from the increased enrichment for the captured promoters enabling the detection of interactions that would have been below the detection threshold for the HiC study. In addition there are notable differences in analysis strategies for the two datasets which also contribute to differences in detection of regions. Reddy et al binned the HiC data into 10Kb regions to identify interacting regions and subsequently used chromatin marks to identify possible enhancer and promoter regions within these large regions. In contrast we have used the pCHiC and CHiCAGO algorithm to identify individual HindIII restriction fragments that are proximal to targeted promoter regions (PIFs), and prioritised those that have accessible regions within them which could represent various types of regions that play regulatory roles such as enhancers, CTCF site or facilitator regions, independent of their chromatin mark composition rather than focusing solely on enhancers.

(3) The authors identify an overlap with some of their identified enhancers with those from VISTA. Is this a fair comparison seeing as the enhancer reporters were tested during early embryonic development (e.g. E11.5 and E13.5) and seen to be active in the hindbrain, would these stages be relevant to GCps from P7? Can the authors identify ATAC-seq for example from hindbrain from embryonic stages and determine if the enhancer accessibility profile looks similar to that for the P7 GCps cells?

We thank the reviewer for this important question regarding the developmental relevance of our VISTA comparison and acknowledge that direct comparison between the time point requires careful consideration. Firstly ,to address the question of how similar the chromatin accessibility profiles are between the embryonic and P7 timepoints, we compared the ATAC-seq data from our paper to ENCODE data from the hindbrain. Of the 140 vista enhancers that were intersected with the pCHi-C dataset, 119 were identified from the lacZ studies as active in the hindbrain at E11.5 whilst 21 were identified as active at timepoint E12.5. We compared ENCODE ATAC-seq peaks from the E11.5 (ENCFF743IYX) and E12.5 ( ENCFF198TLF) hindbrain to the GCps from P7 across both the entire genome (global accessibility) as well as specifically +/- 3MB around the VISTA enhancer regions in the PIFs from the pCHiC to assess the conservation of local accessibility profiles.

When looking at the global accessibility profile of embryonic hindbrain versus P7 GCps across the whole genome there was a large degree of overlap with ~85% (E11.5) and ~88% (E12.5) of all ENCODE ATAC peaks overlapping with accessible ATAC summit regions from P7 GCps:

Author response image 1.

To identify if this was consistent in the immediate chromatin environment of the VISTA enhancers themselves, we compared the accessibility profiles across timepoints in the local environment surrounding the VISTA enhancers. This local environment was defined as a region that added an additional 3MB on either side of all VISTA enhancer positions found in PIFs. 3MB was chosen as the longest interaction found for a single VISTA element was approximately 2.7MB. Consistent with the global analysis a similarly high level of overlap of accessible regions between the timepoints was found for the local chromatin environment in surrounding the VISTA enhancers that were found within PIFs in the pCHiC dataset with ~87% (E11.5) and ~89% (E12.5) of encode detected peaks overlapping with accessible ATAC summit regions from P7 GCps.

Author response image 2.

Regions +/-3MB of VISTA enhancers in PIFs

Author response image 3.

Regions +/-3MB of VISTA enhancers in PIFs

Genome browser shots at the three example VISTA loci from Figure 1 further support this approach. In addition to this we also note that a recent study by Chen et al (2024 https://www.nature.com/articles/s41588-024-01681-2) where capture-HiC performed at E11.5 of 935 VISTA enhancers across multiple tissues confirmed that the majority of VISTA enhancer regions (61%) bypass adjacent genes which is consistent with our nearest gene comparison.

(4) The co-IP experiment appears to support the conclusion that Atoh1 and CHD7 can interact, however there are bands in lanes where there should not be (i.e. Input lanes 1 and 4 for FLAG blot). It would be recommended to repeat this result at least once. [Expected time 2-4 weeks].

This experiment has been repeated 3 times with the same result. It is normal for non-specific background bands to appear on Western blot from total cell lysates (inputs) as most antibodies have significant cross-reactivity. The anti-FLAG antibody clearly detects bands above background in lysates where FLAG-tagged CHD7 is expressed. Most critically, despite the presence of non-specific bands in input, FLAG-tagged CHD7 is only detected in immunoprecipitated samples where either FLAG-tagged proteins have been precipitated and FLAG-tagged CHD7 is expressed and HA-tagged Atoh1 has been precipitated when both FLAG-tagged CHD7 and HA-tagged Atoh1 are expressed.

(5) The methods section describes analysis of several datasets, however we could not access the code at the time of review. Do the authors intend to make this code available at the time of publication?

Yes once the publication is approved all code will be made available along with conda environment yaml files to replicate the software environment in which the analysis was performed.

(6) Page 7 "replicate one and two, respectively". Can the authors clarify the number of biological replicates performed for pcHi-C?

Two biological replicates were performed for pcHiC which were then bioinformatically combined into a ‘superset’ for CHiCAGO interaction calling as is standard practice for pcHiC data (see e.g. Cairns et al, 2016. We have revised the text to make this clearer.

Minor comments:

(1) Page 3 "controlling the expression of 577 genes in GCps" - the authors do not provide evidence that these enhancers control gene expression directly, this should be reworded.

Thank you. We have reworded to: “contacting the promoters of 577 genes” to indicate that these were identified using pcHi-C and not functional assays.

(2) Page 5 "where transient amplifying divisions exponentially expand GCps" - at what stages of embryonic/postnatal development are GCps first detected, and when do they amplify and then differentiate?

GCps that form the EGL are specified in the rhombic lip from E13.5 (Machold, 2005 and Wang, 2005) and a clear EGL can be observed in the cerebellar anlage from E14 (Ben-Arie, 1997) of development. They amplify from this stage and differentiation, induced by neurogenic factors like NeuroD1 is visible from P0 onwards (Miyata, 1999). We have amended the text to include this additional information: “GCps that form the EGL are specified in the rhombic lip from E13.5 (Ben-Arie et al, 1997; Machold & Fishell, 2005) and a clear EGL can be observed in the cerebellar anlage from E14 (Ben-Arie et al., 1997) of development. They amplify from this stage and differentiation, induced by neurogenic factors like NeuroD1 is visible from P0 onwards (Miyata et al, 1999).”

(3) Page 7 "identified 164,387 unique and significant interactions" - how is an interaction defined, a single read, or evidenced by a certain number of reads. "promoter interacting fragments or PIFs" - is PIF referring to a single read evidencing an interaction?

An interaction is defined by the CHiCAGO algorithm. The number of reads needed to score an interaction depends on the both the distance away that PIF is from the promoter (this is modelled using a distance-dependent component that accounts for decay of contact frequence with genomic distance) and also includes a component that models how the sequence or other technical artifacts might influence the capture bias of some sequences compared to others. For each promoter a background model is generated of the expected number of reads that would be captured based on the above considerations and if the number of reads for those regions exceeds this background model by a certain threshold the interaction is deemed significant using a p-value like score. In practice this means that regions further from the promoter will often require less reads to signify a significant interaction compared to regions that are much closer to the promoter. The significant PIFs in the dataset are all evidenced by a minimum of 3 reads in at least one biological replicate. We have included a short explanation of this in the methods of the revised manuscript for clarity.

The maximum reads in a single replicate library for a specific PIF was 1557, and the median number of reads per PIF was 17.

(4) Page 8. What is the distinct between PIFs and "promoter interacting regions (PIRs)"? These could be better defined in the text.

Thank you for picking up this discrepancy, we were using PIR and PIF interchany. We have amended the manuscript to refer to PIFs consistently throughout.

(5) Figure 1C-F. Labels "Random" and "PIFs" don't line up well with the two bars.

Thank you, this has been corrected.

(6) Page 9. Could the authors show some representative images for the "VISTA hindbrain enhancers" (e.g. for Figure 1I-K).

We have inserted representative images showing in vivo activity of these enhancers in mouse embryos from the VISTA enhancer site.

(7) Fig 2G, Page 11 "The 12,354 genes that were linked to a PIF containing an ATAC-seq peak were found to have a higher median expression level than the 2,049 genes that had PIFs that did not coincide with ATAC-seq peaks" - is this significant?<br />

Apologies for this oversight. We have performed a two-sided t-test on the log transformed TPMs between the two groups and have included the significance in the revised figure (p=1.8 e-40).

(8) "Gene Ontology analysis of genes with accessible PIFs revealed a significant enrichment for 119 biological processes" - can you include the GO terms in a supplementary table? Is there a way to prioritise down the 12,354 genes to a shorter more significant list of genes, this seems a long list to include in GO analysis.

We have included a supplementary table with this data in the revised manuscript (Suppl. Table 6). We included all 12,354 genes in this analysis as the point of this analysis was to demonstrate that developmental processes are enriched in the PIFs with accessible chromatin, compared to the genes where only PIFs without ATAC were identified.

(9) Page 11 - "The chromatin remodelling factor CHD7 is essential for normal expansion of GCps in the postnatal mouse cerebellum (Whittaker et al., 2017b) and deletion of Chd7 from GCps results in striking cerebellar hypoplasia and polymicrogyria (Feng et al., 2017; Reddy et al., 2021; Whittaker et al., 2017b). CHD7 haploinsufficiency is also sufficient to cause cerebellar hypoplasia and foliation defects both in mouse models and in the context of CHARGE syndrome in humans (Whittaker et al, 2017a; Yu et al, 2013)." - this appears more suitable for the introduction.

Thank you, we have moved this text to the Introduction.

(10) Page 12 "the majority of which (4,663/5,369) displayed decreased accessibility when Chd7 is depleted". This was difficult to understand initially - which are expected to be the direct effects? Increased or decreased accessibility? Perhaps it would be better to focus only on the decreased accessibility sites?

We have previously shown that the majority of differentially accessible regions in Chd7-deficient GCps show decreased accessibility. Chromatin remodelling by CHD7 could conceptually reduce or increase accessibility of a particular locus and the only way to infer direct effects are by identifying regions to which CHD7 is recruited.

Approximately ~9% of the sites that decreased in accessibility overlapped with regions bound by CHD7 (464/4663), whilst ~2% of sites that increased in accessibility overlapped with regions of CHD7 binding (14/706). Whilst it is likely that the majority of directly regulated sites decrease in chromatin accessibility when CHD7 is removed, the number of sites that increases in accessibility is small but observed and should be included for completeness.

(11) The analysis in Fig 3A reveals that only a small number of CHD7-bound enhancers show differential accessibility and altered linked gene expression upon CHD7-knock down. This requires a little more discussion - why do so many sites change in accessibility compared to the number of sites which change accessibility or are associated with gene expression change?

Identifying CHD7-regulated enhancers is challenging, mostly due to the inefficiency of CHD7 ChIP-seq. The low quality of available CHD7 ChIP-seq data has made it particularly difficult to identify CHD7 peaks. However, the integration of this data with ATAC-seq accessibility, chromatin modification and pcHi-C data has allowed us to identify a subset of enhancers that are most likely directly regulated by CHD7. However, given these technical limitations, we would be hesitant to conclude from the present data that the majority of chromatin accessibility changes in enhancers in Chd7-deficient GCps are indirect. We have added the following text to the discussion to indicate this: “Identifying CHD7-regulated enhancers is challenging, mostly due to the inefficiency of CHD7 ChIP-seq. The low quality of available CHD7 ChIP-seq data has made it particularly difficult to identify CHD7 peaks. However, integrating CHD7 ChIP-seq data with ATAC-seq accessibility, histone modification ChIP-seq and pcHi-C data has allowed us to identify a subset of enhancers that are most likely directly regulated by CHD7. However, given these technical limitations, we would be hesitant to conclude from the present data that the majority of chromatin accessibility changes in enhancers in Chd7-deficient GCps are indirect, as suggested by the data in Fig. 3A.”

(12) Page 12 - "Over-representation analysis confirmed an enrichment of genes linked to nervous system development" - could this and the GO term analysis be included in a supplementary figure?

We have included these results as Suppl. Table 7 in the revised manuscript.

(13) Fig 3D - what does the arrow represent in the chromatin schematic?

The arrow in the schematic indicates chromatin remodelling – we have clarified this in the figure legend and added headings to these panels to indicate the 3 different types of elements: Direct CHD7 targets, Indirect targets and CHD7-bound elements.

(14) Fig 3G does not appear to be referenced in the text. The value of the Upset plots in the main figure 3 wasn't very clear, perhaps these could be moved to the supplement? Is there a clearer plot to support the conclusion "CHD7 primarily regulates enhancers".

We apologise, the panels were mis-labeled in the text. This has now been corrected. We hope that the amendments in response to point 13 above now clarifies these findings showing that direct CHD7 targets are characterised by active enhancer marks.

(15) Page 14 "putative consensus sites for proneural bHLH TAL-family of proteins Neurog2, Neurod2, Neurod1, and, Atoh1 in elements" - HOCOMOCO motifs are only shown for Atoh1 and Nhlh1. It may be valuable to show the sites for all the listed TFs. What does white represent in the heatmap in Fig 3H? This plot is difficult to interpret, and also relatively small in the figure but appears important to conclusions. Perhaps Fig 3H could be made more prominent?

Thank you for highlighting that the white boxes might be confusing. The white blocks indicate that these motifs do not pass threshold for significantly enriched in the dataset based on the p and q values.This has now been clarified in the figure legend.

We have enlarged panel H to make more prominent.

(16) Page 15 - "Myb was the only motif specific to CHD7 bound regions that changed in accessibility compared to those that exhibited accessibility changes without CHD7 binding or CHD7 binding without accessibility changes (Suppl. Fig. 1)." I couldn't interpret this sentence, requires clarifying.

We agree that this description is confusing and since it is difficult to draw clear conclusions about the significance of enhancers with Myb motifs in this context, we have removed this sentence from the revised manuscript.

(17) Page 16 and Fig 4B - a discussion of why both up and down regulated genes are detected for Atoh1 depletion? Which class of genes are expected to be directly regulated (the down-regulated genes)?

Like most transcription factors, ATOH1 may be able to function as both a repressor and activator depending on the context. Although the majority of genes are downregulated in Atoh1-defivcient cells, suggesting that Atoh1 functions as an activator in most cases, our analysis have identified several up-regulated genes that contain Atoh1 ChIP-seq peaks in their cognate enhancers (See Suppl. Table 7), consistent with these also being direct Atoh1 targets.

(18) Fig 5B - the genomic traces are not labelled in this figure.

Thank you, labels have been added.

(19) Page 17 - "Pathway enrichment analysis of the 22 genes compared to all genes that were expressed in GCps shows a significant enrichment of terms: Hypoplasia of the pons (HP:0012110 P=0.006) and Abnormal pons morphology (HP:0007361 P=0.016) from human phenotype ontology, due to the presence of Reln, Dcc, Mab21l1 and Gli2." - this analysis should be included in the supplementary tables.

These results have been included as Suppl. Table 12 in the revised manuscript.

(20) Do the authors have a suggestion for which domains of Atoh1 and CHD7 could be interacting? Could the authors design truncated constructs for overexpression in HEK cells to test this hypothesis? [Expected time 4-6 weeks, interesting but not essential to do experimental work here].

We agree this is an interesting question. Our collaborator, Professor Peter Scambler (UCL) has performed a yeast two hybrid screen for CHD7 interacting proteins in a mouse E11.5 library using the CHD7 BRK domain (aa 2521-2708) as bait. The screen had a single hit, which encompassed the N-term 127aa of ATOH1 (personal communication). This observation supports our co-IP data and suggests that the N-terminus of ATOH1 interacts with the BRK domain of CHD7 but further validation will be needed to confirm this.

(21) Page 28 "Differential accessibility analysis was performed using DESeq2 (v 1.22.1)" and Page 19 "Whereas chromatin accessibility at some of these enhancers were affected by Chd7-deficiency" - what were the cutoffs used for looking at differentially accessible regions? Complete loss of accessibility or a quantitative change?

Quantitative change rather than complete loss was used. Thresholds based on adjusted p-values (padj<0.05) were used as indicated in the methods.

Requested comments on referencing:

- "Long-range" - how do the authors define long-range? Can this be referenced. CO? good reference here.- look to CHiCAGO paper

- "When chromatin conformation or 3D organisation data is not available, studies typically assign regulatory elements to the nearest gene promoter" - needs referencing.

- "Many of these 22 genes regulated by CHD7 and Atoh1 have established critical roles in cerebellar development, including Neurod2, Pax6 and Gli2 (Fig. 5B)" - needs referencing. "from human phenotype ontology, due to the presence of Reln, Dcc, Mab21l1 and Gli2" - needs referencing.

Thank you, references have been added.

- "active enhancers (H3K27ac+, H3K4me1+), promoters (H3K27ac+, H3K4me3+), regulatory elements (H3K27ac+, H3K4me1+, H3K4me3+), or poised enhancers (H3K4me1+)" - needs referencing.

Thank you, references have been added.

- Reference required in main text for VISTA (e.g. Visel et al., 2007)

Thank you, reference added.

Reviewer #2 (Significance):

The strengths of this manuscript are the integrated approach to identify cell-type specific enhancers utilizing available epigenomic datasets, and leveraging 3D genome topology to directly link them to their target genes. For example for the Reln gene previously implicated in cerebellar phenotypes for CHD7 mutants. The pcHi-C dataset generated in this study provides a valuable reference for the community of enhancer-promoter pairs for a specific cell-type of interest with human disease relevance.

We thank the reviewer for recognising the potential value of our work to the community.

The limitations of the study are partially addressed in the text by the authors, including the resolution from the pcHi-C using a 6-bp cutter, the limitation of sequencing depth (more interactions may have been identified with more depth), and the limitated of correlation between replicates (likely due to undersampling the library). Page 9 "some additional interactions with the nearest gene promoters might be identified in our pcHi-C dataset with deeper sequencing".

We thank the reviewer for highlighting our acknowledgements of the potential limitations of our work.

Additional limitations include the use of the VISTA browser mouse LacZ embryos to validate some of their enhancers, the limitation here being that the VISTA browser tests enhancers at embryonic stages (focused at E11.5 and E13.5) while the GCps cells were collected at P7. The LacZ images from VISTA are also not shown. The HEK cells used for the co-IP could be seen as a limitation as these are not relevant cells for the cell state studied, the authors could clarify their use of these cells.

We thank the reviewer for their careful assessment of the limitations of our study. We have now included images of the VISTA enhancers in Fig. 1I,J,K. Rather than a limitation, using irrelevant cells for co-IP might be seen as a better approach, as conceivably the chances of an indirect interaction between the two proteins being tested by a bridging complex is less in an irrelevant cell types that might not contain such complexes. Either way, HEK293T cells is the standard laboratory model for co-IP studies as they can be transfected with ease.

The study reported here is largely based on previous work from the authors (Whittaker et al 2017b). This study reported that the chromatin remodelling factor CHD7 is essential for normal expansion of GCps in the postnatal mouse cerebellum and deletion of CHD7 from GCps resulted in the phenotype of cerebellar hypoplasia. This study also largely leverages previously published datasets from the Whittaker et al 2017b (e.g. CHD7 deletion data) and reanalyses it in the light of the new pcHi-C datasets.

This manuscript will be of interest to researchers interested in analysing long-distance targets of as well as researchers trying to understand the precise gene regulation in cerebellar development. It may also be of interest to clinical geneticists to interpret novel putative non-coding disease mutations.

We thank the reviewer for highlighting the wide interest of our manuscript.

In assessing this manuscript, my expertise lies in models of human development and gene regulation, with a focus on enhancer function.

Reviewer #3 (Evidence, reproducibility and clarity):

Riegman et al have explored the gene regulatory landscapes of cerebellar granule cell progenitors (GCps). They have generated promoter capture Hi-C data to identify regions that interact with promoters in these cells. In addition they generate ATACseq data in wild-type and CDH7 knock-out cells. They integrate these data to identify enhancers that potentially regulate genes in GCps. In addition, the authors identify an interaction between CHD7 and ATOH1, whose binding sites also overlap in the genome.

The dataset can be potentially interesting for people studying cerebellar development.

I have a few concerns regarding the paper. The most pressing one is that the authors seem to equate interactions in pcHi-C with regulation. This is problematic for two reasons. First whether interaction equates regulation is still debated and whether this can be detected with a low-resolution C-method (i.e. using HindIII) is a further point of contention.

We thank the reviewer for pointing this out. We agree and apologise for not being clear in our manuscript. We have made the necessary amendments to indicate that pcHi-C by itself only assess proximity in the nucleus, not function.

We acknowledge the limitations of the pcHi-C method, including that resolution is limited by the use of a restriction enzyme. However, we (see e..g. Suppl. Fig. 1) and others (see e.g. Freire-Pritchett et al (2017) and Mifsud et al (2015)) have used this approach successfully to identify functional enhancer elements.

The second issue has to do with the way the pcHi-C data is interpreted. What is detected as a significant interaction by Chicago are regions that have a contact frequence above background. This means that local regions with a (much) higher contact frequency may not be called as significant. When we follow the logic that contact frequency is related to gene activation (which may not necessarily be true) whether a fragment is more frequently contacted than the background should not matter (relative contact frequency), rather it should be interpreted based on the absolute contact frequency.

The reviewer is right that local regions will have a higher contact frequency and that local contacts aren’t always captured by the CHiCAGO model. However, the purpose of this study was to prioritise the identification of distal elements that are not captured by existing methods including nearest gene annotation.

There are a number of reasons why absolute contact frequency might not be an appropriate measure to infer gene regulation: 1) Many factors can affect the absolute contact frequency including the proportion of cells that are exhibiting active transcription at that time across a population, especially if expression is limited to a small number of this population at that time. 2) Absolute contact frequency assumes that more contact results in more regulation which is not necessarily true and would depend on the combination of factors that are associated with that regulatory element. Figure 1 from https://www.nature.com/articles/s41596-023-00817-8 - Figure 1 – Micro capture C show that regions with low absolute contact frequency compared to adjacent regions have potential to regulate gene expression, as have other studies that have used CHiCAGO to identify regulatory elements. 3) The sequence of some fragments makes them more likely to captured or enriched in the HiC protocol, which the relative contact frequency above background controls for.

This becomes relevant because the authors claim that 80% of enhancers are wrongly annotated based on their metrics. The only way to correctly annotate an enhancer is to knock it out and checking the effect on genes in the vicinity. Therefore, to claim that their method can correctly annotate enhancer is grossly overstated, particularly when considering the issues with contact frequency stated above. Therefore, claims like 80% of enhancers are wrongly annotated should be removed from the paper. The authors should discuss how to annotate enhancers, in the Discussion and what the proper method is for annotations.

We have amended the text to indicate that we do not suggest that VISTA enhancers are wrongly annotated but incompletely assigned. We apologise for making this suggestion in the first draft. There is however complementary evidence from Cheng et al (2024), now referenced in the revised manuscript, that also find 60% of the VISTA enhancers skip their adjacent gene. It is also well established in the literature that nearest genes are not always regulated.

Other points:

- The authors claims that PIFs have 2.14 and 2.69 fold enrichment of H3K4me1 and H3K27ac sites. Did the authors use the whole genome as background. If so, they should take into account that promoter are more likely in regions of high gene density, which are more dense in active marks. It would be better to perform local, circular permuation of the the PIFs around the promoter.

The reviewer is correct that a whole genome background is not an appropriate background for testing enrichment of active marks within PIFs. Fortunately, this is taken into account in the CHiCAGO enrichment test which selects the background from fragments that are matched to the same distance of the PIFs to account for the observation that promoters are more likely in regions of high gene density and are therefore more enriched for active chromatin modifications.

- The authors talk about "lead PIF", which is the fragment with the "most significant CHICAGO score". What does this mean? Something is significant or not, despite common misuse of the term there is no gradient of significance.

The reviewer makes a good point here and we apologise for the oversight in wording and have corrected the text to be more specific that the lead PIF is the one with the highest ChiCAGO score.

- In the GO analysis the categories with the lowest p-value are presented, but this biases for large categories. It would be more relevant to also select for and show the enrichment scores.

We agree with the reviewer that a drawback of GO analysis is that it biases for large categories and that if by ‘enrichment score’ the reviewer means the –log10(p-value) we have included that in the supplementary tables which also includes the size of the category and number of genes detected in it.

Reviewer #3 (Significance):

The study provides a dataset that may be interesting for people studying cerebellar development. In that sense the data is mostly interesting from a fundamental viewpoint. The data seem of good quality.

The authors claim that they a very sizeable fraction of enhancers are misannotated, but I do not believe that this is correct.

We thank the reviewer for pointing this out. We apologise for creating the impression that VISTA enhancers are incorrectly annotated. We have amended the text to reflect that these are incompletely annotated.

My expertise is 3D genome, bioinformatics.

Author response:

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

eLife Assessment

This important study concerns the propagation of waves in bacterial biofilms, bridging active matter physics and bacterial biophysics. While the experimental observations are solid, the theoretical interpretation and model validation are currently incomplete and require further refinement. This work will be of interest to microbiologists, biophysicists, and researchers studying collective behavior in biological systems.

In the revised manuscript, we have added new experimental results that strengthen the connection between our observations and the modeling framework used to interpret the collective oscillations. We have not introduced a new theoretical model; rather, we employed established active matter models and sought to link the observed phenomena to these frameworks. In particular, our new data demonstrate that the transition between the motile and biofilm-forming states specifically modulates the elasticity and elasto active coupling of the bacterial structure. This behavior is in excellent agreement with the predictions of the active solid model. All the experimental details are given below. We believe that the revised version of the manuscript now establishes this connection more clearly and convincingly.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Overall, this is an interesting paper. The authors have found multiple experimental knobs to perturb a mechanical wave behavior driven by pilli feedback. The authors framed this as nonreciprocal interactions - while I can see how nonreciprocity could play a role - what about mechanical feedback? Phenomenological models are fine, but a lack of mechanistic understanding is a weakness. I think it will be more interesting to frame the model based on potential mechanochemical feedback to understand microscopic mechanisms. Regardless, more can be done to better constrain the model through finding knobs to explain experimental observations (in Figures 3, 4, 5, and 7).

We thank the reviewer for the positive assessment and for highlighting this important point. The reviewer is correct that the phenomenological Kuramoto-based model does not explicitly show the detailed cell–cell interactions. However, the active solid model is formulated on detailed elastic couplings and active forces, which inherently represent mechanical feedback within the biofilm structure. In this framework, nonreciprocity emerges naturally from the tensorial nature of active forces between bacteria—a concept already well established in the active matter literature. Importantly, this mechanism is purely mechanical and closely parallels nonreciprocal hydrodynamic interactions among active particles, which also arise from tensorial couplings.

In our system, elastic interactions within the biofilm matrix, combined with pilus-generated active forces, provide a natural origin for nonreciprocal interactions. To further validate this, we improved our imaging to record single-cell dynamics both at the colony edge and on the biofilm surface. (new supplementary Video). These experiments show that motile bacteria at the leading edge of the biofilm structure do not generate waves, whereas stationary bacteria within the biofilm display local oscillations within the elastic network. This observation supports the view that collective oscillations are a property of the elastic biofilm state rather than of freely motile cells.

Moreover, the main control parameter for these oscillations is the ratio between elastic strength and the active force generated by pili. In the active solid model, this ratio is captured by the parameter π and alpha terms. Experimentally, we can tune this ratio simply by adding or removing water from the biofilm, thereby modulating its elasto active coupling. We further motivated the controllability of this feature experimentally. We let the plate dry nonuniformly and observed that the transition between spiral target and plane waves could emerge spontaneously across the plate (see Figure 3a). This observation also states the importance of moisture in the biofilm. Starting from this point we established the connection between experimental observation and modelling. In our new simulations we also noticed that the transition from spiral to target wave is particularly driven by merging processes of different topological charges +/- 1 spiral pairs. This critical point was also confirmed by modelling which links the process to elasto active coupling. Further we supported our claim by imagining the edge and the biofilm structure. These new results clarify that elastic structure of the biofilm is critically important (Supplementary Figure 3). We have clarified this mechanistic link in the revised manuscript and rewritten the relevant sections to make this connection explicit.

Modification in the manuscript:

“To gain deeper insight into the mechanisms underlying wave formation, we imaged the dynamics of individual bacteria from the fingering regions toward the center of the biofilm. This distinction is critical because, unlike the biofilm center, the edges do not generate waves. We observed that bacteria near the fingering regions remain motile and exhibit collective flow. In contrast, bacteria at the biofilm center are surface-attached and undergo periodic lifting motions. This behavior strongly resembles Mexican-wave dynamics.”

“We further found that the central region of the biofilm is mechanically more elastic, whereas the edge regions—where wave formation is absent—are motile. These observations suggest that gradual biofilm maturation is a key factor that transforms motile bacteria into a periodically moving but spatially constrained state. Consistent with this picture, the PAO1 strain, which has a strong biofilm-forming capability, completely suppresses surface oscillations. In contrast, the PA14 strain exhibits intermediate behavior, sustaining a partial transition between motile and locally constrained dynamics. Remarkably, signatures of this transition and wave generation are already detectable at the earliest stages of finger formation.”

Strengths:

The report of mechanical waves in bacterial collectives. The mechanism has potential application in a multicellular context, such as morphogenesis.

We thank the reviewer for the positive assessment and for highlighting this potential broad impact of our findings.

Weaknesses:

My most serious concern is about left-right symmetry breaking. I fail to see how the data in Figure 6 shows LR symmetry breaking. All they show is in-out directionality, which is a boundary condition. LR SM means breaking of mirror symmetry - the pattern cannot be superimposed on its mirror image using only rigid body transformations (translation and rotation) - as far as I am aware, this condition is not satisfied in this pattern-forming system.

We thank the reviewer for pointing out this critical issue. We acknowledge that we overlooked the distinction between biological and physical definitions of left–right symmetry in our initial submission, and we agree that our terminology was confusing.

In developmental biology, the term “left–right symmetry breaking” is often used to describe asymmetric flows generated by nodal cilia, which subsequently establish developmental asymmetry. This usage differs fundamentally from the physical definition of mirror symmetry breaking, which refers to chirality switching upon mirror reflection. As the reviewer correctly noted, our system does not exhibit mirror symmetry breaking in this strict physical sense.

To avoid confusion, we have revised the manuscript and replaced the term left–right symmetry breaking with left–right asymmetry between the edge and the center of the biofilm. This asymmetry arises from frequency gradients across the biofilm and is not a trivial boundary effect. For circular colonies, this phenomenon is more accurately described as radial asymmetry. We have rewritten the relevant sections of the manuscript to clarify this distinction and prevent misinterpretation.

Reviewer #2 (Public review):

Summary:

This manuscript by Altin et al. examines the dynamics of bacterial assemblies, building on previously published work documenting mechanical spiral waves. The authors show that the emergent dynamics can be influenced by various factors, including the strain of bacteria and water content in the sample. While the topic of this paper would be of broad interest, and the preliminary results are certainly interesting, various aspects of this paper are underdeveloped and require further exploration.

Strengths:

One of the nice features of this system is the ability to transition between the different states based on the addition or withdrawal of water. The authors use a similar experimental model system and mathematical model to previously published work (Reference 49), but extend by showing that the behaviour can be modified through simple interventions. Specifically, the authors show that adding water droplets or drying the sample through heating can result in changes in the observed wave structure. This represents a possible way of controlling active matter.

The mathematical model proposed in this paper involves a phase-oscillator model of Kuramotostyle coupling (similar to previously reported models). A non-reciprocal phase lag is introduced in order to facilitate the patterns seen in experiments. The qualitative agreement in the behaviour is quite striking, showing both spiral waves and travelling waves.

We thank the reviewer for the positive assessment and for pointing out areas that required further development. The reviewer is correct that our work builds on previously reported bacterial spiral wave systems; however, there are several significant differences that we now emphasize more clearly in the revised manuscript.

First, our study involves a different bacterial species and reveals a distinct dynamical process: the waves we report are strictly localized on the surface of the biofilm, in contrast to the bulk oscillations detected through density fluctuations in the earlier work (Ref. 49). The surface waves in our system resemble “Mexican wave”-like motions, in which surface bacteria periodically lift upward. To highlight this key distinction, we performed new imaging experiments that directly visualize this process. (New Video 5 and 6, Author response image 1).

Second, we systematically compared different bacterial strains, including pathogenic species such as P. aeruginosa PA14 and PAO1, alongside our BSL-1 strain. This comparative approach demonstrates that the observed phenomenon spans strains with different pathogenicity levels, and genetic variations while also showing that our strain provides a safer and more broadly usable model system for laboratory investigations.

Third, the modeling frameworks differ. Whereas the referred study relied primarily on phase models similar to those used in cilia systems, we combine a delayed Kuramoto-style oscillator model with an active solid model. This combination provides both a phenomenological description and a physical interpretation of the collective dynamics. We acknowledge that, in the original submission, the physical interpretation of the model in relation to our experimental system was underdeveloped. In the revision, we have now established this link explicitly through the elasticity and elasto active coupling of the biofilm. Specifically, we show that the transition from motile to biofilm states is accompanied by changes in elasticity, which directly influence the observed transitions between different types of wave defects. This connection is consistent with prior theoretical works and has even been only studied in robotic active matter systems.

Together, these clarifications and new results reinforce the novelty of our findings and establish a stronger connection between the experiments and the modeling framework.

Author response image 1.

Comparison between the elastic biofilm core and the motile colony edge. Highresolution video recordings revealing individual bacterial motion highlight the key physical differences driving wave-generating. Time-lapse snapshots show that bacteria at the colony edge move freely and form fingering structures, whereas bacteria in the elastic central biofilm periodically lift vertically, producing a Mexican-wave–like collective motion across the surface. See new Video

Weaknesses:

The principal observation of the paper - that spiral waves emerge in these systems and can be controlled in various ways - is not linked to microscale dynamics at the cell level. It is recognised that hydrodynamics can introduce non-reciprocity, an essential ingredient of this model. However, in this work the authors have not identified a physical mechanism for the lag, e.g., either through steric interactions or hydrodynamic disturbances. This is also relevant in the phase oscillator modelling section. In low Reynolds number flows, dynamics are instantaneously determined. In this light, what does the phase lag term represent?

The reviewer is correct that, at low Reynolds numbers, fluid dynamics are instantaneous and do not generate real temporal delays. However, nonreciprocity in hydrodynamic interactions can still emerge from the tensorial structure of the Blake–Oseen Green’s function. In this formalism, the effective asymmetry can be represented mathematically as a phase-lag–like term. This has been theoretically demonstrated in Ref.40. While this is not a literal time delay, it functions analogously by breaking odd symmetry in the coupling.

In our system, strong long-range hydrodynamic interactions are absent, as the bacteria are embedded in an elastic biofilm matrix. Instead, the dominant interactions are active elastic couplings mediated by pili and biofilm structure. The elastic solid model behaves in a way that is conceptually similar to the hydrodynamic case: pili-induced deformations of the elastic medium produce anisotropic stresses that play a role analogous to the tensorial hydrodynamic Green’s function. Thus, the phase-lag term in our Kuramoto-based model can be interpreted as an effective representation of these nonreciprocal elastic interactions.

We have clarified this point in the revised manuscript by explicitly connecting the phenomenological phase-lag term to the underlying elastic coupling in biofilms.

What is the origin of the coupling term, b? Can this be varied systematically or derived from experimental measurements or parameters?

The term b represents the enhanced elasto-active coupling of the pili process. The length of the Pili varies, and the elongated Pili has more potential to modulate the coupling between bacteria which is known to depend on a critical threshold. This process resembles the pinning dynamics and is driven by the activity of molecular motors within the pili machinery. However, the detailed mechanisms that set the effective coupling strength remain highly complex and are not yet fully understood.

At present, we do not have a direct way to systematically manipulate b in experiments. A major technical limitation is the nanoscale nature of type IV pili: these protein assemblies are extremely small and difficult to monitor or manipulate directly. Even basic tools such as GFP-based labeling have proven challenging to implement, which restricts our ability to track the detailed dynamics of these structures in live biofilms.

While we cannot currently derive b directly from experimental parameters, we emphasize in the revised manuscript that b should be understood as an effective parameter capturing the excitability of pili retractions. We also highlight this limitation and note that future advances in molecular imaging and manipulation of pili will be essential for quantitatively linking b to microscopic processes.

Classification of wave properties is an important aspect of this paper, but is not accomplished in a quantitative sense. What is the method for distinguishing between travelling and spiral waves? There is a range of quantitative tools that could be used to investigate these dynamics (and also compare quantitatively with the models). For example, examining the correlation functions and order parameters could assist with the extraction of wave features (see extensive literature on oscillator models).

We thank the reviewer for emphasizing this important point. In the revised manuscript, we have incorporated the classic Kuramoto order parameter (S) to characterize the dynamics in our model simulations. However, this metric is not directly applicable to our experimental system, because we cannot resolve the phase of individual bacteria at large scales.

Instead, we have focused on a flux-based parameter, as previously used in Ref. 40, which can be measured experimentally from collective surface dynamics. Interestingly, we find that the directional flux extracted from our experimental movies closely matches the trends predicted by the model order parameter. We suspect that this similarity arises from the combination of our optical illumination method and the characteristic surface modulations of the biofilm. While we currently lack a rigorous theoretical justification for this correspondence, so we want to keep this discussion in the review document.

In summary, we now use the classic Kuramoto order parameter in simulations and rely on the experimentally accessible flux measure for our experimental data. This dual approach allows us to compare model and experiment in a consistent manner.

Author response image 2.

Critical order parameters of the coupled biofilm system. (a) The Kuramoto global order parameter increases continuously as the system becomes globally synchronized. In contrast, in the nonreciprocally coupled system the order parameter saturates at a critical level. (b) In the experimentally observed biofilm, however the flux generated by the coupled oscillations provides a more appropriate measure of synchronization. Blue curves indicate directionally propagating planar waves, red curves correspond to spiral wave formation, and green curves represent the globally synchronized reciprocal system.

Author response image 3.

Comparison of flux profiles of the simulations with experimental measurements. Directional optical illumination enhances the flux term on the surface of the biofilm.

The methodology of changing the dynamics through moisture content appears to be slightly underdeveloped, e.g., adding water involves a droplet, and removing water is accomplished by heating (which presumably could cause other effects). Could the dynamics not be controlled more directly by varying the humidity?

We thank the reviewer for this valuable suggestion. Our results indicate that water content in the biofilm plays a key role in driving the transition to the biofilm state by modulating its elasticity. During the initial submission, we did not know how to systematically vary humidity without simultaneously altering temperature. Standard approaches typically involve water evaporation in controlled chambers, which inherently changes both parameters.

Following the reviewer’s recommendation, we first measured the ambient moisture levels inside closed culture plates. To our surprise, the relative humidity was already ~98%, leaving virtually no room to increase it further. We then attempted to decrease humidity by flowing dry synthetic air, but even under these conditions we could not reduce it below ~85%, and achieving this required unrealistically high flow rates. Moreover, we noticed that in closed-lid NGM plates, evaporation is already substantial, and when the lid is left open the evaporation rate reaches ~1 µm/s. This rapid surface thinning severely limits the quality of long-term time-lapse imaging.

Taken together, these technical constraints explain why we have to reliy on localized perturbations such as water droplets and heating rather than global humidity control. We have clarified this point in the revised manuscript and now explicitly discuss both the challenges and limitations of humidity-based approaches.

At the same time, the authors also mention that temperature itself plays a role in shaping the behaviour. What is the mechanism for this? Is it just through evaporation? Since the frequency increases with temperature, could it just be that activity increases with temperature?

We thank the reviewer for raising this critical point. We believe that temperature has two distinct impacts operating on different timescales.

Short timescale (~minutes): We observed that biofilm oscillations respond to temperature changes very rapidly and in a reversible manner. This timescale is too short to be explained by modulation of water content or bulk elasticity of the biofilm. Instead, we attribute the immediate frequency increase to enhanced biological activity of the bacteria at elevated temperatures.

Long timescale (~tens of minutes to hours): During processes such as the transition from planar to spiral waves, prolonged heating can significantly alter the biofilm structure. These changes are not reversible and likely involve modifications of elasticity and other structural properties.

In the modeling framework, the short-timescale effect is represented as an increase in the active force term, while the long-timescale effect is captured by concurrent changes in both the active force and the elastic properties of the biofilm. We have clarified this mechanism and its representation in the revised manuscript.

Reviewer #3 (Public review):

Summary:

This manuscript presents a novel investigation into unidirectionally propagating waves observed on the surface of Pseudomonas nitroreducens bacterial biofilms. The authors explore how these waves, initially spiral in form, transition into combinations of spiral, target, and planar patterns. The study identifies the periodic extension-retraction cycles of type IV pili as the driving mechanism for wave propagation, which preferentially moves from the colony's edge to its center. Furthermore, the manuscript proposes two theoretical models-a phase-oscillator model and a continuum active solid model-to reproduce these phenomena, and demonstrates how external manipulations (e.g., water droplets, temperature, PEG) can control wave patterns and direction, often correlating with oscillation frequency gradients. The work aims to bridge the fields of activematter physics and bacterial biophysics by providing both experimental observations and theoretical frameworks for understanding these complex biological wave phenomena.

We thank the reviewer for the positive assessment of our work and for highlighting both the novelty and the key contributions of our study.

Strengths:

The experimental discovery of unidirectionally propagating waves on bacterial biofilms is highly intriguing and represents a significant contribution to both microbiology and active-matter physics.

The detailed observations of wave pattern transitions (spiral to target to planar) and their response to various environmental perturbations (water, temperature, PEG) provide valuable empirical data. The identification of type IV pili as the driving force offers a concrete biological mechanism. The observed correlation between frequency gradients and wave direction is a compelling finding with potential for broader implications in understanding biological pattern formation. This work has the potential to stimulate further research in the collective behavior of living systems and the physical principles underlying biological organization.

We thank the reviewer once again for emphasizing the importance of wave directionality. We also believe that this phenomenon may provide insight into early symmetry-breaking processes observed in developmental biology, where oxygen or nutrient gradients in dense environments could play a similar role.

Weaknesses:

The manuscript attempts to link unidirectional wave propagation to non-reciprocal couplings but ultimately shows that the wave direction is determined by the gradient of the oscillation frequency. The couplings in the two theoretical models are both isotropic and thus cannot dictate the wave direction. A clear distinction should be made between non-reciprocity as a source of wave generation and non-uniformity as a controlling factor of wave direction.

We greatly appreciate the reviewer’s careful evaluation, particularly for highlighting this important and often confusing distinction. The relationship between nonreciprocity, spontaneous symmetry breaking, and frequency gradients has also been a challenging concept for us and required significant effort to clarify.

Recent theoretical studies have established that traveling wave formation requires nonreciprocity, which provides a framework for understanding phenomena ranging from spiral to target and planar waves. In our system, nonreciprocity arises between the displacement field (U) and the pili force vector (P): as a result in broken phase U effectively “chases” P, breaking PT symmetry locally and thereby enabling the generation of local directional flux and traveling waves. In this sense, nonreciprocity is essential for travelling wave generation and spontaneous symmetry breaking in either direction.

However, we now agree that global directionality (always from right to left, or edge to center) is set by an independent factor—namely, the oscillation frequency gradient across the biofilm. Thus, while nonreciprocity determines whether waves can travel, frequency gradients determine the large-scale direction in which they propagate. Put differently, PT symmetry is already broken spiral waves due to nonreciprocity, but global asymmetry (frequency gradients) is required to align the overall propagation in one direction.

We have clarified this distinction in the revised manuscript, emphasizing that nonreciprocity is a necessary ingredient for travelling wave generation, whereas global asymmetry controls global wave direction.

Modification in the manuscript:

“We should note that traveling waves indicate broken PT symmetry between these fields triggered by nonreciprocity, with spiral waves serving as a classic signature of this phenomenon. A further transition from spiral to planar waves reflects an overall asymmetry in the frequency profile, which is not directly related to PT-symmetry breaking.”

The relationship between the phase oscillator model and the active solid model is unclear. Given that U and P are both dynamical variables evolving in three-dimensional space, defining the phase Φ precisely in the phase space spanned by U and P could be challenging. A graphical illustration of the definition of Φ would be beneficial. To ensure reproducibility of the numerical results, the parameter values used in the numerical simulations and an explicit definition of the elastic force in the active solid model should be provided.

We agree with the reviewer that the relationship between the phase oscillator model and the active solid model can be confusing, but establishing this link is essential to connect different modeling approaches in the literature. As the reviewer notes, in a fully three-dimensional setting with freely moving bacteria, defining the oscillation phase (Φ) in the phase space spanned by U and P is indeed complicated.

However, our recent imaging results show that bacteria within the biofilm do not undergo large translational motions but instead exhibit periodic “Mexican wave”-like oscillations. These oscillations are confined to a restricted phase space, which allows us to define Φ in a straightforward way. In this context, the phase oscillator model becomes a natural reduction of the dynamics.

Similarly, in the active solid (or active gel) model, we can plot not only the displacement and force vectors but also the local phase, which shows strong agreement with the phenomenological Kuramoto-style model. To make this connection clearer, we have now included a schematic illustration in the revised manuscript that explicitly shows how Φ is defined in the reduced phase space, and we provide the parameter values used in the simulations as well as the explicit definition of the elastic force in the active solid model to ensure reproducibility.

The link between the theoretical models and experimental results is weak. For example, the propagation of the kink from the lower to the higher part of the surface (Figure 1e) could be addressed within the framework of the active solid model. The mechanism of transition from spiral to target waves (Figure 3a), b)) requires clarification, identifying which model parameter is crucial for inducing this transition. The wave propagation toward the lower frequency side is numerically demonstrated using the phase oscillator model, but a physical or intuitive explanation for this phenomenon is missing. Also, the wave transitions induced by the addition of water droplets and temperature rise are not linked to specific parameters in the theoretical models.

We thank the reviewer for highlighting this important weakness, which was also consistently noted by the other reviewers. We fully agree that the link between our theoretical models and experimental results required significant strengthening.

With improved imaging in the revised study, we were able to uncover additional connections that help establish this link more clearly. We acknowledge that our ability to measure detailed biofilm parameters is limited, which restricts us from providing fully quantitative mappings. Nonetheless, based on the reviewers’ suggestions, we carried out additional imaging and simulations to compare bacterial dynamics at the colony edge and within the biofilm surface. These data confirm that cells within the biofilm undergo restricted, “Mexican wave”-like oscillations, emphasizing the critical role of elasticity in governing the collective dynamics.

Experimentally, we found that adding water or PEG, or alternatively inducing drying, strongly modulates the effective elasticity of the biofilm. Within the active solid framework, elasticity and the elasto-active coupling are the key parameters controlling the system. By tuning these parameters in simulations, we could reproduce the qualitative transitions observed experimentally. Specifically, we observed that:

At low elasticity, topological defects are mobile and can move, merge, or annihilate, leading to the emergence of planar waves.

At high elasticity, defects remain pinned, across the biofilm surface, dominating the dynamics.

These observations suggest that the motility of defects is the crucial parameter governing the transition between spiral, target, and planar waves. Although we cannot independently manipulate each parameter in experiments, varying the moisture content provides an effective and experimentally accessible control.

Finally, our simulations and new analyses reveal that spiral defect cores can move and merge to form target waves or annihilate entirely—processes that we also observe experimentally. This rich dynamical behavior underscores the importance of elasticity in shaping pattern transitions, and we believe it warrants further theoretical exploration. We have clarified this connection and its implications in the revised manuscript.

First, we compare defect dynamics in both Kuramoto-based simulations and the active solid model. Both systems exhibit similar defect-survival behavior. As shown in the review , pairs of unlike (+/−) defects can stably persist only at high nonreciprocity. We further quantify this behavior by plotting the separation distances between unlike defect pairs and find that short-range defect separations are possible exclusively in the high-nonreciprocity regime Supplementary Figure 11.

This high-nonreciprocity regime corresponds to the dry biofilm state. Increasing moisture reduces elasticity, leading to the loss of stable defect dynamics and promoting the annihilation of unlike defect pairs, which in turn drives the system toward target-wave formation and ultimately planar waves. Conversely, heating the biofilm removes water, enhances elasticity, and increases the system’s ability to sustain closely separated defect pairs.

Experimentally, we further observe that removing water by heating enhances surface nonuniformities, which readily trigger defect-pair formation. To investigate this mechanism, we performed additional simulations in which local nonuniformities were introduced Supplementary Figure 12. Consistent with experiments, defect-pair generation occurs only at high nonreciprocity, where pairs of unlike defects can be stably maintained. Experimental observation (Author response image 4) also show that surface nonuniformities on the biofilm surface similarly trigger the formation of closely separated defect pairs. We have updated the details of the defect dynamics in the revised manuscript to clarify the transition between these waves.

Author response image 4.

Experimental observation showing that small surface nonuniformities on the biofilm surface trigger the formation of closely separated defect pairs. Arrows indicate the position of the nonuniformities

Modification in the manuscript:

Defect dynamics controlling the transition between spiral to target waves

“To better understand the dynamics of the transition between different form of the waves we focused on numerical simulations. We noticed that the motility of defects is the crucial parameter governing the transition between spiral, target, and planar waves varying the moisture content provides an effective and experimentally accessible control this motility. Our analyses revealed that spiral defect cores can move and merge to form target waves or annihilate entirely—processes that we also observe experimentally. This rich dynamical behavior underscores the importance of elasticity in shaping pattern transitions. First, we compare defect dynamics in both Kuramotobased simulations and the active solid model. Both systems exhibit similar defect-survival behavior. As shown in Supplementary Figure10, pairs of unlike (+/−) defects can stably persist only at high nonreciprocity. We further quantify this behavior by plotting the separation distances between unlike defect pairs and find that short-range defect separations are possible exclusively in the high-nonreciprocity regime (Supplementary Figure11). This high-nonreciprocity regime corresponds to the dry biofilm state. Increasing moisture reduces elasticity, leading to the loss of stable defect dynamics and promoting the annihilation of unlike defect pairs, which in turn drives the system toward target-wave formation and ultimately planar waves. Conversely, heating the biofilm removes water, enhances elasticity, and increases the system’s ability to sustain closely separated defect pairs. Experimentally, we further observe that removing water by heating enhances surface nonuniformities, which readily trigger defect-pair formation (Supplementary Video9). To investigate this mechanism, we performed additional simulations in which local nonuniformities were introduced (Supplementary Video12-13). Consistent with experiments, defect-pair generation occurs only at high nonreciprocity, where pairs of unlike defects can be stably maintained. Experimental observation (Supplementary Video9) also show that surface nonuniformities on the biofilm surface similarly trigger the formation of closely separated defect pairs.”

All the recommended points have been addressed in the revised manuscript.

Author response:

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

Reviewer #1 (Public review):

Summary

Sullivan and colleagues examined the modulation of reflexive visuomotor responses during collaboration between pairs of participants performing a joint reaching movement to a target. In their experiments, the players jointly controlled a cursor that they had to move towards narrow or wide targets. In each experimental block, each participant had a different type of target they had to move the joint cursor to. During the experiment, the authors used lateral perturbation of the cursor to test participants’ fast feedback responses to the different target types. The authors suggest participants integrate the target type and related cost of their partner into their own movements, which suggests that visuomotor gains are affected by the partner’s task.

Strengths

The topic of the manuscript is very interesting, and the authors are using well established methodology to test their hypothesis. They combine experimental studies with optimal control models to further support their work. Overall, the manuscript is very timely and shows important findings - that the feedback responses reflect both our and our partner’s tasks.

We thank the reviewer for the positive comments regarding our work.

Weaknesses

However, in the current version of the manuscript, I believe the results could also be interpreted differently, which suggest that the authors should provide further support for their hypothesis and conclusions.

Major Comments

(1) Results of the relevant conditions:

In addition to the authors’ explanation regarding the results, it is also possible that the results represent a simple modulation of the reflexive response to a scaled version of cursor movement. That is, when the cursor is partially controlled by a partner, which also contributes to reducing movement error, it can also be interpreted by the sensorimotor system as a scaling of hand-to-cursor movement. In this case, the reflexes are modulated according to a scaling factor (how much do I need to move to bring the cursor to the target). I believe that a single-agent simulation of an OFC model with a scaling factor in the lateral direction can generate the same predictions as those presented by the authors in this study. In other words, maybe the controller has learned about the nature of the perturbation in each specific context, that in some conditions I need to control strongly, whereas in others I do not (without having any model of the partner). I suggest that the authors demonstrate how they can distinguish their interpretation of the results from other explanations.

We thank the reviewer for the thoughtful comment. While it is possible that the change in the visuomotor feedback responses could be just from a scaling factor. This hypothesis could explain the difference between two conditions, but would fail to explain differences between two other conditions. Specifically, this hypothesis could explain a decrease in involuntary visuomotor feedback responses between partner-irrelevant/self-relevant and partner-relevant/self-relevant. Critically, this hypothesis could not explain the difference between partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant. That is, there is no reason to scale a response to correct for a partner’s relevant target when your own target is irrelevant. However, our finding that there is a greater involuntary visuomotor feedback response in partner-relevant/self-irrelevant compared to partner-irrelevant/self-irrelevant is predicted by the notion that humans form a representation of others and consider their movement costs.

We have added a paragraph in the discussion to justify our hypothesis over the scaling factor hypothesis.

“Our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses can parsimoniously explain all of our experimental findings. There are a few alternative hypotheses that could explain a subset of results. One alternative hypothesis is that participants simply learned the hand to center cursor mapping in each experimental condition. That is, instead of using a model of their partner, participants simply adapted to the dynamics of the center cursor. However, this hypothesis would not predict an increased involuntary visuomotor feedback response in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-irrelevant condition. If participants did not form a model of their partner nor consider their partner’s costs, then they would not display an increased feedback response when they had an irrelevant target and their partner’s target was relevant. An increased feedback response to help a partner achieve their goal is captured by our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses.”

(2) The effect of the partner target:

The authors presented both self and partner targets together. While the effect of each target type, presented separately, is known, it is unclear how presenting both simultaneously affects individual response. That is, does a small target with a background of the wide target affect the reflexive response in the case of a single participant moving? The results of Experiment 2, comparing the case of partner- and self-relevant targets versus partner-irrelevant and self-relevant targets, may suggest that the system acted based on the relevant target, regardless of the presence and instructions regarding the self-target.

We thank the reviewer for bringing up another valid point, which we discussed at length as a group when designing the experiment. The reviewer is correct in pointing out the lack of difference in the involuntary epoch between the partner-relevant/self-relevant and partner-irrelevant/self-relevant could potentially suggest that the sensorimotor system acted based on only relevant targets, irrespective if it was a self or partner relevant target. While the effect of the simultaneous presentation of a narrow and wide target on an individual’s response by themselves is unknown, comparing the differences between our other experimental conditions control for this potential confound. Participants viewed a wide target and a narrow target on the screen, in both the partner-irrelevant/self-relevant condition and the partner-relevant/self-irrelevant condition. Crucially, we found that the visuomotor feedback responses were greater in the partner-irrelevant/self-relevant condition compared to the partner-relevant/self-irrelevant condition in both Experiment 1 and 2. That is, participants were able to distinguish between the self-target and partner target and appropriately modify their feedback responses in both Experiment 1 and 2, despite there being both a wide and narrow target on the screen in both conditions. Given that we found different visuomotor feedback responses between the two conditions that had both a narrow and wide target, this rules out the alternative hypothesis that the sensorimotor system acted based just on a relevant target being present. We have added to our discussion to clarify this point.

“Another alternative hypothesis would be that the sensorimotor system was responding only to the relevant target displayed on the screen. Again, this hypothesis would only explain a subset of our results. In particular, this relevant target hypothesis cannot explain the observed feedback response differences between the partner-relevant/self-irrelevant and partner-irrelevant/self-relevant conditions in both Experiments 1 and 2.”

(3) Experiment instructions:

It is unclear what the general instructions were for the participants and whether the instructions provided set the proposed weighted cost, which could be altered with different instructions.

Our instructions explicitly informed participants that their performance bonus was only based on them stabilizing within their own self-target within the time constraint. We have added the following in the methods to emphasize this instruction.

“In other words, we ensured participants had a clear understanding that their performance in the task was only based on stabilizing the center cursor in their own self-target within the time constraint. Therefore, the instructions and timing constraints did not enforce participants to work together.”

(4) Some work has shown that the gain of visuomotor feedback responses reflects the time to target and that this is updated online after a perturbation (Cesonis & Franklin, 2020, eNeuro; Cesonis and Franklin, 2021, NBDT; also related to Crevecoeur et al., 2013, J Neurophysiol). These models would predict different feedback gains depending on the distance remaining to the target for the participant and the time to correct for the jump, which is directly affected by the small or large targets. Could this time be used to target instead of explaining the results? I don’t believe that this is the case, but the authors should try to rule out other interpretations. This is maybe a minor point, but perhaps more important is the location (&time remaining) for each participant at the time of the jump. It appears from the figures that this might be affected by the condition (given the change in movement lengths - see Figure 3 B & C). If this is the case, then could some of the feedback gain be related to these parameters and not the model of the partner, as suggested? Some evidence to rule this out would be a good addition to the paper - perhaps the distance of each partner at the time of the perturbation, for example. In addition, please analyze the synchrony of the two partners’ movements.

(1) Time to target and forward position

The reviewer raises an interesting point. In our task, the cursor/target jump occurs once the center cursor crosses 6.25 cm from the start. We analyzed the time it took for the center cursor to intercept the targets from perturbation onset (Supplementary D). In Experiment 1, an ANOVA with center cursor time-to-target as the dependent variable showed no main effect of self-target (F[1,47] = 2.45, p = 0.124) or partner target (F[1,47] = 2.50, p=0.120), nor any interaction (F[1,47] = 1.97, p = 0.166). In Experiment 2, an ANOVA with center cursor time-to-target as the dependent variable showed a significant interaction (F[1,47] = 5.87, p = 0.019). Post-hoc mean comparisons showed that only the difference between the partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant condition was significant (p = 0.006). Given that only one comparison in Experiment 2 showed a difference in time-to-target, we do not believe that time-to-target was a significant driver of the change in involuntary visuomotor feedback responses observed between conditions. While time-to-target is likely a metric the nervous system modifies feedback gains around, our results suggest that the nervous system can also use a partner model to modify feedback gains. We have added a supplemental analysis on time to target

“Previous work by Česonis and Franklin (2020) showed that time to-target is a key variable the sensorimotor system uses to modify feedback responses. In their experiment, they manipulated the time-to-target of the participant’s cursor, while controlling for other movement parameters (e.g., distance from goal) [1]. When compared to classical optimal feedback control models, they showed that a model that modifies feedback responses based on time-to-target best predicted their results. In our task, it’s possible that the time-to-target could have influenced visuomotor feedback responses, since the distance to the center of the target is greater for a narrow target than a wide target on perturbation trials.”

“We calculated the time from perturbation onset to the center cursor reaching the forward position of the targets (Supplementary Fig. S5). In Experiment1, an ANOVA with center cursor time-to-target as the dependent variable showed no main effect of self-target (F[1,47]=2.45,p=0.124) or partner target (F[1,47] = 2.50, p=0.120), nor any interaction (F[1,47] = 1.97, p = 0.166). In Experiment2, an ANOVA with center cursor time-to-target as the dependent variable showed a significant interaction (F [1,47] = 5.87, p = 0.019). Post-hoc mean comparisons showed that only the difference between the partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant condition was significant (p=0.006). Although time-to-target and hand position are important variables for the control ofmovement,[1,2,3] they are likely not driving factors of the different in voluntary visuomotor feedback responses between our experimental conditions.”

However, it is possible that the participant forward position at perturbation onset could also influence the involuntary feedback response. We show the forward positions at perturbation onset in Supplementary D. Statistical analysis of the forward positions in Experiment 1 showed a main effect of self-target (F[1,47] = 12.72, p < 0.001), main effect of partner target (F[1,47] = 12.82, p < 0.001), and no interaction (F[1,47] = 0.00, P = 0.991). We see the same trend in experiment 2, showing a main effect of self-target (F[1,47] = 12.11, p < 0.001), main effect of partner target (F[1,47] = 12.04, p < 0.001), and no interaction (F[1,47] = 0.00, p = 0.986). The fact that there was no interaction implies that the results could not solely be due to forward position. Nevertheless, given there were main effects, we proceeded to run an ANCOVA on the involuntary visuomotor feedback responses with forward position as a covariate. For experiment 1, we still observed a significant interaction between self and partner target (F[1,47] = 43.14, p < 0.001). Further, we also observed no significant main effect of forward position on the involuntary visuomotor feedback responses. The ANCOVA for Experiment 2 also showed that there was still a significant interaction of self and partner target on the involuntary visuomotor feedback responses (F[1,47] = 9.80, p = 0.002). However, here we did find a significant main effect of the forward position (F[1,47] = 5.06, p = 0.026). Therefore, we ran follow-up mean comparisons with the covariate adjusted means. We found the same statistical trend as reported in the main results. We found significant differences between the partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant conditions (p = 0.003), partner-relevant/self-irrelevant and partner-irrelevant/self-relevant conditions (p < 0.001), partner-relevant/self-irrelevant and partner-relevant/self-relevant conditions (p < 0.001). We found no significant difference between the partner-irrelevant/self-relevant and partner-relevant/self-relevant conditions (p = 0.381). Given that there was no main effect of forward position in Experiment 1, and that our adjusted mean comparisons in Experiment 2 showed the same trends as the unadjusted mean comparisons in the main manuscript, our results show that the forward position of the participants is not a significant factor in explaining the differences in involuntary visuomotor feedback responses between conditions.

“Supplementary Fig. 6 shows the participant hand forward position at perturbation onset time for Experiment 1 (A) and Experiment 2 (B). It is possible that the participant forward hand position at perturbation onset time could influence their visuomotor feedback responses. Therefore, we ran an ANCOVA with self-target and partner target as factors, and participant forward hand position at perturbation onset time as a covariate. In Experiment 1, we found no main affect of participant forward hand position on involuntary visuomotor feedback responses (F[1,47] = 1.466, p = 0.228). Further, when including the covariate, we still found a significant interaction between self-target and partner target on in voluntary visuomotor feedback responses (F[1,47]=43.2, p<0.001).”

“In Experiment 2, we found a significant main effect of participant forward hand position on involuntary visuomotor feedback responses (F[1,47] = 6.73, p = 0.010). We still found a significant interaction between self-target and partner target (F[1,47] = 9.78, p = 0.002). Since we found a main effect of participant forward hand position, we calculated the adjusted means of the involuntary visuomotor feedback responses. We then performed follow-up mean comparisons on the adjusted means of the involuntary visuomotor feedback responses (using emmeans in R). We found the same significant trends as the unadjusted means in the main manuscript. Specifically we found involuntary visuomotor feedback responses to be: significantly greater in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-irrelevant condition (p =0.003),significantly greater in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-relevant condition (p<0.001), significantly greater in the partner-relevant/self-relevant condition compared to the partner-relevant/self-irrelevant condition (p<0.001),and not different between the partner-irrelevant/self-relevant and partner-relevant/self-relevant conditions (p = 0.824).”

We have also included in the discussion how time-to-target and participant forward hand position are important control variables to consider, and their potential relationship to our findings.

“Finally, we also considered whether time to target [1,2]. (Supplementary D), participant forward hand position (Supplementary E), or learning [4] (Supplementary G-H) influenced feedback responses, but found that none impacted the observed differences between experimental conditions nor changed our interpretation. Our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses parsimoniously accounts for the differences observed between all conditions.”

(2) Synchrony

In our task, participants movements were not self-initiated. We had them begin the movement as soon as they hear an audible tone so that they would begin their movements at as similar a time as possible. We have analyzed the movement onset synchrony between participants within a pair, shown in Supplementary F.

Supplementary: “We calculated movement onset times at the time that the participants left the start target [8]. We then took the absolute value of the difference between the participants within a pair as a measure of movement onset synchrony. For Experiment 1, an ANOVA with movement onset synchrony as the dependent variable showed no main effect of self-target (F[1,47] = 1.38, p = 0.252), no main effect of partner target (F[1,47] = 0.057, p = 0.813), and no interaction (F[1,47] = 0.45, p = 0.508). For Experiment 2, an ANOVA with movement onset synchrony as the dependent variable showed no main effect of self-target (F[1,47] = 0.07, p = 0.788), no main effect of partner target (F[1,47] = 2.75, p = 0.111), and no interaction (F[1,47] = 2.31, p = 0.142).”

Further, we have modified our methods to emphasize that participants within a pair generally began their movement at the same time.

“Instead of self-initiating their movements, we specifically had participants move at the sound of a tone so that the movement onset between participants in a pair was as synchronous as possible (see Supplementary F for movement onset synchrony analysis).”

Reviewer #1 (Recommendations for the authors):

(1) Lines 291-292: One study extensively examined cursor and target jump visuomotor on set times and found no difference (Franklin et al., 2016; J Neuroscience), which strongly argues against this interpretation.

We thank the reviewer for pointing out this work. We have modified the following lines:

“However, other work by Franklin and colleagues (2016) found no difference in visuomotor feedback response latencies between cursor and target jumps [6].”

(2) Line 411: What were the instructions regarding partner performance in terms of the reward? Did you explain that individual performance alone will determine the reward?

As addressed above, we have made the following changes to emphasize the instructions given to participants.

“In other words, we ensured participants had a clear understanding that their performance in the task was only based on stabilizing the center cursor in their own self-target within the time constraint. Therefore, the instructions and timing constraints did not enforce participants to work together.”

(3) Line 506: Ten probe trials in each direction is very low. Can this still be in the transition state of the feedback response, rather than at steady state? There are many studies done looking at the learning of visuomotor responses in which changes are still occurring after several hundred trials (e.g., Franklin et al., 2017 J Neurophysiol; Franklin et al., 2008; J Neuroscience). In this experiment, each block only lasts 151 trials total if my calculations are correct. How certain are you that the results are at a steady state and not continuously changing? Perhaps with further experimental experience, the feedback responses would approach the predictions of a different model.

The reviewer raises an important point. We had run these analyses prior to submitting the manuscript and did not see anything. However, we believe this information is important to include since both we and yourself asked the same question. Specifically, we have analyzed the visuomotor feedback responses over the trials (Supplementary G), which shows little to no learning over time. Additionally, we also found no difference in the visuomotor feedback response trends between the first and second half of trials in each condition (Supplementary H). Therefore, it appears that the sensorimotor system was at steady state behaviour very quickly and we do believe that the feedback responses would approach the predictions of a different model if participants performed more trials. We have added the following

Supplementary: “Given there were 151 trials and 10 left/right probe trials for each experimental condition, it is possible that completing more trials may have lead to different involuntary visuomotor feedback responses. Therefore, we analysed the in voluntary visuomotor feedback responses over the course of each experimental condition. Visually, involuntary visuomotor feedback responses in neither Experiment 1 (Fig. S8) nor Experiment 2 (Fig. S9) show any consistent learning (see Fig. S10 for statistical analysis). Therefore, it appears participants rapidly formed a partner model based on knowledge of their movement goal to modify their involuntary visuomotor feedback responses.”

Supplementary: “Supplementary Fig. S10 shows the involuntary visuomotor feedback responses in the first half (A,C) and second half (B,D) for each experimental condition. In Experiment 1, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 37.09, p < 0.001) and second half (F[1,47] = 48.68, p < 0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (see Fig. S10A-B).”

Supplementary: “In Experiment 2, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 9.42, p = 0.004) and second half (F[1,47] = 17.40, p < 0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (Fig. S10C-D).”

Supplementary: “Showing the same involuntary visuomotor feedback response trends across the experimental conditions for the first half, second half, and all trials suggests that the sensorimotor system quickly formed a model of a partner and considered their costs to modify rapid motor responses.”

We have also added to the discussion:

“Finally, we also considered whether time to target [1,2] (Supplementary D), participant forward hand position (Supplementary E), or learning [4] (Supplementary G) influenced feedback responses, but found that none impacted the observed differences between experimental conditions nor changed our interpretation.”

(4) The authors should also discuss some of the prior work which is very relevant to the tasks studied: (Knill, Bondata & Chhabra, 2011, J Neuroscience). There may also be other papers that use this task for visuomotor feedback responses and therefore, should be included.

We have included the Knill 2011 paper and also Cross 2019 in our discussion:

“This modification of feedback responses based on a relevant/irrelevant task goal has also been shown in response to visual perturbations [7,8].”

(5) Lines 301-303: The terms ’relevant’ and ’irrelevant’ here describe different concepts than the ones used in this study. I suggest making a distinction to avoid confusion for the reader.

We thank the reviewer for pointing out that this is confusing. We’ve made the following changes to improve the clarity:

“Further, Franklin and colleagues (2008) designed a visual perturbation to be relevant or irrelevant when reaching to the same target, showing greater involuntary visuomotor feedback responses to a relevant visual perturbation compared to an irrelevant visual perturbation [9].”

(6) Line 459: The reaching movement was quite slow (25cm in about 1.2 seconds). Is this needed to ensure that both participants can complete the movements, given potentially very different start times? Please comment as this is different than many previous studies.

Participants needed to stabilize the cursor for 500ms in their target within a time constraint of 1400 - 1600 ms. Therefore, they had to reach the target between 900 - 1100 ms (before stabilizing). Additionally, participants did not perform self-initiated movements, but were required to begin their movement as soon as they heard an audible tone. Given that reaction times are ~200ms, participants had ~700 - 900 ms to reach the target, which aligns with previous research (Franklin et al. (2008), Franklin et al. (2012), Nashed et al. (2012)). We have clarified the time constraints of the task in our Methods:

“They therefore had 700 - 900 ms to first reach the target, since humans generally have response times ~200 ms, and they needed to stabilize within the target for 500 ms (i.e., 1400 - 200 - 500 = 700 ms and 1600 - 200 - 500 = 900 ms). Movement times of 700 - 900 ms are thus consistent with previous human reaching studies [4,9,10].”

(7) Reference [25] is incomplete

Thank you for catching this.

And thank you for the thoughtful and clear review. We feel it has greatly improved the quality and clarity of our manuscript!

Reviewer #2 (Public review):

Summary

Sullivan and colleagues studied the fast, involuntary, sensorimotor feedback control in interpersonal coordination. Using a cleverly designed joint-reaching experiment that separately manipulated the accuracy demands for a pair of participants, they demonstrated that the rapid visuomotor feedback response of a human participant to a sudden visual perturbation is modulated by his/her partner’s control policy and cost. The behavioral results are well-matched with the predictions of the optimal feedback control framework implemented with the dynamic game theory model. Overall, the study provides an important and novel set of results on the fast, involuntary feedback response in human motor control, in the context of interpersonal coordination.

We thank the reviewer for the kind words!

Review:

Sullivan and colleagues investigated whether fast, involuntary sensorimotor feedback control is modulated by the partner’s state (e.g., cost and control policy) during interpersonal coordination. They asked a pair of participants to make a reaching movement to control a cursor and hit a target, where the cursor’s position was a combination of each participant’s hand position. To examine fast visuomotor feedback response, the authors applied a sudden shift in either the cursor (experiment 1) or the target (experiment 2) position in the middle of movement. To test the involvement of partner’s information in the feedback response, they independently manipulated the accuracy demand for each participant by varying the lateral length of the target (i.e., a wider/narrower target has a lower/higher demand for correction when movement is perturbed). Because participants could also see their partner’s target, they could theoretically take this information (e.g., whether their partner would correct, whether their correction would help their partner, etc.) into account when responding to the sudden visual shift. Computationally, the task structure can be handled using dynamic game theory, and the partner’s feedback control policy and cost function are integrated into the optimal feedback control framework. As predicted by the model, the authors demonstrated that the rapid visuomotor feedback response to a sudden visual perturbation is modulated by the partner’s control policy and cost. When their partner’s target was narrow, they made rapid feedback corrections even when their own target was wide (no need for correction), suggesting integration of their partner’s cost function. Similarly, they made corrections to a lesser degree when both targets were narrower than when the partner’s target was wider, suggesting that the feedback correction takes the partner’s correction (i.e., feedback control policy) into account.

The strength of the current paper lies in the combination of clever behavioral experiments that independently manipulate each participant’s accuracy demand and a sophisticated computational approach that integrates optimal feedback control and dynamic game theory. Both the experimental design and data analysis sound good. While the main claim is well-supported by the results, the only current weakness is the lack of discussion of limitations and an alternative explanation. Adding these points will further strengthen the paper.

Reviewer #2 (Recommendations for the authors):

(1) While the current version is already well-written, it would be helpful for readers to further discuss the relationship between the current study and some potentially relevant studies, such as Braun et al. (2009), Ganesh et al. (2014), and Takagi et al. (2017) (2019).

Thank you for pointing out these papers that we missed, which we now cite appropriately in light of our own work. In particular, we have added the following to our discussion, including Braun et al. (2009) and Takagi et al. (2017) (2019). However, Beckers et al. (2020) showed conflicting results from Ganesh et al. (2014), and since these works are about learning, we feel it is outside the scope of our work.

“Further, others have shown that the sensorimotor system modifies movement selection according to game-theoretic predictions, [11] and that the sensorimotor system modifies movements using an estimate of the joint goal during human-human interactions [12,13].”

(2) For an alternative interpretation of the results, one could consider, for instance, that the target’s visual appearance could have served as a contextual cue for learning different movement gains in the lateral direction (e.g., whether the partner corrects the shift might be approximated as a gain change). Although less likely, this alternative account could be tested by simulation and would strengthen the argument.

This a thoughtful comment, also brought up by Reviewer 1. Here we provide our previous response that addresses this concern. While it is possible that the change in the visuomotor feedback responses could be just from a scaling factor. This hypothesis could explain the difference between two conditions, but would fail to explain differences between two other conditions. Specifically, this hypothesis could explain a decrease in involuntary visuomotor feedback responses between partner-irrelevant/self-relevant and partner-relevant/self-relevant. Critically, this hypothesis could not explain the difference between partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant. That is, there is no reason to scale a response to correct for a partner’s relevant target when your own target is irrelevant. However, our finding that there is a greater involuntary visuomotor feedback response in partner-relevant/self-irrelevant compared to partner irrelevant/self-irrelevant is predicted by the notion that humans form a representation of others and consider their movement costs.

We have added a paragraph in the discussion to justify our hypothesis over the scaling factor hypothesis.

“Our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses can parsimoniously explain all of our experimental findings. There are a few alternative hypotheses that could explain a subset of results. One alternative hypothesis is that participants simply learned the hand to center cursor mapping in each experimental condition. That is, instead of using a model of their partner, participants simply adapted to the dynamics of the center cursor. However, this hypothesis would not predict an increased involuntary visuomotor feedback response in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-irrelevant condition. If participants did not form a model of their partner nor consider their partner’s costs, then they would not display an increased feedback response when they had an irrelevant target and their partner’s target was relevant. An increased feedback response to help a partner achieve their goal is captured by our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses.”

(3) Another (maybe unlikely) alternative interpretation is that the targets’ visual appearances might have been confusing. One might find that the closed square is common to both targets for the “Partner Relevant Self Irrelevant” and the “Partner Relevant Self Relevant”, and that this might have elicited the response to perturbation in “Partner Relevant Self Irrelevant”. Related to this point, it would be informative to describe how the “cooperative” fast feedback response developed over the course of the experiment, for instance, by comparing behaviors across experimental blocks.

We have partitioned this question into two responses, relating to visual appearance of the targets and the development (i.e., learning) of visuomotor feedback responses over the course of the experiments.

(1) Participants confused by visual appearance of the targets.

We were also concerned that participants might be confused by the targets, and therefore confirmed with participants after the experiment that they correctly understood that the light grey filled rectangle was their own target and the dark grey hollow rectangle was their partners. Furthermore, in the partner-relevant/self-irrelevant, partner-irrelevant/self-relevant, and partner-relevant/self-relevant conditions, there is a small square target in each of the conditions. However, we found that the partner-irrelevant/self-relevant and partner-relevant/self-relevant conditions both elicited significantly greater involuntary visuomotor feedback responses than the partner-relevant/self-irrelevant condition. Thus, participants involuntary visuomotor feedback responses suggest that they correctly formed different representations based on an accurate understanding of the self vs partner target. The other reviewer had related comments about the visual stimuli, which we also address within the discussion.

“Another alternative hypothesis would be that the sensorimotor system was responding only to the relevant target displayed on the screen. Again, this hypothesis would only explain a subset of our results. In particular, this relevant target hypothesis cannot explain the observed differences between the partner-relevant/self-irrelevant and partner-irrelevant/self-relevant conditions in both Experiments 1 and 2.”

(2) Comparing feedback responses over time

We have included the visuomotor feedback responses over each experimental condition in Supplementary G. Notably, we did not find any learning effect, suggesting that the sensorimotor system quickly developed a model of a partner’s behaviour and used that model to modify feedback responses. We have also added a paragraph on learning to our discussion.

We’ve addressed how learning did not play a role in this study:

“Finally, we also considered whether time to target [1,2] (Supplementary D), participant forward hand position (Supplementary E), or learning [4] (Supplementary G-H) influenced feedback responses, but found that none impacted the observed differences between experimental conditions nor changed our interpretation.”

Supplementary: “Given there were 151 trials and 10 left/right probe trials for each experimental condition, it is possible that completing more trials may have lead to different in voluntary visuomotor feedback responses. Therefore, we analysed the in voluntary visuomotor feedback responses over the course of each experimental condition. Visually, involuntary visuomotor feedback responses in neither Experiment 1 (Fig. S8) nor Experiment 2 (Fig. S9) show any consistent learning (see Fig. S10 for statistical analysis). Therefore, it appears participants rapidly formed a partner model based on knowledge of their movement goal to modify their involuntary visuomotor feedback responses.”

Supplementary: “Supplementary Fig. S10 shows the involuntary visuomotor feedback responses in the first half (A,C) and second half (B,D) for each experimental condition. In Experiment 1, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 37.09, p < 0.001) and second half (F[1,47] = 48.68, p < 0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (see Fig. S10A-B).”

Supplementary: “Supplementary Fig. S10 shows the involuntary visuomotor feedback responses in the first half (A,C) and second half (B,D) for each experimental condition. In Experiment 1, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 37.09, p < 0.001) and second half (F[1,47] = 48.68, p <0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (see Fig. S10A-B).”

Supplementary: “Showing the same involuntary visuomotor feedback response trends across the experimental conditions for the first half, second half, and all trials suggests that the sensorimotor system used a model of a partner based on their goals and considered their costs to modify rapid motor responses.”

(4) It looks slightly counter intuitive (and therefore interesting) that the participant shows some amount of fast feedback responses in the “Partner Relevant Self Irrelevant” condition, since they were instructed to only consider the self-target. Based on the results, the authors suggest an altruistic feature of the motor system (lines 333-340). It would be helpful to clarify the basis for this interpretation, whether it is formally derived from the game-theoretic framework or represents a more conceptual interpretation. Providing additional explanation that translates the game-theoretic reasoning into more accessible, intuitive terms would help readers better understand and evaluate this claim.

We are glad the reviewer also finds this result interesting. The reviewer raises an important point that there needs to be a more clear explanation for why we believe this result was found. We have made the following changes to the discussion:

“Furthermore, this result is predicted by our dynamic game theory models that include the partner’s costs in the self cost function. In other words, a dynamic game theory model that selects feedback gains to minimize both the self and partner cost reflects an altruistic control policy.”

(5) Please check whether all references are displayed correctly. Some of them (e.g., 25, 65) seemed not correctly shown in the References section.

We have fixed the citation.

We thank the reviewer for providing a clear and insightful review. Their comments have significantly improved the manuscript.

References

(1) Česonis, J., & Franklin, D. W. (2020). Time-to-Target Simplifies Optimal Control of Visuomotor Feedback Responses. eneuro, 7 (2), ENEURO.0514–19.2020.

(2) Česonis, J., & Franklin, D. W. (2022). Contextual Cues Are Not Unique for Motor Learning: Task-dependant Switching of Feedback Controllers. PLOS Computational Biology, 18 (6), ed. by Haith, A. M.: e1010192.

(3) Crevecoeur, F., Kurtzer, I., Bourke, T., & Scott, S. H. (2013). Feedback Responses Rapidly Scale with the Urgency to Correct for External Perturbations. Journal of Neurophysiology, 110 (6), 1323–1332.

(4) Franklin, S., Wolpert, D. M., & Franklin, D. W. (2012). Visuomotor Feedback Gains Upregulate during the Learning of Novel Dynamics. Journal of Neurophysiology, 108 (2), 467–478.

(5) Liu, Y., Leib, R., Dudley, W., Shafti, A., Faisal, A. A., & Franklin, D. W. (2025). Partner-Sourced Haptic Feedback Rather than Environmental Inputs Drives Coordination Improvement in Human Dyadic Collaboration. Scientific Reports, 15 (1), 40347.

(6) Franklin, D. W., Reichenbach, A., Franklin, S., & Diedrichsen, J. (2016). Temporal Evolution of Spatial Computations for Visuomotor Control. The Journal of Neuroscience, 36 (8), 2329–2341.

(7) Knill, D. C., Bondada, A., & Chhabra, M. (2011). Flexible, Task-Dependent Use of Sensory Feedback to Control Hand Movements. The Journal of Neuroscience, 31 (4), 1219–1237.

(8) Cross, K. P., Cluff, T., Takei, T., & Scott, S. H. (2019). Visual Feedback Processing of the Limb Involves Two Distinct Phases. The Journal of Neuroscience, 39 (34), 6751–6765.

(9) Franklin, D. W., & Wolpert, D. M. (2008). Specificity of Reflex Adaptation for Task-Relevant Variability. The Journal of Neuroscience, 28 (52), 14165–14175.

(10) Nashed, J. Y., Crevecoeur, F., & Scott, S. H. (2012). Influence of the Behavioral Goal and Environmental Obstacles on Rapid Feedback Responses. Journal of Neurophysiology, 108 (4), 999–1009.

(11) Braun, D. A., Ortega, P. A., & Wolpert, D. M. (2009). Nash Equilibria in Multi-Agent Motor Interactions. PLoS Computational Biology, 5 (8), ed. by Friston, K. J.: e1000468.

(10) Takagi, A., Ganesh, G., Yoshioka, T., Kawato, M., & Burdet, E. (2017). Physically Interacting Individuals Estimate the Partner’s Goal to Enhance Their Movements. Nature Human Behaviour, 1 (3), 0054.

(11) Takagi, A., Hirashima, M., Nozaki, D., & Burdet, E. (2019). Individuals Physically Interacting in a Group Rapidly Coordinate Their Movement by Estimating the Collective Goal. eLife, 8 , e41328.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates how collective navigation improvements arise in homing pigeons. Building on the Sasaki & Biro (2017) experiment on homing pigeons, the authors use simulations to test seven candidate social learning strategies of varying cognitive complexity, ranging from simple route averaging to potentially cognitively demanding selective propagation of superior routes. They show that only the simplest strategy-equal route averaging-quantitatively matches the experimental data in both route efficiency and social weighting. More complex strategies, while potentially more effective, fail to align with the observed data. The authors also introduce the concept of "effective group size," showing that the chaining design leads to a strong dilution of earlier individuals' contributions. Overall, they conclude that cognitive simplicity rather than cumulative cultural evolution explains collective route improvements in pigeons.

Strengths:

The manuscript addresses an important question and provides a compelling argument that a simpler hypothesis is necessary and sufficient to explain findings of a recent influential study on pigeon route improvements, via a rigorous systematic comparison of seven alternative hypotheses. The authors should be commended for their willingness to critically re-examine established interpretations. The introduction and discussion are broad and link pigeon navigation to general debates on social learning, wisdom of crowds, and CCE.

We thank the reviewer for their positive comments.

Weaknesses:

The lack of availability of codes and data for this manuscript, especially given that it critically examines and proposes alternative hypotheses for an important published work.

We thank the reviewer for their comment. The code and data for our manuscript are an important aspect of the study, and we had intended to make them publicly available upon publication. The link to our code and data on fig share can be found here: (https://doi.org/10.6084/m9.figshare.28950032.v1). We have now revised the manuscript to include a link to our dataset.

Reviewer #2 (Public review):

Summary:

The manuscript investigates which social navigation mechanisms, with different cognitive demands, can explain experimental data collected from homing pigeons. Interestingly, the results indicate that the simplest strategy - route averaging - aligns best with the experimental data, while the most demanding strategy - selectively propagating the best route - offers no advantage. Further, the results suggest that a mixed strategy of weighted averaging may provide significant improvements.

The manuscript addresses the important problem of identifying possible mechanisms that could explain observed animal behavior by systematically comparing different candidate models. A core aspect of the study is the calculation of collective routes from individual bird routes using different models that were hypothesized to be employed by the animals, but which differ in their cognitive demands.

The manuscript is well-written, with high-quality figures supporting both the description of the approach taken and the presentation of results. The results should be of interest to a broad community of researchers investigating (collective) animal behavior, ranging from experiment to theory. The general approach and mathematical methods appear reasonable and show no obvious flaws. The statistical methods also appear.

Strengths:

The main strength of the manuscript is the systematic comparison of different meta-mechanisms for social navigation by modeling social trajectories from solitary trajectories and directly comparing them with experimental results on social navigation. The results show that the experimentally observed behavior could, in principle, arise from simple route averaging without the need to identify "knowledgeable" individuals. Another strength of the work is the establishment of a connection between social navigation behavior and the broader literature on the wisdom of crowds through the concept of effective group size.

We thank the reviewer for their positive comments.

Weaknesses:

However, there are two main weaknesses that should be addressed:

(1) The first concerns the definition of "mechanism" as used by the authors, for example, when writing "navigation mechanism." Intuitively, one might assume that what is meant is a behavioral mechanism in the sense of how behavior is generated as a dynamic process. However, here it is used at a more abstract (meta) level, referring to high-level categories such as "averaging" versus "leader-follower" dynamics. It is not used in the sense of how an individual makes decisions while moving, where the actual route followed in a social context emerges from individuals navigating while simultaneously interacting with conspecifics in space and time. In the presented work, the approach is to directly combine (global) route data of solitary birds according to the considered "meta-mechanisms" to generate social trajectories. Of course, this is not how pigeon social navigation actually works-they do not sit together before the flight and say, "This is my route, this is your route, let's combine them in this way." A mechanistic modeling approach would instead be some form of agent-based model that describes how agents move and interact in space and time. Such a "bottom-up" approach, however, has its drawbacks, including many unknown parameters and often strongly simplifying (implicit) assumptions. I do not expect the authors to conduct agent-based modeling, but at the very least, they should clearly discuss what they mean by "mechanism" and clarify that while their approach has advantages-such as naturally accounting for the statistical features of solitary routes and allowing a direct comparison of different meta-mechanisms is also limited, as it does not address how behavior is actually generated. For example, the approach lacks any explicit modeling of errors, uncertainty, or stochasticity more broadly (e.g., due to environmental influences). Thus, while the presented study yields some interesting results, it can only be considered an intermediate step toward understanding actual behavioral mechanisms.

We thank the reviewer for their comment and thoughtful suggestions. We agree that the inherent behavioral mechanisms and the biological basis of these mechanisms cannot be determined just through the navigational data alone. For instance, it remains unexplored if pigeons are adapting their behavior based only on social cues from their partners or using other navigational features such as landmarks or roads, location of the sun, geomagnetic cues or prior learnt routes. However, we do agree (as also pointed by the reviewer) that these behavioral rules generate an emergent ‘meta-mechanism’ where the bird pairs are behaving as if their preferred routes are averaged during a flight. It will be important in future work to explore the biological basis of these mechanisms, but our current approach allows us to only describe the mechanisms in a meta sense with any confidence. Considering this, we believe that our analysis is a more top-down approach towards describing the outcomes of these underlying mechanisms in an abstract sense. We would also like to point the reviewer to Dalmaijer, 2024 [1] who used a bottom up approach, using naive agents and showed that cumulative route improvements emerged in the absence of any sophisticated communication in the same dataset, in agreement with our approach. We have now added a paragraph: “It is also important to clarify that we use the terms…… that lead to these meta-mechanisms arising remain an open question.” found in lines 120-129 in our Introduction to make this clarification.

(2) While the presented study raises important questions about the applicability and viability of cumulative cultural evolution (CCE) in explaining certain animal behaviors such as social navigation, I find that it falls short in discussing them. What are the implications regarding the applicability of CCE to animal data and to previously claimed experimental evidence for CCE? Should these experiments be re-analyzed or critically reassessed? If not, why? What are good examples from animal behavior where CCE should not be doubted? Furthermore, what about the cited definitions and criteria of CCE? Are they potentially too restrictive? Should they be revised-and if so, how? Conversely, if the definitions become too general, is CCE still a useful concept for studying certain classes of animal behavior? I think these are some of the very important questions that could be addressed or at least raised in the discussion to initiate a broader debate within the community.

We thank the reviewer for their comments and interesting questions regarding our study. We agree with the reviewer that our study opens up new avenues for critically analysing the criteria previous studies have used for providing evidence of CCE in non-human animals. According to our literature review, we found that the field has been usually motivated in thinking about CCE in a ‘process’ focused manner (Reindl et al. [2]) in regards to individuals being able to compare strategies and selecting ones resulting in higher individual fitness. This preferential selection of strategies – termed innovations — allows for the stereotypical ratcheting effect seen in CCE. In our study, we propose that in the case of homing pigeons, the ratcheting effect is more of a statistical outcome rather than deliberate individual judgement. We believe that this strategy is also amenable to certain task types (which in our study was homing route choice) and may change for others (for example solving a puzzle box) and the task also needs to be sufficiently complex for animals to benefit from the use of social information (Caldwell et al. 2008 [3]). Thus, we recommend future work to address what classes of problems would fit well within the definition of “emergent” CCE and which ones don’t. Keeping this framework in mind, studies should clearly state what definition of CCE they are using and should be critically evaluated for their underlying task type and cognitive mechanisms to deem them as CCE. Considering these points, we have now expanded our Discussion to include a paragraph: “Our results highlight the need for more…..range of task types and cognitive abilities.” found in lines 420-433 to highlight these key questions.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I do not have any major objections, but I am clarifying my points as major or minor depending on the effort required to address (mostly via rewriting and clarifications).

Major comments:

(1) A schematic summary of the original study: Since the current manuscript builds directly on Sasaki & Biro (2017), it would greatly help readers if you included a concise schematic figure summarizing the original experiment. For instance, a simple panel could depict the chain design (experienced + naïve replacements), the control treatments, and the key empirical findings (improvements in route efficiency across generations, and route similarity within vs. between chains). Presenting this visually would save readers the effort of reconstructing the design and main results from text alone, especially for those unfamiliar with the original paper. It would also clarify exactly what empirical patterns your simulations are intended to reproduce.

We thank the reviewer for this comment. We have now revised the manuscript with a schematic illustration adapted from the original study by Sasaki and Biro (2017). We hope this clarifies the experimental design and results we aimed to highlight in our work.

(2) Reproducibility: Code and data are only "available on request." I believe eLife has strong policies on open science; a lack of immediate open access to analysis would be a barrier. I find it jarring that a paper intending to reproduce and improvise a previously published paper does not make the codes and data available for peer review or to readers without an explicit request.

We have taken the feedback into consideration and updated the Data Availability section with a link to our Fig share dataset.

(3) One huge drawback of the current format of the manuscript, where Methods come after Results, is that one has to really struggle to understand and appreciate Figures 2 and 3. I would strongly urge authors to have a shorter methods section embedded either as a subsection before the Results, or within the results section, as described in each figure. Perhaps a lot of my confusion also comes from not having known the previous paper, but it may be true for other readers, too. More specifically, for Figure 3, how is social weight for the experiments inferred? Figure 3 caption talks of mean difference, but one has to check the manuscript at multiple places throughout to really understand what this difference is (the definition) and how it is computed.

While we agree that our manuscript includes the Methods section at the end, we tried to structure our text to tell a story (as stated in our manuscript title). To this end, we organized the text into short titled subsections that briefly convey the relevant background, identify the knowledge gap and outline our approach. We chose this structure to reserve the indepth details about model implementation and statistical analysis for the Methods.

Additionally, we made sure to include references to methodological details in relevant segments of the Introduction and Results section so as to not bog down the reader by model complexities and keep a coherent narrative that delivers the message of our study. To further address the background of our work, we have now added a schematic of the original study in response to a previous comment by the reviewer, which we hope helps the reader better understand our work. We hope this explanation clarifies the intention behind our writing choice and decision to retain the current structure.

(4) The introduction of the 'effective group size' concept is a potentially valuable and intuitive way to interpret chain dynamics, but the explanation is somewhat buried in the Results/Methods; I suggest highlighting it more prominently (e.g., in the Discussion or with a schematic in the Results) so readers can readily grasp this useful idea.

We thank the reviewer that they found our concept of ‘effective group size’ useful. However, we do believe that we introduced the idea and rationale behind using this method in the Results: “We asked to what extent……to an equivalent group size” found in lines 305-314. We reserved a detailed description of this method in the Methods section. However, to further emphasize the importance of the concept we have now added a text: “This is further supported….. slightly better than two individuals.” found in lines 389-394 in the Discussion. 

Minor comments:

(1) Line 12: "what is the navigation mechanism(s)" - the (s) is a bit awkward. Either remove (s) or ask what the mechanisms are.

We have fixed the typo to clarify the statement.

(2) Line 78: "Such 'ratchet'-like improvements is referred to..." → "are referred to."

We have fixed the typo to clarify the statement.

(3) Figure 3 caption: "color scheme in the plots are same" → should be "is the same."

We have fixed the typo to clarify the statement.

(4) Clarification on reporting confidence intervals: The manuscript reports confidence intervals (CIs) for the model-based comparisons (e.g., Figures 2-3). This might seem unnecessary for simulation studies, since running more iterations can arbitrarily shrink uncertainty. However, in your case, the CIs are justified because the simulations are anchored to a finite empirical dataset (only 9 solo trajectories), sampled with replacement, and analyzed with mixed-effects models that incorporate bird identity as a random effect. Thus, the intervals reflect biological sample variability rather than simulation noise. This must be clarified.

We have added a clarifying statement: “...and reflect the biological uncertainty in the empirical dataset, not simulation noise” found in lines 241 and 293 in the captions of Figures 2 and 3 in accordance with the reviewer’s comment. 

(5) One part of the issue is that details of methods come much later in the manuscript, perhaps following journal style. Therefore, I recommend explicitly highlighting this rationale in the Results, so readers do not misinterpret the CIs as simply reflecting simulation error.

We believe that the clarifying statements we have now added in the captions of Figures 2 and 3 should convey this interpretation of CIs and further changes in the Results may not be required.

With these proposed changes we hope that we improved upon the clarity of our manuscript.

References:

(1) Dalmaijer ES (2024) Cumulative route improvements spontaneously emerge in artificial navigators even in the absence of sophisticated communication or thought. PLoS Biol. 22:e3002644.

(2) Reindl, E., Gwilliams, A.L., Dean, L.G. et al. (2020) Skills and motivations underlying children’s cumulative cultural learning: case not closed. Palgrave Commun 6, 106.

(3) Caldwell CA, Millen AE (2008) Studying cumulative cultural evolution in the laboratory. Phil. Trans. R. Soc. B 363:3529-3539.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript reports a very interesting, novel and important research angle to add to the now enormous interest in how pesticides can be toxic to beneficial insects like the honey bee. Many studies have reported on how pesticides in standard use formulations show both lethality as well as sublethal negative effects on behavior and reproduction. The authors propose to use machine learning algorithms to identify new volatile compounds that can be tested for repellency. They use as input chemical structures that are derived from chemicals that have known repellent effects as identified in their initial behavioral assays.

Strengths:

The conclusion is that such chemicals specific to repelling bees and not pest insects (using the fruit fly as a model for the latter) can be identified using the ML approach. Have a list of such chemicals that can be rotated among in any field application would be a benefit because of the honey bees' ability to learn its way around any kind of stimulus designed to keep it from nectar and pollen, even when they may be tainted by pesticide.

Weaknesses:

The use of machine learning seems well-executed and legitimate. But this is beyond my expertise. So other reviewers can maybe comment more on that.

The behavioral data report on the use of a two-choice assay for bees in small Petrie plates. Bess can feed from two small wells place of filter paper impregnated with control or the control containing a chemical. The primary behavior, for ex in Fig 2C, is the first choice by one of the five bees in the plate of which well to feed from. For some chemical compound, there seems to be a 50:50 choice, indicating no repellent effects. In other cases the first bee making the choice chose the control, indicating possible repellent effects of the test chemical. Choices in this assay were validated in a free flying assay.

Concerns with the choice assay:

50-70 microliters amounts to what one hungry bee will drink. Did the first bee drink most of it, such that measures of bait consumed reflect a single bee or multiple bees?

The measure of lure consumed reflects multiple bees. We observed that the first bee did not empty the 70 ul of honey, allowing us to estimate honey consumption by several bees.

How many bees were repelled to the control side? Was it just the one bee?

All the bees in a group were repelled to the control side for repellents. Evaluating lack of honey consumption, also allowed us to repellency as well. As an example: if 100% honey is consumed on the control side meant that the bees were hungry, but if 0% honey was consumed on the repellent side, this meant that the bees were not hungry enough to drink from the honey on the repellent side.

Were other measures considered? E.g. time to first approach; the number of bees feeding at different time points; the total number of bees observed feeding per unit time.

Bees were cooled down to place them in the plates for the experiments. Therefore, time to first approach could also depend on how long it took the bees to warm up, which was not as relevant for our research question. Because bees can communicate where to find food sources to each other, we restricted ourselves to first choice, only, to get independent data points for each plate. However, we investigated whether the first cup the first bee chose was also the one it drank from, which was the case.

Reviewer #2 (Public review):

Summary:

The search for new repellent odors for honey bees has significant practical implications. The authors developed an iterative pipeline through machine learning to predict honey bee-repellent odors based on molecular structures. By screening a large number of candidate compounds, they identified a series of novel repellents. Behavioral tests were then conducted to validate the effectiveness of these repellents. Both the discovery and the methodological approach hold value for related fields.

Strengths:

The study demonstrates that using molecular structures and a relatively small training dataset, the model could predict repellents with a reasonably high success rate. If the iterative approach works as described, it could benefit a wide range of olfaction-related fields.

The effectiveness of the predicted repellents was validated through both laboratory and field behavioral tests.

Weaknesses:

The small size of the training dataset poses a common challenge for machine learning applications. However, the authors did not clearly explain how their iterative approach addresses this limitation in this study. Quantitative evidence demonstrating improvements achieved in the second round of training would strengthen their claims. For instance, details on whether the success rate of predictions or the identification of higher-affinity components would be helpful. Furthermore, given that only 15 new components were added for the second round of training, it is surprising that such a small dataset could result in significant improvements.

The original repellency dataset was collected from multiple older studies, each with differences in assays for bee behavior, and using differing delivery and chemical concentrations. Moreover, the number of strong repellents were limited in number, and because they varied structurally from non-repellents in the dataset, the AUC appeared high. A smaller dataset result in unusual AI/ML model performance trends, as any algorithm is just a reflection of its training data. As a result, we found that the Round 1 predictions had a low success rate in behavior assays (~20%). Subsequently, even small amounts of data collected using one standard concentration and assay, could dramatically change the quality of the dataset, not just for structures of repellents, but also related structures that were not repellent. What we observe is a more complete representation of how repellents and non-repellents are distributed when adding just 15 chemicals. And the prediction success of Round 2 is more than doubled in repellent behavior assays at >50%. The initially observed performance gains with even small additions to the training dataset will stabilize and ultimately plateau due to the limits of the ML algorithm and/or chemical featurization technique. A more complex model, trained on a large dataset, may not be expected to benefit from a handful of additional examples, it is because the chemical feature distributions are already better approximations of the real world. To put simply, smaller datasets imply there is more to learn.

It is also true that the size of the training dataset is important for AI/ML algorithms, Artificial neural network, for instance, are highly sensitive to noise and generalize poorly with limited data; the noise is amplified in these cases, and the solution—reducing the complexity of the model—impedes learning. Many algorithms like the decision trees and support vector machines featured in our paper can handle noise more efficiently and are suitable for smaller datasets in that they can still make reasonably successful predictions.

Reviewer #3 (Public review):

The manuscript of Kowalewski et al. titled "Machine learning of honey bee olfactory behavior identifies repellent odorants in free flying bees in the field" did machine learning to predict potential candidates for honeybee repellents, which may keep foraging bees from pesticides. This is a pilot research with strong significance in the research of olfactory behavior and in pest control. However, some major issues need to be addressed to enhance the manuscript's clarity, strength, and overall coherence.

(1) Drosophila melanogaster is not considered as a true agricultural pest. The manuscript would be more compelling if using true pests, for example, Drosophila suzukii or others.

Honeybees face a critical risk of lethal pesticide exposure when they drift from their designated orchards into adjacent blooming crops or honeydew-coated fields, where they encounter chemical treatments intended for insects like Citrus Thrips, Asian Citrus Psyllid, Alfalfa Weevil, Peach Twig Borer, Oriental Fruit Moth, Lygus Bugs , Cotton Aphids, Whiteflies, Corn Rootworm, Sunflower Head Moth, Vine Mealybug, Cucumber Beetles, and Sugarcane Aphids. Unfortunately, testing such pest species is outside the scope of this paper, but would deserve further research.

(2) For repellency test, the result relies on dosage. An attractant may become a repellent at high concentration. Test a range of concentrations for each chemicals and compare responses between honeybees and pests.

Testing freely flying honey bees in the field is an extremely challenging undertaking. Nevertheless, we added extra tests for two strong repellents, BR4.5 and BR3.81, at half dose of 0.05 mg/cm². As expected, we found that there was a reduction in repellency. Testing more concentrations was not within the scope of this paper.

(3) Be more clear about bee behavior data and their scores (as in Page 4 Results "184 training chemicals and later for 203 chemicals" and Page 10 Methods). I suggest that authors add a supplemental table with each chemical and its behavioral score, feature and reference - which ones were used for training, and which ones for testing. Also add your own behavioral test data (second input) to this table

We have added the training chemical lists as Supplemental Tables S3 and S4.

(4) The AUC in the first validation was 0.88 (Page 4), and in Page 5, "As expected, the computational validation results based on the AUC values, show an improvement." However, there were no other AUC values to show improvement.

(5) Show plots of ROC AUC curves from Round 1 and Round 2.

The round one ROC curve is shown in Figure 1. The round two ROC curves obtained from 3 different approaches (Author response image 1). The manuscript shows direct behavioral validation of chemicals identified, which is more important.

Author response image 1.

(6) In the Discussion, the authors mentioned olfactory receptors in honeybees. It would be useful to provide a general review of the current understanding of these receptors and their (potential) functions.

We have expanded the discussion and pointed to a review on honey bee olfaction.

(7) I suggest combining Fig. 1 and Fig. 3A as one pipeline for this work.

(8) Figure 2C, some sample sizes are very small, such as 2-piperidone: 1 first-choice control vs 0 first-choice repellent? Increase sample size and do statistical analysis.

Most compounds except the one pointed out, have small sample sizes because of the low percentage of bees participating in the trials. Consequently, we improved methods in round 2 and were able to increase participation from 68% to 81%, as described in the methods. However since the compound was included in the second round of training, we would like to report it anyway. This compound had the highest rate of non-participating plates compared to the others and there is a possibility that it it may affect both the stimuli.

(9) In general, to assist reviewers, include line numbers to the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Other factors about the newly identified chemicals:

Is there a toxicity index for these chemicals that can be listed? This would be important obviously for any humans around the repellents

While toxicity index determination is outside the scope of this manuscript, it is possible to predict Rat LD50 values using the EPA Suite’s toxicity prediction tool. In a pilot test, the software predicted an average oral toxicity is ~3064mg/kg for the 18 repellents in Round 2, which is considered “Practically non-toxic” by the EPA.

Was there any indication of bees being behaviorally impaired or dying when exposed to the chemicals in a confined space? Even exposure to intense floral perfumes in a confined space and be toxic over a longer period.

Less than 5% of the 2225 honey bee died after the experiments, and none of the compounds showed a significantly higher level of dying, suggesting that the minor effect was not due to chemicals, but possibly due to handling steps (starving, chilling, recovery, etc).

The 'plates not participating' measure indicates plates in which no bees fed on either choice. Is that correlated to the choice index? That is, when bees showed some repellency was it the case that often that led to no choice?

Yes, non-participating plates were those, in which the bees did not drink any honey at all. The reason for this could have been that the bees were too cold and unable to heat up enough to participate in the trials, or that the chemical was so repellent, the bees did not want to drink any honey at all. Because we were not able to distinguish between these two reasons, we excluded plates in which the bees did not drink any honey at all from our dataset.

It is unclear why the McNemar test was used.

The McNemar test is used for hypothesis testing for paired dichotomous data. In our data file, we created two columns to report our first-choice results: “Control side first” and “Repellent side first”. When the first bee in a plate drank from the control side first, we added a 1 to the “Control side first” column and a “0” to the “Repellent side first” column. Because one control and one repellent-side honey pot were in the same Petri dish, the bees could only choose one side first, this meant it could not choose the other side at the same time. Consequently, our dataset consisted of paired samples, which were dependent from each other. We therefore split the dataset by Repellent candidate, and we used the paired -sample McNemar tests for non-parametric data. (Lachenbruch P.A. McNemar Test, Wiley StatsRef: Statistics Reference Online)

The statistical result is not discussed in the text, only shown in the figure. And it looks to be significant only for one chemical and DEET. Yet on page 4 the end of the second paragraph, the authors write "For many of the tested compounds the bees preferred to visit the honey-water pots on the control side versus the repellent side,". That implies that they are not really using the test as a meaningful means for showing differences. If they are arguing only from trends, then that should be clearer in the text.

We reported the p-values for each test we had used in tables in Figure 2C and S2. In the methods section we report which statistical tests were used to evaluate the data.

There is no mention of attractant chemicals:

Slessor and Winston used queen pheromone to attract bees to fields and improve pollination. Honey bees use the Nasonov pheromone to attract other bees to feeding locations. Could the addition of their chemical features change ML outcomes? This should be at least discussed.

We thank the referee for the suggestion; however the focus this manuscript is repellents and therefore we restricted the background to that area of knowledge.

Reviewer #2 (Recommendations for the authors):

Minor comments:

Releasing the dataset and code will benefit the readers interested in this study.

The behavioral data are reported within the figures, tables, and supplementary. The computational code will be available upon request from the communicating author for non-commercial use.

Figure 1, AUC curve, "AUC = 0.XX", should there be an actual value from the experiment?

Added

Page 4, "(Talbe S1)" should be placed in the next sentence, as "From the initial training set we identified 45 features that were considered important for predicting aversive valence (Table S1)."

We have added this in the appropriate spot.

Page 5, "As expected, the computational validation results based on the AUC values, show an improvement.". Please list the AUC values.

Author response image 2.

Reviewer #3 (Recommendations for the authors):

Minor comments:

(1) Page 3: "they sense using a sophisticated olfactory system of >180 odorant receptor genes in the genome". In the cited Robertson & Wanner's paper, there are around 160 receptors, and 170 if pseudogenes are included.

We thank the referee and have updated the numbers.

(2) Page 4: "initially for 184 training chemicals and later for 203 chemicals (Table S1)." Table S1 is about features, not chemicals?

We have moved the reference to an appropriate location.

(3) Figure 2A: What is the control? Acetone or another solvent?

Acetone, but it rapidly evaporates before the time of experiment.

(4) Figure 2A: What does asterisks mean?

Statistically significant.

(5) Figure 3: When you added your own testing data as a second input for Round 2, put details about these data: chemical names, preference scores... Also, are Round 2 data (Round 1 plus your own) were also split as 90:10 into training and testing partitions?

Yes, the validation was performed on the updated data set including the new chemicals.

(6) Figure 3D: Is asterisk at correct location? What does it mean?

Means that BR3.15 was significantly different from BR4.5

(7) Figure 4D: "4D" in legend is missing. Also, "... tested at the regular dose (0.1mg/cm2) and half dose (0.05mg/cm2)". In the panel, it is only 0.05mg/cm2.

Added

(8) Table S2 is the same as Fig. 2C? Remove one.

We have deleted Table S2.

Author response:

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

Reviewer #1 (Public review):

(1) While the manuscript is written for a scientific audience, the authors are likely aware that findings like this will be of broad appeal to the field of neurology, where treatments for memory loss are desperately needed. For this reason, the authors could consider including a statement regarding an interpretation of this meta-analysis from a clinical standpoint. Statements such as 'safe and effective' imply a clinical indication, and yet the manuscript does not engage with clinical trials terminology such as blinding, parallel arm versus crossover design, and trial phase. While the authors might prefer not to engage with this terminology, it can be confusing when studies delivering intervention-like five days of consecutive TMS (e.g., Wang et al., 2014) are clustered with studies that delivered online rhythmic TMS, which tests target engagement (e.g., Hermiller et al., 2020). While the 'sessions' variable somewhat addresses the basic-science versus intervention-like approach, adding an explicit statement regarding this in the discussion might help the reader navigate the broad scope of approaches that are utilized in the meta-analysis.

We appreciate the suggestion to enhance interpretability of our report by broader audiences. First, to avoid confusion, we have eliminated “safe” and “effective” descriptors from the main summary of findings in the Abstract (pg. 1) and Discussion (pg. 6). Second, we now describe that reviewed studies included those categorized as traditional clinical trials, as well as non-clinical studies that generally follow clinical trial designs (i.e., multi-day intervention-like studies), in addition to more basic-oriented studies that are geared towards target engagement (Introduction, pg. 2). Third, we now clarify that the Design and Control factors (Figure 3) correspond to fairly standard distinctions in the clinical trials literature and were intended to capture major study design factors choices that are used in both clinical-trial and non-trial studies (Methods, pg. 9; Table S1). Finally, we now clarify that future clinical trials would be needed to evaluate HITS for any specific indication, and that our findings motivate such investigations but do not conclusively indicate efficacy for any given indication (Abstract, pg. 1; Discussion, pg. 7).

Reviewer #1 (Recommendations for the authors):

(1) The color scheme of Figure 1 was a bit confusing. All of the colors used for the flagged regions were incredibly similar. At first glance, it looks like the hippocampus was targeted directly due to the subtle color difference. Could the authors use colors that are more different? Similarly, zooming into the specific locations shows blue dots encompassed by teal. I am not sure what I am looking at here.

We have updated the figure for clarity.

(2) Given the broad appeal of the current study, I would encourage the authors to include a brief visual depiction of "HITS." This could help the more casual reader to understand the general approach.

We have included this in Figure 1A.

Reviewer #2 (Public review):

(1) While the introduction centers on the role of the hippocampus in episodic memory and posits hippocampal neuromodulation by TMS as causative, the true mechanism may be more complex. Clean hippocampal lesions in primates cause focal loss of spatial and place memory, and I am aware of no specific evidence that the hippocampus does more than this in humans. Moreover, there is evidence that lateral parietal TMS also reaches neighboring temporal lobe regions, which contribute to episodic memory. The hippocampus may, therefore, be a reliable deep seed for connectivity-based targeting of the episodic memory network, but might not be the true or only functional target.

We regret to have implied that we think the hippocampus is the true or only functional target. We agree with the reviewer that the hippocampus is “a reliable deep seed for connectivity-based targeting of the episodic memory network” and that the specific locus/loci of the HITS effects and mechanisms are not yet clear. We now emphasize that although hippocampus is used to define the targeted network, effects of TMS are likely distributed throughout the network, citing relevant studies that have shown that brain activity changes due to HITS are certainly not restricted to the hippocampus (Introduction, pg. 2).

(2) The meta-analysis combines studies with confirmation of targeting and target-network engagement from fMRI and studies without independent evidence of having stimulated the putative target (e.g., Koch et al). That seems like a more important methodological distinction than merely the use of any individual targeting method. In my experience, atlas-based estimates are at least as accurate as eyeballing cortical areas in individuals. Hence, entering individual functional targeting as a factor might reveal an effect on efficacy.

Our current definition of the “Targeting” factor appears to satisfy this concern. That is, we distinguish studies that used “individual functional targeting” (i.e., resting-state fMRI or DTI connectivity in each individual to select the target) from those that did not (i.e., atlas or other group-average approach). Notably, the Targeting factor modulation effect failed to survive correction for multiple comparisons. We think this satisfies the reviewer criticism, unless the reviewer is suggesting that we categorize studies based on whether they included evaluation of target engagement (e.g., tested for change in fMRI activity or connectivity of the network due to HITS) versus those that measured only behavioral outcomes. We did not include this distinction as a factor, as our analysis focuses on behavioral effects of HITS, and it is not clear what the neural effects would have been in studies in which they were not measured. Notably, we are providing the full raw dataset of effect sizes in a public repository with our final version of record, such that any other categorization schemes could be assessed by others.

(3) The funnel plot and Egger's regression for episodic memory outcomes suggested possible bias, and the average sample size of 23 is small, contributing to the likelihood of false positive results. It would be informative, therefore, to know how many or which studies had formal power estimates and what the predicted effect sizes were.

Regarding the average sample size of 23, we note that we used Hedges’ g for the effect size measure because it corrects for bias associated with small samples (pg. 10). Further, small sample sizes contribute to noisy estimates of true effects, allowing outliers to contribute to false positives and low power to contribute to false negatives, but without any reason to systematically yield bias towards false positives. Regarding potential publication bias, although we cannot rule this out based only on the statistics, we think that bias against publication of negative results is unlikely. First, HITS experiments are time consuming and expensive, and most in the field seem to be motivated to publish, whatever the outcome. Second, the notion of memory enhancement via brain stimulation is controversial, and groups have certainly been motivated, if not overly eager, to publish “failure to replicate” studies for HITS (e.g., the failure-to-replicate publication by Hendrikse et al. 2020, which was then re-analyzed by many of the original authors to arrive at different conclusions in Cash et al. 2022). Given these considerations, we think that it is very unlikely that publication bias had any major impact on our conclusions, but of course it cannot be conclusively excluded. Finally, we note that our finding of HITS selectivity for recollection enhancement is likely not affected by publication bias, as this selectivity versus other memory and non-memory outcomes was found only within published studies (i.e., it is very unlikely that publication bias would have led researchers to withhold publication of studies that found effects of HITS on recognition but not on recollection).

(4) In the Discussion, the authors might provide a comparison between the effect size for memory improvement found here with those reported for other brain-targeted interventions and behavioral strategies. It may also be worthwhile pointing out that HITS/memory is one of the very few, or perhaps the only, neuromodulatory effects on cognition that has been extensively reproduced and survived rigorous meta-analysis.

We now emphasize that this is, to our knowledge, the only neuromodulatory effect on cognition that is selective, has been extensively reproduced, and survived rigorous meta-analysis (Discussion, pg. 6). However, we wish to avoid the clinical overinterpretation of our findings that might result if we were to compare directly to effect size estimates for other current therapies, which have been evaluated for specific clinical indications. For example, antibody and pharmacological interventions for Alzheimer’s dementia typically have been associated with similar effect sizes to our estimate for HITS. However, those estimates derive from systematic review of randomized controlled trials measuring clinically relevant outcomes at relatively long delays, whereas the HITS studies we review include a mix of controlled and uncontrolled trials, vary in whether clinical outcomes were assessed, and mostly assessed outcomes at shorter delays. Thus, it could be misleading to directly compare the effect sizes. We instead continue to highlight that the HITS effects are promising and warrant rigorous testing for any given clinical indication.

(5) The section of the Discussion on specificity compares HITS to transcranial electrical stimulation without specifying an anatomical target or intended outcome. A better contrast might be the enormous variety of cognitive and emotional effects claimed for TMS of the dorsolateral prefrontal cortex.

We now also note that TMS of lateral frontal cortex has not been associated with similarly high specificity (Discussion, pg. 6). Note however that we cannot exclude anti-depressant or other psychological effects of HITS, as such outcomes were not consistently assessed in HITS studies and so were not included in our analyses.

(6) With reference to why other nodes in the episodic memory network have not been tested, current flow modeling shows TMS of the medial prefrontal cortex is unlikely to be achievable without stronger stimulation of the convexity under the coil, in addition to being uncomfortable. The lateral temporal lobe has been stimulated without undue discomfort.

We now additionally indicate that medial prefrontal stimulation may be ineffective given conventional TMS (Discussion, pg. 7). However, we are aware of no studies that have stimulated the portion of middle temporal gyrus that shows strong connectivity with hippocampus. We have tried this location, which positions the coil on or slightly above the ear and bordering on the temple area that is very sensitive to most. We were not able to minimize pain/discomfort for most subjects in pilot experiments, and so had to abandon it. Perhaps others have succeeded? If the reviewer has any specific references that could be included we would be happy to add them and update this section accordingly.

(7) Finally, a critical question hanging over the clinical applicability of HITS and other neuromodulation techniques is how well they will work on a damaged substrate. Functional and/or anatomical imaging might answer this question and help screen for likely responders. The authors' opinion on this would be informative.

We appreciate this point but don’t think there are enough data to assess the level of substrate damage needed to frustrate any stimulation benefits. The only thing we can say is that HITS was equally effective for mild to moderate Alzheimer’s dementia as it was for other non-neurodegenerative groups (nonsignificant effect of the Population factor, Figure 3B), suggesting that whatever degree of damage present in that group is insufficient to prevent the stimulation effects. We now highlight this point and raise the issue that, presumably, some level of damage would render HITS ineffective (Discussion, pg. 8).

Reviewer #3 (Public review):

(1) My only significant concern is how studies are categorized in the 'Timing' factor (when stimulation is applied). Currently, protocols in which TMS is administered across days are categorized as 'pre-encoding' in the Timing factor. This has the potential to be misleading and may lead to inaccurate conclusions. When TMS is administered across multiple days, followed by memory encoding and retrieval (often on a subsequent day), it is not possible to attribute the influence of TMS to a specific memory phase (i.e., encoding or retrieval) per se. Thus, labeling multi-day TMS studies as 'pre-encoding' may be misleading to readers, as it may imply that the influence of TMS is due to modulation of encoding mechanisms per se, which cannot be concluded. For example, multi-day TMS protocols could be labeled as 'pre-retrieval' and be similarly accurate. This approach also pools results from TMS protocols with temporal specificity (i.e., those applied immediately during encoding and not on board during memory testing) and without temporal specificity (i.e., the case of multi-day TMS) regarding TMS timing. Given the variety of paradigms employed in the literature, and to maximize the utility/accuracy of this analysis, one suggestion is to modify the categories within the Timing factor, e.g., using labels like 'Temporally-Specific' and 'Temporally Non-specific'. The 'Temporally-Specific' category could be subdivided based on the specific memory process affected: 'encoding', 'retrieval', or 'consolidation' (if possible). I think this would improve the accuracy of the approach and help to reach more meaningful conclusions, given the variety of protocols employed in the literature.

We agree in principle with this criticism and think that the most straightforward way to address it is to relabel the “Pre-Encoding” category as “Pre-Task”. The issue with labeling/considering single-session stimulation delivered immediately before encoding as “Pre-encoding” is that this makes the assumption that this stimulation doesn’t also affect retrieval (i.e., is temporally specific). We do not have certainty about the timecourse of how a single session of stimulation affects brain activity. We think the “Pre-Task” label and interpretation is the best way to address this, to avoid suggesting that we are confident about the timecourse/selectivity of stimulation effects. Notably, the “Sessions” factor directly compares among designs that delivered stimulation in a single session versus in multiple consecutive sessions, and was a nonsignificant modulator. Thus, our analyses already compare studies that are relatively temporally specific versus those that, likely, are less so. In addition to relabeling, we have also added clear caveats to address the interpretive constraint imposed by the unknown timecourse of stimulation effects (Discussion, pg. 6-7) and revised the Abstract to reflect this change.

(2) As the scope of the meta-analysis is limited to TMS applied to parietal or superior occipital cortex, it is important to highlight this in the Introduction/Abstract. The 'HITS' terminology suggests a general approach that would not necessarily be restricted to parietal/nearby cortical sites.

This was previously highlighted only in the Methods and Discussion (with a Discussion paragraph dedicated to the issue of target selection; see also Comment 6 from Reviewer 2). We now also note this in the Introduction (pg. 2) and Abstract.

Minor:

(1) To reduce the number of study factors tested, data reduction was performed via Lasso regression to remove factors that were not unique predictors of the influence of TMS on memory. This approach is reasonable; however, one limitation is that factors strongly correlated with others (and predict less unique variance) will be dropped. This may result in a misrepresentation, i.e., if readers interpret factors left out of this analysis as not being strongly related to the influence of TMS on memory. I do see and appreciate the paragraph in the Discussion which appropriately addresses this issue. However, it may be worth also considering an alternative analysis approach, if the authors have not already done so, which explicitly captures the correlation structure in the data (i.e., shown in Figure S2) using a tool like PCA or an appropriate factor analysis. Then, this shared covariance amongst factors can be tested as predictors of the influence of TMS - e.g., by testing whether component scores for dominant PCs are indeed predictive of the influence of TMS. This complementary approach would capture rather than obfuscate the extent to which different factors are correlated and assess their joint (rather than independent) influence on memory, potentially resulting in more descriptive conclusions. For example, TMS intensity and protocol may jointly influence memory.

We argue that feature selection via Lasso regression is a better approach for our research question than PCA, factor analysis, or other latent variable methods. The main reason is that PCA would sacrifice the interpretability of our findings with respect to the design of future experiments using or testing HITS. That is, because PCA creates composite components that are linear combinations of multiple variables, we would lose the ability to provide clear, actionable guidance to researchers about which specific study design choices (e.g., stimulation intensity, protocol type, timing) influence memory outcomes. Given that a major goal of our meta-analysis is to inform future experimental design, we believe that it is essential to maintain interpretability of the individual factors that must be decided when designing a study. Regarding factor analysis, this approach would require making a priori theoretical decisions about how to group individual moderators, which could introduce subjective bias into the analysis and would introduce other complications such as a need for validation of the resulting factor scores. We believe that the exploratory nature of our investigation, examining which among many possible study design factors substantially determine TMS efficacy, is better suited to a data-driven selection approach like Lasso. While the reviewer correctly notes that Lasso may drop factors that are correlated with stronger predictors, this feature can be considered advantageous in terms of identifying factors for inclusion in future study designs. That is, this can help identify the most parsimonious set of independent predictors, such that researchers can focus on the study design elements that matter most when controlling for other factors. Notably, we provide the table of factor relationships (Figure S2) so that interested readers can inspect how dropped factors were related to those that were retained.

It is also important to note that we have provided the full dataset with our resubmission, which has been deposited in Dryad with a link in the Data Availability section (pg. 15). Thus, others are free to explore alternative analytical approaches should they wish to examine the data from different perspectives or to answer different questions.

(2) Given the specific focus on TMS applied to parietal cortex to modulate hippocampal and related network function, it would be fruitful if the authors could consider adding discussion/speculation regarding whether this approach may be effectively broadened using other stimulation methods (e.g., tACS, tDCS), how it may compare to other non-invasive brain stimulation methods with depth penetration to target hippocampal function directly (transcranial temporal interference, or transcranial focused ultrasound), and/or how or whether other stimulation sites may or may not be effective.

We briefly discuss a meta-analysis of tACS studies which reported nonspecific effects, including for parietal targets overlapping those used for HITS (Discussion, pg 6). We briefly speculate about how tES effects remain mechanistically uncertain. We are afraid that further speculation about other stimulation modalities and targets would be beyond the scope of this focused meta-analysis, given especially the few datapoints for newer approaches such as TI or tFUS.

(3) Studies were only included in the meta-analysis if they contained objective episodic memory tests. How were studies handled that included both objective and subjective memory, or other non-episodic memory measures? For example, Yazar et al. 2014 showed no influence of TMS on objective recall, but an impairment in subjective confidence. I assume confidence was not included in the meta-analysis. Similarly, Webler et al. 2024 report results from both the mnemonic similarity task (presumably included) and a fear conditioning paradigm (presumably excluded). Please clarify in the methods how these distinctions were handled.

Studies were included in our meta-analysis if they included at least one objectively scorable test of episodic memory. We only included objectively scorable test performance in our analysis, excluding scores from any other subjective measures if they were also reported. This is now clarified in Methods (pg. 9).

(4) The analysis comparing memory to non-memory measures is important, showing the specificity of stimulation. Did the authors consider further categorizing the non-memory tasks into distinct domains (i.e., language, working memory, etc.)? If possible, this could provide a finer detail regarding the selectivity of influences on memory vs. other aspects of cognition. It is likely that other aspects of cognition dependent on hippocampal function may be modulated as well, i.e., tasks with high relational/associative processing demands.

This is an interesting idea, but it is beyond our expertise to categorize these other tasks based on the nature of processing demands that they capture. Note that the task names are provided in the data table that we are making available online with our submission of record (via Dryad), such that other groups could address this question if interested.

(5) In the analysis of the Intensity factor, how were studies using Active (rather than resting) MT categorized? Only resting MT is mentioned in Table S1. This is important as the original theta-burst TMS protocol from Huang et al. 2005 determines intensity based on Active Motor Threshold.

MT was resting/passive in all reviewed studies except for one (Tambini et al. 2018), which used 80% of active MT. We categorized this as <100% MT for the Intensity factor, as it was <100% of MT as defined in that study. Although one could make the argument that 80% AMT might instead correspond to 100+% RMT, this change would have very little influence on our results or conclusions. We now clarify this in Table S1.

(6) Is there a reason why the study by Koen et al. 2018 (Cognitive Neuroscience) was not included? TMS was performed during encoding to the left AG, and objective memory was assessed, so it would seemingly meet the inclusion criterion.

The failure to include Koen et al. 2018 was our error. Koen et al. 2018 is the only study that used “online” stimulation, delivered during the trials when memoranda were displayed for encoding in the task. In contrast, all other reviewed studies delivered “offline” stimulation either before the memoranda was presented (“Pre-Task”) or after the encoding period but before retrieval (“Post-Encoding”). Therefore, categorization for the “Timing” factor would be problematic for its inclusion in the main analysis. We therefore now include Koen et al. 2018 in the “Supplementary Results” section as well as the corresponding main Results section on “Similar outcomes in studies that were excluded from meta-analysis”. We also note in the relevant discussion that “online” stimulation, as done in Koen et al. 2018, is typically considered disruptive (e.g., Beynel et al. 2019 Neuroscience & Biobehavioral Reviews; Yeh & Rose 2019 Frontiers in Psychology), which should be taken into account when considering the findings of Koen et al. 2018 relative to other reviewed studies that used “offline” designs.

(7) It would be helpful to briefly differentiate the current meta-analysis from that performed by Yeh & Rose (How can transcranial magnetic stimulation be used to modulate episodic memory?: A systematic review and meta-analysis, 2019, Frontiers in Psychology) (other than being more current).

Beyond being more current and therefore including many more studies in which stimulation targets were based on hippocampal connectivity (which tend to have been published more recently), the differences with Yeh & Rose 2019 are subtle. Our review focuses on assessment of network targeting and whether effects were specific to episodic memory versus other tasks, which differs somewhat from the focus of Yeh & Rose 2019. The main difference in conclusions likely derives from there being more network-focused memory TMS experiments now than were available for Yeh & Rose’s review. We also differentiate episodic memory into recollection versus other components to test specificity and analyze modulation by many study design factors relevant to HITS studies that were not emphasized in Yeh & Rose’s review. Note that we now cite Yeh & Rose for those interested in potential differences.

(8) For transparency and to facilitate further understanding of the literature and potential data re-use, it would be great if the authors consider sharing a supplementary table or file that describes how individual studies/memory measures were categorized under the factors listed in Table S1.

As promised in our original submission, we are providing the full data table, including how individual studies and memory measures were categorized, as an open dataset in Dryad. The Dryad dataset is cited in “Data availability” (pg. 15).

Reviewer #3 (Recommendations for the authors):

Please explicitly state in the Methods (Meta-analysis of effect modifiers section) that the criteria used for categorizing each measure into a factor (e.g., probing Recollection, Recognition, etc.) are fully described in Table S1; this will help readers to find these details (it took me a while!).

This is now emphasized (pg. 10).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer 1 (Public review):

(1) "The timescales of the peptide recognition and unbinding process are much longer than what can be sampled from unbiased simulations. Therefore, the proposed mechanism of recognition should only be considered a hypothesis based on the results presented here. For example, peptides that do not dissociate within one one-microsecond MD simulation are considered to be stable binders. However, they may not have a viable way to bind to the narrow protein cleft in the first place."

We thank the Reviewer for this valuable feedback and we agree with the Reviewer. Our work on the IRE1 cLD activation mechanism is focused on generating a hypothesis of the binding mechanism driven by MD simulations. We recognize the limitations in defining a stable binder due to the time scales sampled. However, our primary focus was to sample and characterize a possible binding pose in the center of the cLD dimer. We contextualized our statements about stable binders and limited our claims to stating that the protein-peptide complex is stable within 1 µs-long simulations. However, we believe that our finding that the cLD dimer groove is not able to accommodate peptides is solid, as the steric impediment described is present in all our replicas, both with and without peptides, in a cumulative sampling time of 24 µs without peptides and 66 µs with peptides. Additionally, we included a plot showing the distribution of groove width across all replicas.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) The title was changed from “Unfolded polypeptides can stably bind to hIRE1α cLD dimer” to “Unfolded polypeptides bind to hIRE1α cLD dimer surface”

Addition to the text. (Figure 15 A legend) “(A) Distributions of the groove width of peptide-bound cLD dimers throughout all simulations performed. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(2) Oftentimes, representative structures sampled from MD simulation are used to draw conclusions (e.g., Figure 4 about the role of R161 mutation in binding affinity). This is not appropriate as one unbinding event being observed or not observed in a microsecond-long trajectory does not provide sufficient information about the binding strength of the free energy difference.

We thank the Reviewer for the insightful comment. As explained in the previous point, we believe that our simulations provide useful hypotheses. We are aware of the limitations due to the timescale and agree that these limitations cannot be overcome with standard equilibrium simulations. To address these limitations, used orthogonal methods, specifically MM/PB(GB)SA calculations, to calculate binding free energies from existing trajectories. We added predictions of all the peptides using AlphaFold 3, to confirm the binding region. Importantly, we now provide experimental results to assess the binding affinity of cLD dimer mutants E102R and Y161R.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. 16A). We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Figure 16 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT). (B) Difference in enthalpy (enthalpy of binding, ∆H) as an estimate of the binding free energies of unfolded polypeptides to hIRE1α cLD dimer derived from MM/PBSA calculations of our peptide simulations.”

Addition to the text. (Figure 4 G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Results section: Point mutations destabilize unfolded peptide binding to cLD) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102 K_1/2= 6.35 µM and Y161R K_1/2= 5.4 µM, Supplementary Table 3) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 3), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary Table 3)

Reviewer 2 (Public review):

(1) Improving presentation to include more computational details.

We thank the Reviewer for raising this critical point. We agree that the manuscript is tailored for a biology audience, as the data are particularly relevant for that community. Nevertheless, we also understand the importance of providing sufficient methodological detail for computational readers. We added more references to the methods for computational information in the main text.

(2) More quantitative analysis in addition to visual structures.

We added an uncertainty estimate for the HDX calculations using bootstrapping and included additional information on bond distances for E102 and Y161. We also incorporated time-series data showing the distance of the peptide from the groove across all replicas.

Addition to the text. (Figure 1C legend) “(C) The deuterated fraction obtained from experimental results (dashed line, shaded area indicates the error we calculated from bootstrapping) published by Amin-Wetzel et al. and the fraction computed from MD simulations (solid lines, blue for TIP3P water and orange for TIP4PD water) for the PDB and AF model at incubation time point 0.5 min. This time point corresponds to experimental incubation times, not MD simulation time. Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping. Below each absolute value plot, we report the discrepancy, which is defined as the difference between the simulated and experimental deuterated fractions, with the shaded area indicating the corresponding error.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

Reviewer 3 (Public review):

A potential weakness of the study is the usage of equilibrium (unbiased) molecular dynamics simulations, so that processes and conformational changes on the microsecond time scale can be probed. Furthermore, there can be inaccuracies and biases in the description of unfolded peptides and protein segments due to the protein force fields. Here, it should be noted that the authors do acknowledge these possible limitations of their study in the conclusions.

We appreciate the Reviewer’s thoughtful comment. As noted in our response to Reviewer 1, we addressed the concern about sampling by applying orthogonal methods and experimental techniques. We agree with the Reviewer that some form of enhanced sampling is necessary if we want to assess binding in a more quantitative way, e.g., via free energy calculations. However, we also realize that applying any enhanced sampling scheme to our system is very challenging, given its large size and the complex peptide-protein interactions, which are not easily captured in a few collective variables. After a careful assessment and some preliminary tests, we decided that estimating free energies using enhanced sampling would necessitate a separate paper due to both the conceptual complexity of the project and the size of the necessary sampling campaign.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Some enhanced sampling or path sampling simulations may be carried out to identify the peptides’ binding and unbinding mechanisms to the protein. This can show whether the disordered peptides studied in this work do indeed bind to the protein.

We thank the Reviewer for this constructive criticism. We acknowledge the limitations associated with investigating binding and unbinding mechanisms of disordered peptides within the time scales accessible to our equilibrium simulations. However, the primary objective of our study was to sample and characterize a plausible binding pose at the center of the cLD dimer. We wanted to understand if unfolded model peptides require an open groove able to contain them to bind to IRE1’s core luminal domain or if binding also in the absence of an open groove.

Enhanced sampling is, of course, an important strategy to overcome the limits of equilibrium simulations. However, we note that implementing enhanced sampling approaches in this system poses significant challenges due to its large size and the complexity of peptide–protein interactions, which cannot be easily captured using a limited set of collective variables. We decided that a thorough application of enhanced sampling would therefore constitute a separate study. Instead, we decided to validate our simulations in two ways: 1) we ran a new set of free energy calculations, and 2) we tested key predictions in experiments, adding significant new data to strengthen the conclusions of our manuscript.

To evaluate whether the binding free energies of MPZ-derived peptides to human IRE1α cLD dimers are consistent with experimentally reported binding constants, we employed the MM/PBSA (Molecular Mechanics/Poisson–Boltzmann Surface Area) method. Calculations were performed over the final 250 ns of each simulation replica using the Single Trajectory Protocol (STP), which avoids the need for additional simulations. This approach provides an estimate of the effective binding free energy (i.e., enthalpy of binding) by accounting for bonded and non-bonded interactions, as well as solvation contributions. The entropic contribution, being computationally more demanding and subject to additional approximations, was not included. Binding enthalpies were obtained for MPZ1-N (in different initial orientations), MPZ1-C, MPZ1-N-2X, and MPZ1-N-2X-RD. The results indicated small differences in effective binding energies between the shorter peptides (MPZ1-N and MPZ1-C), whereas MPZ1-N-2X exhibited the lowest binding energy and MPZ1-N-2X-RD the highest, consistent with experimental trends. These findings support the reliability of our model and sampling strategy as a framework for analyzing peptide binding conformations to cLD.

We identified residues E102 and Y161 as key contributors to the binding of unfolded peptides in our simulations. Contact analysis revealed these residues as binding hotspots, centrally located within the observed interaction regions. To probe their relevance, we conducted simulations of cLD dimers with single arginine mutations in these residues, aimed at disrupting these hotspots through charge repulsion. These simulations revealed increased instability of the MPZ1N2X on the cLD dimer surface. We further validated these findings experimentally using fluorescence anisotropy assays. Fluorescently labeled MPZ1N-2X was titrated with purified cLD mutants (E102R and Y161R), and anisotropy measurements were fitted to derive  K_1/2 values. Both mutations resulted in approximately a two-fold reduction in binding affinity relative to the wild-type cLD, confirming the importance of these residues in stabilizing peptide binding.

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “Thus, we investigated how the point mutations of two key residues, E102R and Y161R, would affect peptide binding by simulating the cLD mutant in complex with MPZ1N-2X (Fig. 4C-E). We initialized the systems in the pose described for the other peptide-cLD systems described earlier (Fig. 3B, t = 0 µs). In simulations of the wild-type (WT) cLD dimer, the peptide generally remained near the center (Fig. 4C,F). By contrast, MPZ1N-2X displayed reduced binding to E102R, fully dissociating in one TIP4P-D replica (Fig. 4E,F). A similar trend was observed for Y161R, where one partial dissociation event occurred (Fig. 4D,F). Comparative analysis of MPZ1N-2X contact sites on the WT and mutant cLD dimers (Supplementary Fig. 17B-D) revealed that, in the presence of mutations, the peptide engages a broader surface region rather than remaining centrally localized, while forming fewer contacts with the specific residues (Supplementary Fig. 18A-B).”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102  K_1/2= 6.35 µM and Y161R  K_1/2= 5.4 µM, Supplementary Table 1) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 1), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4 legend) “(E) Side view snapshot after 1 µs of simulation of E102R hIRE1α cLD dimer (gray) in complex with MPZ1N-2X (orange). The amino acid R102 on both monomers is represented in magenta sticks. (F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Methods section: Binding free energy calculations (MM/PBSA)) “The binding free energy of noncovalently bound complexes of human IRE1 cLD and peptides was calculated with MM/PBSA (Molecular mechanics/PoissonBoltzmann Surface Area) method via gmx_MMPBSA (version 1.6.4)[1, 2]. The Poisson-Boltzmann method was used to estimate the electrostatic contribution to solvation free energy as recommended for data obtained with the CHARMM force field. The contribution of the entropic term was omitted, obtaining effective binding free energy values, or enthalpy of binding (∆H). We used the Single Trajectory Protocol (STP), using the cLD-peptide simulations as input. The calculations were performed on the last 250 ns of each replica. Single-term total non-polar solvation free energy (inp = 1) was used. The charmm_radii (PBRadii= 7) was used to build amber topology files [3]. The default parameters were applied for other terms.”

Addition to the text. (Methods section: Protein purification) “To express hIRE1α LD (24-443) human cDNA sequences were cloned into pET47b(+) to create a coding sequence with N-terminal His6-tag. Mutations of hIRE1α LD were introduced by overlap extension PCR and restriction cloning into pET47b(+). For expression of the proteins, the plasmid of interest was transformed into Escherichia coli strain BL21DE3* RIPL (Agilent Technologies). Cells were grown in Luria Broth until OD600=0.6-0.8. Protein expression was induced with 0.6 mM IPTG, and cells were grown in 20°C overnight. For purification, cells after harvesting were resuspended in Lysis Buffer (50 mM HEPES pH 7.2, 400 mM NaCl, 20 mM imidazole, 5% glycerol, 5 mM β-mercaptoethanol) and were lysed in Constans Systems cell disruptor at 25 000 psi. The supernatant was collected after centrifugation for 45 minutes at 48000×g in 4°C. Supernatant was loaded onto Ni-NTA column (Cytiva) and the protein eluted with a linear gradient of imidazole from 20 to 500 mM. Fractions containing the protein were diluted 1:8 with anion exchange wash buffer (50 mM HEPES pH 7.2, 5 mM β-mercaptoethanol), loaded onto HiTRAP-Q ion exchange column (Cytiva) and eluted with a linear gradient from 50 mM to 1 M NaCl. Afterwards, the His6tag was removed by cleavage with Precission protease (GE Healthcare, 1 µg of enzyme per 100 µg of protein). The cleavage was performed overnight in 4°C. The protein sample after cleavage was loaded onto a Ni-NTA column, and the flow-through containing protein without the tag was collected. The protein was further purified on a Superdex 200 10/300 gel filtration column equilibrated with Buffer A (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT). Protein concentrations were determined using extinction coefficient at 280 nm predicted by the Expasy ProtParam tool (http://web.expasy.org/protparam/).”

Addition to the text. (Methods section: Fluorescence anisotropy) “For fluorescence anisotropy measurements, the MPZ1-N-2X peptide attached to 5 carboxyfluorescein (5-FAM) at its N-terminus was obtained from GenScript at >95% purity. Binding affinities of hIRE1α LD mutants to FAM-labeled peptides were determined by measuring the change in fluorescence anisotropy on a Tecan CM Spark Micro Plate Reader with excitation at 485 nm and emission at 525 nm with increasing concentrations of hIRE1α LD variants. Measurements were performed in Buffer A supplemented with Tween 20 (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT, 0.025% Tween 20). Fluorescently labeled peptides were used in a concentration of 90 nM. The reaction volume of each data point was 25 µL and the measurements were performed in 384-well, black flat-bottomed plates (Corning) after incubation of peptide with hIRE1α LD variants for 30 min at 25◦C. Binding curves were fitted using Prism Software (GraphPad) using the following equation: F_bound = r_free +( r_max − r_free)/(1+10((Log K_1/2 −x)·n_H)), where F_bound is the fraction of peptide bound, r_max and r_free are the anisotropy values at maximum and minimum plateaus, respectively. n_H is the Hill coefficient and x is the concentration of the protein in log scale. Curve-fitting was performed with minimal constraints to obtain K_1/2 values with high R² values. However, as this equation does not consider the equilibria between hIRE1α LD dimers/oligomers, these apparent K_1/2 values do not reflect the dissociation constant.”

(2) Wherever possible, conclusions related to binding affinity should not be drawn from single unbinding events. For example, the title of Figure 4, "Single point mutation of cLD alters the binding affinity of unfolded peptide," should be softened. Similar changes should be made throughout the manuscript where such claims have been presented.

We thank the Reviewer for highlighting this important point. In the revised manuscript, we have adjusted the text to remove or soften conclusions related to binding affinity that were based on single unbinding events in the MD simulations.

Addition to the text. (Figure 4 title) “Single point mutations of cLD alter the binding of unfolded peptide MPZ1N-2X.”

Addition to the text. (Results section title: Unfolded polypeptides can stably bind to hIRE1α cLD dimer) “Unfolded polypeptides bind to hIRE1α cLD dimer surface.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1αα cLD dimer surface) “Our goal was to elucidate a potential binding pose and identify the relevant features of unfolded proteins and the cLD that affect the binding.”

Reviewer #2 (Recommendations for the authors):

(1) A table of all simulated trajectories, including simulation conditions, number of replicas, box size, number of atoms, equilibration length, recording time step, number of frames for further analysis.

We thank the Reviewer for this helpful suggestion. We have added a summary table of all simulations, including the requested details, to the Supplementary Information (Table 1).

Addition to the text. (Supplementary figures and tables: Table 2)

(2) The current NVT equilibration time was 0.125ns, and then no productive NPT simulations were mentioned as equilibration. Even though this is a simulation of mostly folded structures, it still takes some time for these amino acids to relax within the force field.

We thank the Reviewer for this constructive comment and acknowledge the validity of the concern. However, our simulations were extensively sampled, and equilibration was achieved within the first 50 ns of the production runs. Therefore, the segments of the trajectories from which we draw conclusions correspond to equilibrated states (see RMSD analysis, Figure 1). Additionally, binding free energy calculations (MM/PBSA) were carried out on the last 250 ns of the simulation replicas.

(3) At least three histograms were presented in Figure 2C, which I guess is from multiple simulations, and does not seem to be discussed.

We thank the Reviewer for pointing out the lack of reference to Figure 2C. We added the correct reference to the text where the groove width of luminal domains of human and yeast is discussed.

Author response image 1.

RMSD analysis of human IRE1_α_ cLD dimer simulated in complex with unfolded peptides.

Addition to the text. (Results section: The putative groove of human IREα cLD is dynamic but unable to contain peptides ) In simulations of the dimeric structures, the average groove width was 7.3 ± 0.1 Å for the human cLD and 8.9 ± 0.1 Å for the yeast cLD, averaged over three TIP3P and three TIP4P-D replicas per system (Fig. 2C).

(4) The comment regarding the CHARMM force field on Page 6 is not justified. Actually the force field the authors used (CHARMM36m, Jing et al Nat Methods 2016) did include scaling of TIP3P LJ parameters to correctly capture the dimensions of the intrinsically disordered proteins (IDPs). However, the authors cited a couple of examples of literature of previous versions of CHARMM force fields and commented that it cannot capture IDP dimensions with TIP3P.

We thank the Reviewer for pointing out this source of confusion. We cited the main papers of CHARMM as [4, 5], which were misleading, and following the Reviewer’s advice, we removed these citations.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “Current all-atom force fields used in MD simulations are mainly designed to reproduce the dynamics of folded and globular proteins [6].”

(5) I am fine that the authors used TIP4PD with CHARMM36m, but caution should be taken for such a combination of protein and water force fields. Note that when optimizing force fields for IDPs, one often has to balance protein-water interactions by either enhancing protein-water interactions, enhancing water dispersions, or reducing protein-protein interactions. So, all such optimization is dependent on both protein and water force fields. TIP4PD was designed to pair with Amber99sb-ildn or, most recently, Amber99sb-disp instead of CHARMM36m. This could result in rescaling of LJ parameters.

We thank the Reviewer for raising this issue. We argue that the TIP4P-D water model has been used in combination with the CHARMM36m force field [7] and has been shown to yield satisfactory results for disordered regions.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “The TIP4P-D water model was developed to address limitations of existing force fields in reproducing the structural ensembles of intrinsically disordered proteins and regions. It incorporates enhanced dispersion and moderately stronger electrostatic interactions to improve the balance between water dispersion and electrostatics [8]. Zapletal et al. [7] showed that for proteins containing both folded and disordered regions, the CHARMM36m force field [9] in combination with the TIP4P-D water model provides a robust framework, preventing collapse of disordered regions while preserving folded regions. Acknowledging that the behavior of disordered regions can be case-specific, we conducted molecular dynamics simulations of the two cLD dimer models using the CHARMM36m force field with both TIP3P and TIP4P-D water models.”

(6) I suggest referring to the methodology part for simulation details as much as possible when presenting the story.

We thank the Reviewer for this suggestion. In the revised manuscript, we now refer the reader to the Methodology section for detailed descriptions of the HDX-MS data analysis and the MM/PBSA free energy calculations.

Addition to the text. (Results section: Hydrogen-deuterium exchange experimental data validate the cLD dimer structure) “From our simulations, we calculated the theoretical deuterated fraction using the method by Bradshaw et al.[10] and compared it to the experimental data (Fig. 1C-D and Supplementary Fig. 10) (see Methods).”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

(7) Error bars and methodology of error analysis should be provided for all cases of all-atom simulations if possible, since convergence is always an issue when considering these conformational changes within microseconds of all-atom simulations.

We thank the Reviewer for the important observation. We agree and added error methodology for the estimation of theoretical deuterated fractions (Fig. 1C).

Addition to the text. (Figure C legend) “Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping.”

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To reproduce the time points after incubation in deuterium (D₂O), we computed deuterated fractions separately for each of the two monomers constituting a dimer for the time points 0.5 min (30 s) and 5 min (300 s). Then, we computed the mean and standard deviation over the data coming from replicas of the same cLD dimer model (AF or PDB model) and the same water model (TIP3P or TIP4P-D). To estimate the uncertainty of the mean values obtained from our datasets and the dataset from Amin-Wetzel et al. ([11] Figure 3—source data 1), we applied a non-parametric bootstrap resampling procedure. For each sequence range from HDX-MS analysis, we treated the measurements from the N=6 independent datasets as independent samples, accounting for 3 replicas each with two monomers (6 monomers total). We then generated 10,000 bootstrap replicates by sampling the datasets with replacement, maintaining the same number of samples N in each resample. For each replicate, we calculated the mean at each sequence position. The resulting distribution of bootstrap means was used to compute the standard deviation as an estimate of the standard error. We computed the difference between simulation and experimental data (deuterated fraction discrepancy), and for each residue, we selected as the ‘best structure’ the model with the discrepancy closest to zero among PDB-TIP3P, PDB-TIP4P-D, AF-TIP3P, and AF-TIP4P-D systems.”

(8) Technically I would call DR1 and DR2 linker regions within a folded structure. Their motions are quite restrained by the fold part. I therefore, am not sure how much TIP4PD really helps in contrast to a scaled TIP3P. A plot of structures colored with PLDDT score or b-factor within the PDB should be provided. Quantitative metrics of these regions (e.g. chi chi-squared) might help justify the choice of the AF model against the PDB model. Currently, the two models look very similar in Figures 1c and 1d. Similarly, quantitative metrics as a function of different simulation time windows will help justify the convergence of the simulation and indicate the flexibility of these regions.

We thank the Reviewer for this thoughtful comment. In response, we analyzed the AlphaFold2 and AlphaFold3 predictions, which consistently assign very low pLDDT values (<50) to the DR2 region, while DR1, is predicted with higher but still low confidence (50 < pLDDT < 70). These scores indicate intrinsic uncertainty in the structural definition of both regions, supporting their flexibility despite being located within a folded context.

Addition to the text. (Results section: The hIRE1_α_ cLD forms a stable dimer) “All five AlphaFold 2 predictions closely resembled the top-ranked model used for our simulations (Supplementary Fig. 7C). In contrast, the five AlphaFold 3 predictions yielded greater variability in DR2 organization and longer helices in DR2, but still consistently maintain low pLDDT scores in this region, indicating disorder (Supplementary Fig. 7D).”

Addition to the text. (Figure 7 C-D legend) “(C) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT). (D) Superposition of the 5 structures predicted by AlphaFold 3 for the cLD dimer and colored by confidence prediction score (pLDDT).”

(9) Fluorescence anisotropy seems to be an important set of experimental data to justify the binding of multiple unfolded peptides to IRE. I suggest the authors include a bar plot of binding affinity of different variants in Figure 3. The raw titration curves should also be included in SI.

We thank the Reviewer for this valuable suggestion. The binding affinities reported in previous studies are summarized in Table 2; the reader is referred to those works for the corresponding raw titration curves. The binding affinities for the cLD mutants analyzed in the present study are provided in Table 3, and the associated titration curves are shown in Figure 4G.

Addition to the text. (Figure 4G legend) “Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary figures and tables: Table 3) See Tab. 1

(10) The authors should discuss the dependence of initial orientations of unfolded peptides on the final results. The authors claimed that after 1 microsecond simulations, the orientation of these peptides to IRE changed. Quantitative metrics showing both the binding (e.g., number of contacts) and binding orientation (contact region or angles) should be provided to tell whether the simulation is converged. The comparison to the experimental data lacks quantitative metrics. The authors mentioned the dissociation of MPZ1N-2X-RD in half of the simulations; they might want to provide such a metric for all peptides. Technically, 1 microsecond brute-force simulation is quite short for observing such a binding event, and enhanced sampling methods (e.g. metadynamics) might be necessary for investigating binding. However, at least the presentation and interpretation of the current results should be improved for comparing simulations and experiments.

We thank the Reviewer for the insight. We expanded the discussion of the peptide orientation and added an analysis of the peptide angle with respect to the cLD central groove and contacts. Additionally, we inserted AlphaFold 3 predictions of all the simulated complexes.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0◦ orientation", as the peptide forms a 0 ◦ angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0◦) orientation (Supplementary Fig. 14). We refer to these poses as the "90◦ orientation" and "270◦ orientation".”

Addition to the text. (Supplementary Figures and Tables Fig. 14) “(A) Peptide orientation with respect to the central groove principal axis. The angle was computed as the dihedral angle described by the Cα atoms of Y161 residues (groove principal axis) and the C_α_ atoms of residues L1 and A12 of the MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 10 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between hIRE1α cLD dimer and MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 50 frames, while the shaded lines indicate the value per frame. The analysis were performed on three sets of simulations: "90 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis; "270 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis but flipped 180 degrees with respect to the 0 degree; "0 degrees" orientation, the peptide is placed parallel to the groove principal axis.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. ??A).”

Addition to the text. (Supplementary Figures and Tables Fig. 16A) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT).”

(11) I also have a couple of questions regarding the point mutant Y161R. a) The motivation of mutating Y161 to R is more speculative (Figures 4a,b) than quantitative. The authors might want to show an intermolecular contact map between IRE and unfolded peptides or IRE contact probability along residue indexes to show the interaction hotspots. Figure S11 only showed the structure instead of any metrics for such a purpose. b) It might be better to also show a histogram of the distances of Figure 4e and 4f. Figure 4f actually suggested 1 microsecond simulation is quite short to observe the dissociation event. c) Testing the mutation within the experiment, if possible, would clearly strengthen this part of the manuscript.

We thank the Reviewer for these constructive suggestions. We have added an analysis of intermolecular contacts for the Y161R and E102R mutants (Fig. 18A–B), which highlights the interaction hotspots between IRE1 residues and the unfolded peptides. To further characterize peptide–groove interactions, we now provide minimum peptide–groove distance time series for all peptides (Fig. 15B). Moreover, to experimentally support our simulations, we performed fluorescence anisotropy measurements on the MPZ1N-2X peptide with cLD WT and mutant constructs. These experiments confirm our computational observations (Fig. 4F–G and Fig. 18C).

Addition to the text. (Figure 18 legend) “(A) Number of contacts between residues 102 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between residues 161 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (C) Protein purification of WT hIREα LD and mutants E10R and Y161R.”

Addition to the text. (Figure 4F-G legend) “(F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(12) Similar comments of quantitative analysis (e.g. contact map as a function of simulation time) apply to the last part of results when discussing the intermolecular interactions. Observations such as "the interface predicted by AlphaFold showed stability across MD simulation replicas lasting 200 ns" were provided, but there is no quantitative analysis. How consistent was this observation across multiple replicas of simulations, and how many replicas were used?

We thank the Reviewer for this valuable suggestion. To provide a quantitative assessment, we performed new triplicate simulations of the BiP–cLD monomer complex and plotted the fraction of native contacts over time. These results, which demonstrate the consistency of the interface across replicas, are now included in the Supplementary Material.

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Figure 20 legend) “Fraction of native contacts between BiP and cLD monomer in simulations of the structures predicted by AlphaFold 3 without ligands or in complex with ADP or ATP. The dark lines indicate the rolling average of the fraction of native contacts over 100 frames, while the shaded lines indicate the value per frame. The fraction of native contacts (Q) was calculated according to the definition of Best et al. [12]: . For N pairs of native contacts (i, j), where is the distance of the pair in the initial configuration (here the AlphaFold 3 prediction), r_(i,j)(X) is the distance at frame X, β is a smoothing parameter (β = 50 nm⁻¹), λ is the tolerance of the reference distance (λ \= 1.8) and the cutoff used to define a contact between heavy atoms was 0.45 nm.”

(13) The figure legends are noted using lowercase letters but are described using uppercase.

We thank the Reviewer for pointing that out, and we changed everything to capital letters.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1: I am confused about the HDX-MS results shown in Figure 1. Here, I must also mention that I am not familiar with comparing HDX-MS experiments with MD simulations. The authors mention that they show the deuterated fraction computed from MD simulations for the PDB and AF model at time points 0.5 min and 5 min. However, this time certainly does not correspond to the MD simulation time, thus, it is unclear to me where the difference between the results comes from. Are the two time points some input parameters to the script used to calculate the deuterated fraction? Thus, I would ask the authors to better explain what is the difference in the results between the two time points. Especially, since the general reader might not be familiar with comparing HDX-MS experimental results to MD simulations. Furthermore, I would ask the authors to clarify in the Figure 1 caption that these time points do not correspond to the MD simulation time.

We thank the Reviewer for pointing us to this possible source of confusion. The time points are effectively input parameters to the calculations of theoretical deuterated fractions from MD simulations. We expanded the explanation of the method in the method section and clarified in the Figure 1 caption that these time points do not correspond to the MD simulation time.

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To determine the deuterated fraction of a peptide segment from simulations, the protection factor for each residue i, Pi, must be computed from the simulation snapshots, following the approach of Best and Vendruscolo [13]: . Here, N_C,i and N_H,i are the number of H-bonds and heavy-atom contacts of the backbone amide of residue i, and the scaling factors β_C and β_H are set to 0.35 and 2.0, respectively. The simulated deuterated fraction of a peptide segment, , defined by residues m_j +1 to n_j, was then calculated at any exchange time point t as:

Where m_j and n_j are the first and last residue numbers of the j-th protein fragment, respectively. The intrinsic exchange rate constants for each residue type () were obtained from Bai et al. with updated acidic residues and glycine [14, 15].”

Addition to the text. (Figure 1 legend: ) “This time point corresponds to experimental incubation times, not MD simulation time.”

Addition to the text. (Figure 10 legend: ) “Time points correspond to experimental incubation times, not MD simulation time.”

(2) For AlphaFold 2 Multimer prediction, the authors only considered the top predicted structure. However, AF2-M, one generally obtains 5 structures, and it is also possible to obtain more structures by using an additional random seed. Thus, it would be interesting if the authors would consider the difference between the 5 structures they obtained from the AF2-M prediction. Are they all very similar? (Especially considering the DR1 and DR2 segments, that is the main difference between the PDB and AF2 structures). Analyzing the different predicted AF2 structures would give more insight into the accuracy of the AF2-M predicted model.

We thank the Reviewer for this insightful suggestion. All AF2-M predicted structures were found to be highly similar, and we now include them in Figure 7E for comparison.

Addition to the text. (Figure 7E legend) “(E) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT).”

(3) On Page 6, the authors talk about a "an early PDB model". First, I find the nomenclature "early" confusing here; perhaps it would be better to talk about "an initial PDB model", but I leave it up to the authors to think about if they want to change that. More importantly, reading the Comp. detail on Page 23, it is not so clear what the difference is between the "early" and "final" PDB models, and how the difference in their setups leads to different results. The information is somewhat there on Page 6 and Page 23, but it can be made much clearer. Thus, I would ask the authors to better explain the difference between the early and final PDB models.

We thank the Reviewer for this helpful comment. In the revised manuscript, we have clarified the terminology and provided a more explicit explanation of the differences between the two IRE1 models, both in the Results section and in the Methods.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “An initial PDB model with modified side chain orientations in residues L116 and Y166 due to the modelling of neighbouring missing DR1, caused the dimer to dissociate in one-third of the replicas. [...] The final PDB model, with correctly oriented L116 and Y166 (Supplementary Fig. 9B), was stable in simulations in both TIP3P and TIP4P-D water (Supplementary Fig. 7B).”

Addition to the text. (Methods section: IRE1_α_ core Luminal Domain (cLD) structural models - Human PDB dimer) “An initial PDB model was briefly equilibrated in NPT, and a conformation with a groove width of approximately 0.6 nm was selected. This snapshot was used as the initial structure for the initial “PDB model” simulations, in which the dimer dissociates.”

(4) Page 12: "In early simulations", again, I find the nomenclature "early" confusing here. Perhaps it would be better to talk about "In initial simulations" or "In preliminary simulations", but I leave it up to authors to think about this.

We thank the Reviewer for pointing out this possible source of confusion. We improved the text by referring to these simulations based on the different orientations of the peptide on the cLD dimer in the modeled complex.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0° orientation", as the peptide forms a 0° angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0°) orientation (Supplementary Fig. 14). We refer to these poses as the "90° orientation" and "270° orientation".”

Here, we provide a detailed description of the additional changes made to the manuscript.

Additional edits to the manuscript

Following discussions with Prof. Dr. David Ron, we refined our BiP model by removing the signal peptide (residues 1–18). Using AlphaFold 3, we predicted BiP–cLD heterodimeric complexes in the presence of ADP, ATP, or without nucleotide. Each of the three complexes was simulated in TIP3P water, in three independent replicas of 1 µs each.

Addition to the text. (Results section: hIRE1α cLD intermolecular interactions guide the activation process) “We used AlphaFold 3 to model the interaction between a cLD monomer and BiP (residues E19–L654) in the presence of ATP and ADP (Fig. 5B, Supplementary Fig. 19A). Prediction quality was limited in the apo and ADP-bound states (pTM = 0.48, ipTM = 0.59; pTM = 0.49, ipTM = 0.61, respectively), whereas ATP binding improved accuracy (pTM = 0.66, ipTM = 0.72). The predicted interfaces involved DR2, particularly residues 314PLLEG-318, forming a short parallel β-sheet with the substrate-binding domain (SBD) of BiP through two hydrogen bonds. All AlphaFold 3 models were stable across three 1-µs simulations (Supplementary Fig. 19B), with cLD–BiP interfaces retaining 60–80% of initial contacts (Supplementary Fig. 20). In the apo and ADP-bound states, the nucleotide-binding domain (NBD) showed high Predicted Aligned Error (PAE) relative to the cLD, indicating uncertain positioning of the two domains relative to each other. Notably, in the ADP-bound state, which is thought to interact with hIRE1α cLD, the NBD remained mobile but proximal to the αB-helices, thereby restricting access to this region. Together, the AlphaFold 3 predictions suggest that BiP engages hIRE1α cLD by sterically hindering the oligomerization interface defined by DR2 and the αB-helices [16].”

Addition to the text. (Figure 5 legend) “(B) BiP-cLD monomer complex as predicted by AlphaFold (BiP in shades of purple, cLD in orange) before the simulation (t = 0 µs) and at the end of the simulation (t = 1 µs). The SBD (residues E19-D408) is colored in light purple, and the NDB (residues C420-E650) in dark purple, and the interdomain linker (residues D409-V419) and KDEL motif (residues K651-L654) in light purple.”

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Methods section: cLD monomer in complex with BiP) “The BiP-cLD heterodimer systems were predicted with AlphaFold 3 using the AlphaFold server[17] at https://alphafoldserver.com/. The hIRE1α cLD sequence used is the same used for predicting the dimer: the PDB 2HZ6 sequence, Uniprot identifier O75460 with mutations C127S and C311S, and residues P29-P368. The BiP sequence used is taken from UniProt identifier P11021, residues E19L654. We predicted three complexes: one without any nucleotide, one containing ADP, and another containing ATP. Simulations of the BiP-cLD complex were run in TIP3P water.”

We have updated the Zenodo repository with additional data and calculations, and the corresponding link is provided in the manuscript.

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Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Thach et al. report on the structure and function of trimethylamine N-oxide demethylase (TDM). They identify a novel complex assembly composed of multiple TDM monomers and obtain high-resolution structural information for the catalytic site, including an analysis of its metal composition, which leads them to propose a mechanism for the catalytic reaction.

In addition, the authors describe a novel substrate channel within the TDM complex that connects the N-terminal Zn²-dependent TMAO demethylation domain with the C-terminal tetrahydrofolate (THF)-binding domain. This continuous intramolecular tunnel appears highly optimized for shuttling formaldehyde (HCHO), based on its negative electrostatic properties and restricted width. The authors propose that this channel facilitates the safe transfer of HCHO, enabling its efficient conversion to methylenetetrahydrofolate (MTHF) at the C-terminal domain as a microbial detoxification strategy.

Strengths:

The authors provide convincing high-resolution cryo-EM structural evidence (up to 2 Å) revealing an intriguing complex composed of two full monomers and two half-domains. They further present evidence for the metal ion bound at the active site and articulate a plausible hypothesis for the catalytic cycle. Substantial effort is devoted to optimizing and characterizing enzyme activity, including detailed kinetic analyses across a range of pH values, temperatures, and substrate concentrations. Furthermore, the authors validate their structural insights through functional analysis of active-site point mutants.

In addition, the authors identify a continuous channel for formaldehyde (HCHO) passage within the structure and support this interpretation through molecular dynamics simulations. These analyses suggest an exciting mechanism of specific, dynamic, and gated channeling of HCHO. This finding is particularly appealing, as it implies the existence of a unique, completely enclosed conduit that may be of broad interest, including potential applications in bioengineering.

Weaknesses:

Although the idea of an enclosed channel for HCHO is compelling, the experimental evidence supporting enzymatic assistance in the reaction of HCHO with THF is less convincing. The linear regression analysis shown in Figure 1C demonstrates a THF concentration-dependent decrease in HCHO, but the concentrations used for THF greatly exceed its reported KD (enzyme concentration used in this assay is not reported). It has previously been shown that HCHO and THF can couple spontaneously in a non-enzymatic manner, raising the possibility that the observed effect does not require enzymatic channeling. An additional control that can rule out this possibility would help to strengthen the evidence. For example, mutating the THF binding site to prevent THF binding to the protein complex could clarify whether the observed decrease in HCHO depends on enzyme-mediated proximity effects. A mutation which would specifically disable channeling could be even more convincing (maybe at the narrowest bottleneck).

We agree with the reviewer that HCHO and THF can react spontaneously in a non-enzymatic manner, and our experiments were not intended to demonstrate enzymatic channeling. The linear regression analysis in Figure 1C was designed solely to confirm that HCHO reacts with THF under our assay conditions. Accordingly, THF was titrated over a broad concentration range starting from zero, and the observed THF concentration–dependent decrease in HCHO reflects this chemical reactivity.

We do not interpret these data as evidence that the enzyme catalyzes or is required for the HCHO–THF coupling reaction. Instead, the structural observation of an enclosed channel is presented as a separate finding. We have clarified this point in the revised text to avoid overinterpretation of the biochemical data (page 2, line 16).

Another concern is that the observed decrease in HCHO could alternatively arise from a reduced production of HCHO due to a negative allosteric effect of THF binding on the active site. From this perspective, the interpretation would be more convincing if a clear coupled effect could be demonstrated, specifically, that removal of the product (HCHO) from the reaction equilibrium leads to an increase in the catalytic efficiency of the demethylation reaction.

We agree that, in principle, a decrease in detectable HCHO could also arise from an indirect effect of THF binding on enzyme activity. However, in our study the experiment was not designed to assess catalytic coupling or allosteric regulation. The assay in question monitors HCHO levels under defined conditions and does not distinguish between changes in HCHO production and downstream consumption.

Additionally, we do not interpret the observed decrease in HCHO as evidence that THF binding enhances catalytic efficiency, or that removal of HCHO shifts the reaction equilibrium. Instead, the data are presented to establish that HCHO can react with THF under the assay conditions. Any potential allosteric effects of THF on the demethylation reaction, or kinetic coupling between HCHO removal and catalysis, are beyond the scope of the current study, and are not claimed.

While the enzyme kinetics appear to have been performed thoroughly, the description of the kinetic assays in the Methods section is very brief. Important details such as reaction buffer composition, cofactor identity and concentration (Zn²⁺), enzyme concentration, defined temperature, and precise pH are not clearly stated. Moreover, a detailed methodological description could not be found in the cited reference (6), if I am not mistaken.

Thank you for the suggestion. We have added reference [24] to the methodological description on page 8. The Methods section has been revised accordingly on page 8 under “TDM Activity Assay,” without altering the Zn²⁺ concentration.

The composition of the complex is intriguing but raises some questions. Based on SDS-PAGE analysis, the purified protein appears to be predominantly full-length TDM, and size-exclusion chromatography suggests an apparent molecular weight below 100 kDa. However, the cryo-EM structure reveals a substantially larger complex composed of two full-length monomers and two half-domains.

We appreciate the reviewer’s careful analysis of the apparent discrepancy between the biochemical characterization and the cryo-EM structure. This issue is addressed in Figure S1, which may have been overlooked.

As shown in Figure S1, the stability of TDM is highly dependent on protein and salt conditions. At 150 mM NaCl, SEC reveals a dominant peak eluting between 10.5 and 12 mL, corresponding to an estimated molecular weight of ~170–305 kDa (blue dot, Author response image 1). This fraction was explicitly selected for cryo-EM analysis and yields the larger complex observed in the reconstruction. At lower salt concentrations (50 mM) or higher (>150 mM NaCl), the protein either aggregates or elutes near the void volume (~8 mL).

SDS–PAGE analysis detects full-length TDM together with smaller fragments (~40–50 kDa and ~22–25 kDa). The apparent predominance of full-length protein on SDS–PAGE likely reflects its greater staining intensity per molecule and/or a higher population, rather than the absence of truncated species.

Author response image 1.

Given the lack of clear evidence for proteolytic fragments on the SDS-PAGE gel, it is unclear how the observed stoichiometry arises. This raises the possibility of higher-order assemblies or alternative oligomeric states. Did the authors attempt to pick or analyze larger particles during cryo-EM processing? Additional biophysical characterization of particle size distribution - for example, using interferometric scattering microscopy (iSCAT)-could help clarify the oligomeric state of the complex in solution.

Cryo-EM data were collected exclusively from the size-exclusion chromatography fraction eluting between 10.5 and 12 mL. This fraction was selected to isolate the dominant assembly in solution. Extensive 2D and 3D particle classification did not reveal distinct classes corresponding to smaller species or higher-order oligomeric assemblies. Instead, the vast majority of particles converged to a single, well-defined structure consistent with the 2 full-length + 2 half-domain stoichiometry.

A minor subpopulation (~2%) exhibited increased flexibility in the N-terminal region of the two full-length subunits, but these particles did not form a separate oligomeric class, indicating conformational heterogeneity rather than alternative assembly states (Author response image 2). Together, these data support the 2+2½ architecture as the predominant and stable complex under the conditions used for cryo-EM. Additional techniques, such as iSCAT, would provide complementary information, but are not required to support the conclusions drawn from the SEC and cryo-EM analyses presented here.

Author response image 2.

The authors mention strict symmetry in the complex, yet C2 symmetry was enforced during refinement. While this is reasonable as an initial approach, it would strengthen the structural interpretation to relax the symmetry to C1 using the C2-refined map as a reference. This could reveal subtle asymmetries or domain-specific differences without sacrificing the overall quality of the reconstruction.

We thank the reviewer for this thoughtful suggestion. In standard cryo-EM data processing, symmetry is typically not imposed initially to minimize potential model bias; accordingly, we first performed C1 refinement before applying C2 symmetry. The resulting C1 reconstructions revealed no detectable asymmetry or domain-specific differences relative to the C2 map. In addition, relaxing the symmetry consistently reduced overall resolution, indicating lower alignment accuracy and further supporting the presence of a predominantly symmetric assembly.

In this context, the proposed catalytic role of Zn²⁺ raises additional questions. Why is a 2:1 enzyme-to-metal stoichiometry observed, and how does this reconcile with previous reports? This point warrants discussion. Does this imply asymmetric catalysis within the complex? Would the stoichiometry change under Zn²⁺-saturating conditions, as no Zn²⁺ appears to be added to the buffers? It would be helpful to clarify whether Zn²⁺ occupancy is equivalent in both active sites when symmetry is not imposed, or whether partial occupancy is observed.

The observed ~2:1 enzyme-to-Zn²⁺ stoichiometry likely reflects the composition of the 2 full-length + 2 half-domain (2+2½) complex. In this assembly, only the core domains that are fully present in the complex contribute to metal binding. The truncated or half-domains lack the Zn²⁺ binding domain. As a result, only two metal-binding sites are occupied per assembled complex, consistent with the measured stoichiometry.

We note that Zn²⁺ was not deliberately added to the buffers, so occupancy may not reflect full saturation. Based on our cryo-EM and biochemical data, both metal-binding sites in the full-length subunits appear to be occupied to an equivalent extent, and no clear evidence of asymmetric catalysis is observed under these current experimental conditions. Full Zn²⁺ saturation could potentially increase occupancy, but was not explored in these experiments.

The divalent ion Zn²⁺ is suggested to activate water for the catalytic reaction. I am not sure if there is a need for a water molecule to explain this catalytic mechanism. Can you please elaborate on this more? As one aspect, it might be helpful to explain in more detail how Zn-OH and D220 are recovered in the last step before a new water molecule comes in.

Thank you for your suggestion. We revised our text in page 2 as bellow.

Based on our structural and biochemical data, we propose a structurally informed working model for TMAO turnover by TDM (Scheme 1). In this model, Zn²⁺ plays a non-redox role by polarizing the O–H bond of the bound hydroxyl, thereby lowering its pK_a. The D220 carboxylate functions as a general base, abstracting the proton to generate a hydroxide nucleophile. This hydroxide then attacks the electrophilic N-methyl carbon of TMAO, forming a tetrahedral carbinolamine (hemiaminal) intermediate. Subsequent heterolytic cleavage of the C–N bond leads to the release of HCHO. D220 then switches roles to act as a general acid, donating a proton to the departing nitrogen, which facilitates product release and regenerates the active site. This sequence allows a new water molecule to rebind Zn²⁺, enabling subsequent catalytic turnovers. This proposed pathway is consistent with prior mechanistic studies, in which water addition to the azomethine carbon of a cationic Schiff base generates a carbinolamine intermediate, followed by a rate-limiting breakdown to yield an amino alcohol and a carbonyl compound, in the published case, an aldehyde (Pihlaja et al., J. Chem. Soc. Perkin Trans. 2, 1983, 8, 1223–1226).

Overall, the authors were successful in advancing our structural and functional understanding of the TDM complex. They suggest an interesting oligomeric complex composition which should be investigated with additional biophysical techniques.

Additionally, they provide an intriguing hypothesis for a new type of substrate channeling. Additional kinetic experiments focusing on HCHO and THF turnover by enzymatic proximity effects would strengthen this potentially fundamental finding. If this channeling mechanism can be supported by stronger experimental evidence, it would substantially advance our understanding and knowledge of biologic conduits and enable future efforts in the design of artificial cascade catalysis systems with high conversion rate and efficiency, as well as detoxification pathways.

Reviewer #2 (Public review):

Summary:

The manuscript reports a cryo-EM structure of TMAO demethylase from Paracoccus sp. This is an important enzyme in the metabolism of trimethylamine oxide (TMAO) and trimethylamine (TMA) in human gut microbiota, so new information about this enzyme would certainly be of interest.

Strengths:

The cryo-EM structure for this enzyme is new and provides new insights into the function of the different protein domains, and a channel for formaldehyde between the two domains.

Weaknesses:

(1) The proposed catalytic mechanism in this manuscript does not make sense. Previous mechanistic studies on the Methylocella silvestris TMAO demethylase (FEBS Journal 2016, 283, 3979-3993, reference 7) reported that, as well as a Zn2+ cofactor, there was a dependence upon non-heme Fe2+, and proposed a catalytic mechanism involving deoxygenation to form TMA and an iron(IV)-oxo species, followed by oxidative demethylation to form DMA and formaldehyde.

In this work, the authors do not mention the previously proposed mechanism, but instead say that elemental analysis "excluded iron". This is alarming, since the previous work has a key role for non-heme iron in the mechanism. The elemental analysis here gives a Zn content of about 0.5 mol/mol protein (and no Fe), whereas the Methylocella TMAO demethylase was reported to contain 0.97 mol Zn/mol protein, and 0.35-0.38 mol Fe/mol protein. It does, therefore, appear that their enzyme is depleted in Zn, and the absence of Fe impacts the mechanism, as explained below.

The proposed catalytic mechanism in this manuscript, I am sorry to say, does not make sense to me, for several reasons:

(i) Demethylation to form formaldehyde is not a hydrolytic process; it is an oxidative process (normally accomplished by either cytochrome P450 or non-heme iron-dependent oxygenase). The authors propose that a zinc (II) hydroxide attacks the methyl group, which is unprecedented, and even if it were possible, would generate methanol, not formaldehyde.

(ii) The amine oxide is then proposed to deoxygenate, with hydroxide appearing on the Zn - unfortunately, amine oxide deoxygenation is a reductive process, for which a reducing agent is needed, and Zn2+ is not a redox-active metal ion;

(iii) The authors say "forming a tetrahedral intermediate, as described for metalloproteinase", but zinc metalloproteases attack an amide carbonyl to form an oxyanion intermediate, whereas in this mechanism, there is no carbonyl to attack, so this statement is just wrong.

So on several counts, the proposed mechanism cannot be correct. Some redox cofactor is needed in order to carry out amine oxide deoxygenation, and Zn2+ cannot fulfil that role. Fe2+ could do, which is why the previously proposed mechanism involving an iron(IV)-oxo intermediate is feasible. But the authors claim that their enzyme has no Fe. If so, then there must be some other redox cofactor present. Therefore, the authors need to re-analyse their enzyme carefully and look either for Fe or for some other redox-active metal ion, and then provide convincing experimental evidence for a feasible catalytic mechanism. As it stands, the proposed catalytic mechanism is unacceptable.

We thank the reviewer for the detailed and thoughtful mechanistic critique. We fully agree that Zn²⁺ is not redox-active, and cannot directly mediate oxidative demethylation or amine oxide deoxygenation. We acknowledge that the oxidative step required for the conversion of TMAO to HCHO is not explicitly resolved in the present study. Accordingly, we have revised the manuscript to remove any implication of Zn²⁺-mediated redox chemistry, and have eliminated the previously imprecise analogy to zinc metalloproteases.

We recognize and now discuss prior biochemical work on TMAO demethylase from Methylocella silvestris (MsTDM), which proposed an iron-dependent oxidative mechanism (Zhu et al., FEBS 2016, 3979–3993). That study reported approximately one Zn²⁺ and one non-heme Fe²⁺ per active enzyme, implicated iron in catalysis through homology modeling and mutagenesis, and used crossover experiments suggesting a trimethylamine-like intermediate and oxygen transfer from TMAO, consistent with an Fe-dependent redox process. However, that system lacked experimental structural information, and did not define discrete metal-binding sites.

In contrast,

(1) Our high-resolution cryo-EM structures and metal analyses of TDM consistently reveal only a single, well-defined Zn²⁺-binding site, with no structural evidence for an additional iron-binding site as in the previous report (Zhu et al., FEBS 2016, 3979–3993).

(2) To investigate the potential involvement of iron, we expressed TDM in LB medium supplemented with Fe(NH₄)₂SO₄ and determined its cryo-EM structure. This structure is identical to the original one, and no EM density corresponding to a second iron ion was observed. Moreover, the previously proposed Fe²⁺-binding residues are spatially distant (Figure S6).

(3) ICP-MS analysis shows undetectable Iron, and only Zinc ion (Figure S5).

(4) Our enzyme kinetics analysis with the TDM without Iron is comparable to that of from MsTDM (Figure 1A). The differences in Km and Vmax we propose is due to the difference in the overall sequence of the enzymes. Please also see comment at the end on a new published paper on MsTDM.

While we cannot comment on the MsTDM results, our ‘experimental’ results do not support the presence of an iron-binding site. Our data indicate that this chemistry is unlikely to be mediated by a canonical non-heme iron center as proposed for MsTDM. We therefore revised our model as a structural framework that rationalizes substrate binding, metal coordination, and product stabilization, while clearly delineating the limits of mechanistic inference supported by the current data.

The scheme 1 and proposal mechanism section were revised in page 4. Figure S6 was added.

(2) Given the metal content reported here, it is important to be able to compare the specific activity of the enzyme reported here with earlier preparations. The authors do quote a Vmax of 16.52 µM/min/mg; however, these are incorrect units for Vmax, they should be µmol/min/mg. There is a further inconsistency between the text saying µM/min/mg and the Figure saying µM/min/µg.

Thank you for the correction. We converted the V_max unit to nmol/min/mg. and revised the text in page 2. We also compared with the value of the previous report in the TDM enzyme by revising the text on page 2. See also the note on a newly published manuscript and its comparison.

(3) The consumption of formaldehyde to form methylene-THF is potentially interesting, but the authors say "HCHO levels decreased in the presence of THF", which could potentially be due to enzyme inhibition by THF. Is there evidence that this is a time-dependent and protein-dependent reaction? Also in Figure 1C, HCHO reduction (%) is not very helpful, because we don't know what concentration of formaldehyde is formed under these conditions; it would be better to quote in units of concentration, rather than %.

We appreciate this important point. We have revised Figure 1C to present HCHO levels in absolute concentration units. While the current data demonstrate reduced detectable HCHO in the presence of THF, we agree that distinguishing between HCHO consumption and potential THF-mediated enzyme inhibition would require dedicated time-course and protein-dependence experiments. We have therefore revised the description to avoid overinterpretation and limit our conclusions to the observed changes in HCHO concentration in page 2, line 18-19.

(4) Has this particular TMAO demethylase been reported before? It's not clear which Paracoccus strain the enzyme is from; the Experimental Section just says "Paracoccus sp.", which is not very precise. There has been published work on the Paracoccus PS1 enzyme; is that the strain used? Details about the strain are needed, and the accession for the protein sequence.

Thank you for this comment. We now indicate that the enzyme is derived from Paracoccus sp. DMF and provide the accession number for the protein sequence (WP_263566861) in the Experimental Section (page 8, line 4).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The ITC experiment requires a ligand-into-buffer titration as an additional control. Also, maybe I misunderstood the molar ratio or the concentrations you used, but if you indeed added a total of 4.75 μL of 20 μM THF into 250 μL of 5 μM TDM, it is not clear to me how this leads to a final molar ratio of 3.

We thank the reviewer for this suggestion. A ligand-into-buffer control ITC experiment was performed and is now included in Figure S8C, which shows no realizable signal.

Regarding the molar ratio, it is our mistake. The experiment used 2.45 μL injections of 80 μM THF into 250 μL of 5 μM TDM. This corresponds to a final ligand concentration of ~12.8 μM, giving a ligand-to-protein molar ratio of ~2.6. We revised our text in page 9, ITC section.

(2) Characterization/quality check of all mutant enzymes should be performed by NanoDSF, CD spectroscopy or similar techniques to confirm that proteins are properly folded and fit for kinetic testing.

We appreciate the reviewer’s suggestion. All mutant proteins, including D220A, D367A, and F327A, were purified with yields similar to the wild-type enzyme. Additionally, cryo-EM maps of the mutants show well-defined density and overall structural integrity consistent with the wild-type. These findings indicate that the introduced mutations do not significantly affect protein folding, supporting their use for kinetic analysis. While NanoDSF might reveal differences in thermal stability due to mutations, it does not provide structural information. Our conclusions are not based on minor differences in thermostability. Our cryo-EM structures of the mutants offer much more reliable structural data than CD spectroscopy.

(3) Best practice would suggest overlapping pH ranges between different buffer systems in the pH-dependence experiments to rule out buffer-specific effects independent of pH.

We thank the reviewer for this helpful suggestion. We agree that overlapping pH ranges between different buffer systems can be valuable for excluding buffer-specific effects. In this study, the pH-dependence experiments were intended to provide a qualitative assessment of pH sensitivity rather than a detailed analysis of buffer-independent pKa values. While we cannot fully exclude minor buffer-specific contributions, the overall trends observed were reproducible and sufficient to support the conclusions drawn. We have added a clarifying statement to the revised manuscript to reflect this consideration, page 2, line 12.

(4) Structural comparison revealed high similarity to a THF-binding protein, with superposition onto a T protein.": It would be nice to show this as an additional figure, as resolution and occupancy for THF are low.

We thank the reviewer for this suggestion. To address this point, we have revised Figure S6 by adding an additional panel (C, now is Figure S7C) showing the structural superposition of TDM with the THF-binding T protein. This comparison is included to better illustrate the structural similarity, despite the limited resolution and partial occupancy of THF density in our map.

(5) Editing could have been done more thoroughly. Some spelling mistakes, e.g. "RESEULTS", "redius", "complec"; kinetic rate constants should be written in italic (not uniform between text and figures); Prism version is missing; Vmax of 16.52 µM/min/mg - doublecheck units; Figure S1B: The "arrow on the right" might have gone missing.

We corrected the spelling in page 2 ~ line 10, page 5 ~ line 34, page 6 ~ line40. All were highlighted as blue color. Prism version was added. The arrow was added into figure S1B. The Vmax unit is corrected to nmol/min/mg

Reviewer #2 (Recommendations for the authors):

(1) The authors must re-examine the metal content of their purified enzyme, looking in particular for Fe or another redox-active metal ion, which could be involved in a reasonable catalytic mechanism.

We thank the reviewer for this suggestion and have carefully re-examined the metal content of TDM. Elemental analyses by EDX and ICP-MS consistently detected Zn²⁺ in purified TDM (Zn:protein ≈ 1:2), whereas Fe was below the detection limit across multiple independent preparations (Fig. S5A,B). To assess whether iron could be incorporated or play a functional role, we expressed TDM in E. coli grown in LB medium supplemented with Fe(NH₄SO₄)₂ and performed activity assays in the presence of exogenous Fe²⁺. Neither condition resulted in enhanced enzymatic activity.

Consistent with these biochemical data, all cryo-EM structures reveal a single, well-defined metal-binding site coordinated by three conserved cysteine residues and occupied by Zn²⁺, with no evidence for an additional iron species or other redox-active metal site.

(2) The specific activity of the enzyme should be quoted in the same units as other literature papers, so that the enzyme activity can be compared. It could be, for example, that the content of Fe (or other redox-active metal) is low, and that could then give rise to a low specific activity.

Thank you for the suggestion, we quoted the enzyme units as similar with previous report. and revised the text in in page 2.

Since the submission of our paper a new report on MsTDM has been published (Cappa et al., Protein Science 33(11), e70364). It further supports our findings. First, the reported kinetic parameters using ITC (Vmax = 0.309 μmol/s, approximately 240 nmol/min/mg; Km = 0.866 mM) are comparable to our observed (156 nmol/min/mg and 1.33 mM, respectively) in the absence of exogenous iron. Second, the optimal pH for enzymatic activity similar to that observed in our paraTDM. Third, the reported two-state unfolding behavior is consistent with our cryo-EM structural observations, in which the more dynamic subunits appear to destabilize prior to unfolding of the core domains. Based on these findings, we now propose that Zn²⁺ appears to function primarily as an organizational cofactor at the core catalytic domain (revised Scheme 1).

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

Summary:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments both from the rodent and the human literature such as splitter cells, lap cells, the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over/under representation of context information.

My general assessment of the work is unchanged, and I still have some questions requesting methodological clarification

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, action selection. The model also nicely links ideas from reinforcement learning to a neuronally interpretable mechanisms, e.g. learning a value function from hippocampal activity.

Weaknesses:

The presentation, particularly of the methodological aspects, needs to be heavily improved. Judgment of generality and plausibility of the results is severely hampered but is essential, particularly for the conclusions related to psychiatric disorders. In its present form, it is impossible to judge whether the claims and conclusions made are justified. Also, the lack of clarity strongly reduces the impact of the work on the field.

Thank you for pointing this out.

In the revised text, we clarified the definition of “time step” and how hippocampal neurons behaved in each time step (see individual comments below). Also, we clarified the implementation of disorder conditions in our model by indicating the exact neuron numbers of the stimulus domain in H module as below. (Other parameters were common in all conditions.)

“𝑋 consists of two domains: stimulus domain 𝑋 and context domain 𝑋. The neuron ratio in the stimulus domain over the whole neurons dim 𝑋/𝑁 is 16.7% (200 neurons) for the control condition, 2.5% (30 neurons) for the SZ condition, and 50% (600 neurons) for the ASD condition.”

Comments:

The authors have made strong efforts to improve on their description of the methods, however, it is still very hard to understand. As a result of some of their clarifications, new issues appeared that I was not able to extract in the previous version.

(1) Particularly I had problems figuring out how the individual dynamical systems are interrelated (sequences, attractor, action, learning). As I understand it now (and I still might be wrong) there is one discrete time dynamics, where in each time step one action takes place as well as the attractor and sequence dynamics are moved one step forward. Also, synaptic updates happen in every one of those time steps. The authors may verify or correct my interpretations and further improve on their description in the manuscript. It is also confusing that time in the figure panels is given in units of trials, where each trial may consist of (maybe different amounts of) multiple time steps. Are the thin horizontal red ad blue lines time steps?

Thank you for raising the confusing point.

The reviewer’s understanding is correct. In our model, at each time step the agents transition to the next environmental state (which also corresponds to the contextual state). During this step, each processing stage proceeds in order: Context selector performs attractor selection, Sequence composer performs sequence selection, followed by action selection and synaptic updates. As learning progresses and hippocampal sequences begin to predict longer futures, reducing the need for step-by-step planning. However, at least at the beginning of each task, all processes are conducted at each time step (see Fig. 1G).

In all tasks, trials are reset when the agents visit the reward sites (i.e., S4 or S5). n Fig. 2C, for example, one trial consists of three time steps (i.e., three state transitions), and the red and blue shaded regions indicate individual trials. During each time step, two types of hippocampal neurons are activated: a state-coding neuron and a transition-coding neuron. (In contrast, in X, one contextual state is active during one time step). Therefore, in Fig. 2E, two neuronal activities correspond to a single time step.

For clarification, we have revised Fig. 2 and related descriptions in the manuscript as follows.

“Here, we simplified this task by using an environment with five discrete states (S1-S5), i.e., five discrete external stimuli (Figure 2A), where agents transition to the next state at each time step.”

“Figure 2C illustrates an example of both the environmental state transition and the corresponding contextual state transition of an agent, with each trial resetting upon visiting the reward sites (S4 or S5). ”

“At each time step, one state-coding neuron and one transition-coding neuron are active in this order.”

“At each time step, the agents transition between environmental states.”

“The model’s computational dynamics are fundamentally synchronized with the environmental (behavioral) time step, and at each time step, the agents transition to the next environmental state. Upon a state transition, the agents first perform contextual state estimation by Context selector and activate a corresponding hippocampal neuron.”

(2) As a consequence of my new understanding of the model dynamics, I have become doubts about the interpretation of the attractor network as context encoding. Since the X population mainly serves to disambiguate sequence continuation, right before the action has to be taken (active for only two time steps in Figure 1C?) they could also be considered to encode task space (El-Gaby et al. 2024; doi: 10.1038/s41586-024-08145-x).

We thank the reviewer for this insightful comment.

First of all, we would like to clarify that Figure 1C shows the following process: the activity of H at time step t−1 and the external stimulus at time step t jointly provide input to X module, and the activity of X settles into a contextual state at the time step t. As explained in our response to comment (1), the activity of X remains constant during each time step.

The primary function of X module in our model is to disambiguate the environmental states defined by the external stimuli based on the history information. It is true that, in practice, whether an ongoing sequence is maintained or remapped depends on whether the observed stimulus is consistent with the predicted stimulus. However, this is a consequence of the predictive sequence obtained from scratch rather than the primary computational role of X module. In contrast, X module becomes particularly important when past experience does not uniquely determine the next state. In this situation, the agent must infer the contextual state by associating the current situation with previously experienced contexts, rather than relying solely on temporal continuity.

We also add that, in most successful cases, the contextual states learned by the agent often correspond to the hidden states of each task as a result of disambiguation. In this sense, the resulting representation may resemble a “task space” encoding, as suggested by the reviewer. However, an important aspect of our model is that the agent does not assume the existence or number of hidden states a priori. Instead, we considered the situation where the agent initially underestimates the number of contextual states, and through remapping it incrementally increases the number of contextual representations. When the number of contextual states matches the number of hidden task states, the task is typically solved.

(3) Also technically, I wonder why the authors introduce the criterion of 50(!) time steps to allow the attractor to converge, if the state of the attractor network is only relevant in one time step to choose the appropriate continuation of the sequence of actions. Is attractor dynamics important at all? What would happen if just the input and output weights to the X population are kept and the recurrent weights are set 0?

We thank the reviewer for raising this confusing point.

First, we would like to clarify that the “50 iterations” mentioned in the manuscript does not refer to 50 environmental time steps. We implemented multiple iterations of attractor updates (typically until convergence) by Context selector within each behavioral time step.

We clarify this point in the Method section as below.

“After history-based or landmark-based initialization, X iteratively updates its contextual state at the beginning of each time step according to the associative memory dynamics:”

The recurrent connectivity within the X population is essential for attractor updates. If the recurrent weights were removed (i.e., set to zero), the network would lose the ability to retrieve distinct contextual states for the same stimulus. In that case, the model would be unable to solve the context-dependent task as we showed in this manuscript.

(4) Figure 3E: How many time steps are the H cells active (red bars?) Figure 4J: What are the units of the time axis?

Thank you for pointing this out.

In Figure 3E, each time step is indicated in the X-axis ticks (i.e., each environmental state). As we explained in the comment (1), two hippocampal neurons’ activity (red bars) corresponds to each time step.

Similarly, in Figure 4J, each time step is indicated in the X-axis ticks. To better represent the results, we added descriptions of the environmental states in our model to the X-axis tick labels in Figure 4J.

We added the following texts below in Figure captions.

“The x-axis represents each time step (corresponding to environmental states), and the y-axis shows the sorted activity of H module.”

“The x-axis represents each time step (corresponding to environmental states), and the y-axis shows the decoding accuracy of each context based on hippocampal activity.”

Author response:

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

Joint Public Reviews:

In this manuscript, the authors proposed an approach to systematically characterise how heterogeneity in a protein signalling network affects its emergent dynamics, with particular emphasis on drug-response signalling dynamics in cancer treatments. They named this approach Meta Dynamic Network (MDN) modelling, as it aims to consider the potential dynamic responses globally, varying both initial conditions (i.e., expression levels) and biophysical parameters (i.e., protein interaction parameters). By characterising the "meta" response of the network, the authors propose that the method can provide insights not only into the possible dynamic behaviours of the system of interest but also into the likelihood and frequency of observing these dynamic behaviours in the natural system.

The authors studied the Early Cell Cycle (ECC) network as a proof of concept, specifically focusing on PI3K, EGFR, and CDK4/6, with particular interest in identifying the mechanisms that cancer could potentially exploit to display drug resistance. The biochemical reaction model consists of 50 equations (state variables) with 94 kinetic parameters, described using SBML and computed in Matlab. Based on the simulations, the authors concluded the following main points: a large number of network states can facilitate resistance, the individual biophysical parameters alone are insufficient to predict resistance, and adaptive resistance is an emergent property of the network. Finally, the authors attempt to validate the model's prediction that differential core sub-networks can drive drug resistance by comparing their observations with the knock-out information available in the literature. The authors identified subnetworks potentially responsible for drug resistance through the inhibition of individual pathways. Importantly, some concerns regarding the methodology are discussed below, putting in doubt the validity of the main claims of this work.

While the authors proposed a potentially useful computational approach to better understand the effect of heterogeneity in a system's dynamic response to a drug treatment (i.e., a perturbation), there are important weaknesses in the manuscript in its current form:

(1) It is unclear how the random parameter sets (i.e., model instances) and initial conditions are generated, and how this choice biases or limits the general conclusions for the case studied. Particularly, it is not evident how the kinetic rates are related to any biological data, nor if the parameter distributions used in this study have any biological relevance.<br /> (2) Related to this problem, it is not clear whether the considered 100,000 random parameter samples sufficiently explore parameter space due to the combinatorial explosion that arises from having 94 free parameters, nor 100,000 random initial conditions for a system with 50 species (variables).<br /> (3) Moreover, the authors filter out all the cases with stiff behaviour. This filtering step appears to select model parameters based on computational convenience, rather than biological plausibility.<br /> (4) Also, it is not clear how exactly the drug effect is incorporated into the model (e.g., molecular inhibition?), nor how it is evaluated in the dynamic simulations (e.g., at the beginning of the simulation?). Moreover, in a complex network, the results may differ depending on whether the inhibition is applied from the start or after the network has reached a stable state.<br /> (5) On the same line, the conclusions need to be discussed in the context of stability, particularly when evaluating the role of initial conditions. As stable steady states are determined by the model parameters, once again, the details of how the perturbation effect is evaluated on the simulation dynamics are critical to interpret the results.<br /> (6) The presented validation of the model results (Fig. 7) is only qualitative, and the interpretation is not carefully discussed in the manuscript, particularly considering the comparison between fold-change responses without specifying the baseline states.

We thank the reviewers for their thoughtful and constructive comments. In response to their comments, we have undertaken a substantial revision to address all the comments, improve clarity, transparency, and robustness while preserving the paper’s core contribution: a principled, scalable framework (MDN) for mapping how molecular heterogeneity and network architecture shape adaptive drug-response dynamics. At a high level, we clarified the study design and analysis goals, tightened definitions, and added methodological detail where it most advances interpretability. Importantly, these updates leave the analytical pipelines and major conclusions unchanged.

Conceptually, we now make explicit that our objective is coverage of the output space of qualitative dynamics supported by the network topology, not exhaustive enumeration of parameter space. To support this, we added a convergence analysis and clarified that “triplicates” refers to independent ensembles used to demonstrate reproducibility. We also refined how we describe and implement initial conditions (as conserved total abundances that encode expression heterogeneity) and reframed filtering as minimal numerical/feasibility checks, using rejection sampling to obtain the prespecified ensemble size. Solver choices and input modelling (constant step mitogen/drug) are now spelled out succinctly.

We expanded the model specification and rationale (complete reaction list with rate laws and brief biological justifications in the Supplement) and unified terminology throughout. Figures and legends have been overhauled for readability and accuracy, with missing labels added and ordering corrected. For validation, we clarified the nature of the single-cell reporter readout, improved Figure 7’s presentation, and emphasised - consistent with our aims - that comparisons are qualitative.

Finally, we have rewritten the Discussion to centre on interpretation, implications, and connect our findings to the literature. It now: (i) frames MDN as a systems-level framework that links molecular heterogeneity to qualitative signalling “meta-dynamics” and adaptive escape under constant drug pressure; (ii) highlights two key findings: an asymmetry in control (interaction kinetics exert stronger, more consistent influence than protein abundance) and a topology-driven convergence whereby a vast parameter space funnels into a finite set of recurrent behaviours; (iii) shows that resistance is a network-level property, with many possible routes but a small set of recurrent hubs/modules dominating; and (iv) provides a qualitative alignment with single-cell reporter data while clarifying the intent and limits of that comparison. Moreover, we now explicitly discuss limitations (rate-law simplifications, broad priors, determinism, and modular abstractions) and outline next steps for future research, including data-constrained priors and stochastic extensions.

We believe these revisions materially strengthen the manuscript and fully address all the reviewers’ comments. A detailed, point-by-point response follows.

Joint Recommendations for the Authors:

(1) It is confusing exactly what are the different sets evaluated in each cases, e.g. "generated 100,000 model instances, each with the same set of ICs but a unique set of randomly generated parameter values" (lines 299-300), "generated 100,000 model instances (in triplicate), each with the same set of 'nominal' parameter values (see supplementary Table S1), and a unique set of ICs, and repeated the analysis as performed previously" (lines 366-368), "combined the 1000 IC sets with each parameter set to create 1000 model instances" (lines 382-383), "repeated for 1000 parameter sets, allowing us to observe how frequently IC variation induced adaptive resistance independent of the chosen parameter set" (lines 386-387). A small table or just a clearer explanation is needed.

In response to these comments, we have revised the main text to clarify the process of model instance generation. Specifically, we have made changes at page 7: line 297 - page 8: line 302, page 8: lines 305 - 310, page 9: lines 372-378, and page 9: line 384 – page 10: line 399 in the revised main text.

We have also added a new Figure (Figure S1) to the supplementary file to allow readers to visualise the model generation process for each relevant set of experiments. Supplementary figures are referenced in the main text where appropriate.

(2) The authors mentioned performing each simulation in triplicate, which is puzzling as the model is based on deterministic ODEs with fixed parameters for each simulation. Under such conditions, one would anticipate identical results from multiple simulations with the same initial conditions and fixed parameters. Perhaps the authors expect the model to exhibit chaos or aim to assess the precision of the parameter estimates through triplicate simulations. Further clarification from the authors would be valuable to comprehend the rationale behind conducting triplicate simulations in a deterministic setting.

We agree that repeating deterministic ODE simulations with identical inputs would be redundant. In our study, “triplicate” referred instead to generating three independent ensembles of 100,000 unique model instances each, where model parameters (or initial conditions) were randomly resampled. These ensembles were analysed separately to assess whether the inferred meta-dynamic distributions converged robustly. Indeed, the distributions from the three replicates were nearly indistinguishable, confirming that the results are reproducible and not artefacts of a particular random draw.

We have revised the main text to clarify this distinction (page 8: lines 305 - 310) and added an extended explanation for meta-dynamic behaviour convergence in the new section Error Convergence in the supplementary text (page 6: lines 184 - 210).

(3) While the lack of a connection between model parameters and biological data (mentioned in the public review) may not be a fatal flaw in the manuscript, the concern about the 100,000 random samples being insufficient to explore the parameter space is valid. In a thought experiment, considering the high and low rate for each parameter and the combinatorial explosion of possibilities (2^94), the number of simulations performed (100,000) represents only an extremely small fraction of the entire parameter space (~1/10^(23)). This limitation might not accurately capture the true heterogeneity present inside a solid tumour. One potential solution is to determine biological bounds on model parameters through data fitting, which can provide more meaningful constraints for the simulations. Alternatively, increasing the number of simulations and adopting more efficient sampling techniques can enhance the coverage of possible parameter sets.

We thank the reviewer for this insightful comment. We agree that the 94-dimensional parameter space is vast, and that 100,000 simulations represent only a fraction of the total combinatorial possibilities. However, the objective of our study is not to exhaustively sample the entire parameter space, but rather to sufficiently sample the ‘output space’ - that is, the complete spectrum of qualitative dynamic behaviours the network topology can generate. The key question is whether 100,000 model instances are sufficient for the distribution of these output dynamics to converge.

To formally address this, we have performed a convergence analysis, which is now detailed in the new supplementary section "Error Convergence" (Supplementary text page 6: lines 184 - 210) and illustrated in Supplementary Figure S12. This analysis demonstrates that the mean squared error (MSE) between dynamic distributions from N and 2N simulations exponentially decreases as N increases, and the distribution of protein dynamics changes negligibly well before reaching 100,000 instances. Furthermore, performing the entire analysis in triplicate with independent random seeds yielded nearly identical meta-dynamic maps (average standard deviation < 0.04%), giving us high confidence that we have robustly captured the network's behavioural repertoire.

We believe this convergence occurs because the system is degenerate: many distinct parameter sets within the high-dimensional space map to the same qualitative outcome (e.g., 'rebound' or 'decreasing'). Our goal was to capture the set of possible outcomes, not every unique parameter combination that leads to them.

Regarding the parameter range, we intentionally chose a broad, unbiased range (10^-5 to 10<sup4></sup>)as a proof-of-concept to delineate the theoretical upper limit of heterogeneity the network can support, thereby capturing even rare but potentially critical resistance dynamics. We agree with the reviewer that a future direction is to constrain these ranges using biological data. Such an approach would transition from defining what is possible (the focus of this manuscript) to predicting what is probable in a specific biological context. We have added this important point to the Discussion (page 16: lines 663-679) to highlight this avenue for future work.

(4) One of the manuscript's main results indicates that protein interactions play a more significant role in driving adaptive resistance than protein expression. To explore the impact of protein expression, the authors fixed a nominal parameter set and generated 100,000 initial concentrations of the 50 proteins in the ODE model. However, the simulations' equilibrium concentrations in the "starvation" and "fed" phases, which form the initial condition for the treated phase, are uniquely determined by the nominal model's kinetic parameters and not the initial conditions, which remain identical for each simulation. From a dynamical systems perspective, stable steady states are determined by the model parameters and attract all initial conditions within their basin of attraction. As a result, a random sampling of the initial conditions has a limited impact on the model dynamics. The authors' conclusion that "the ability of expression to induce resistance also seems to be dependent on the master parameter set" can be explained by this dynamical systems perspective, where the resistance state corresponds to a stable steady state determined by the master parameter set. Considering this, the evidence presented in the manuscript may not fully support the authors' conclusion regarding the importance of protein expressions relative to protein dynamics. The discrepancy might be attributed to a possible misunderstanding of this point, and further clarification from the authors could be helpful.

We thank the reviewer for the thoughtful perspective. We agree that, in a monostable system with fixed kinetic parameters and fixed conserved totals, varying only the initial split among moieties (e.g., X vs pX) will not change the final steady state; trajectories converge to the same attractor. In our analysis, however, “initial conditions” predominantly refer to total protein abundances (e.g., X_tot = X + pX + complexes), used as a proxy for expression heterogeneity. These totals are invariants on the simulated timescale (no synthesis/degradation in the pre-equilibration phases), and therefore alter the value of the steady state under a given parameter set. In other words, our IC sampling mostly varies conserved totals rather than merely redistributing a fixed total; hence the equilibrium reached after the starvation/fed pre-equilibrations depends on the sampled totals and the kinetics. This can be seen in the new Supplementary Figure S4, showing that changing the ICs does shift the eventual steady state even when kinetic parameters are fixed.

We have revised the text to: (1) define ICs explicitly as total abundances for multi-state species, (2) distinguish “initial split” from “conserved totals,” and (3) clarify that expression effects are context-dependent rather than universally dominant (page 4: lines 139-141 and page 10: lines 413-416)

(5) Additionally, it is important to note that the random sampling of 100,000 initial concentrations might not sufficiently explore the vast space of possible initial conditions. In the thought experiment mentioned earlier, where each protein can have high or low expression concentrations, there are approximately 2^(50) = ~10^(15) possible combinations of initial concentrations. Thus, the 100,000 random simulations only represent around ~1/10^(10) of the possible initial conditions in this simplistic scenario. Consequently, this limited sampling of initial conditions may not provide enough information to draw meaningful conclusions, even if the initial conditions were more directly linked to kinetic rates.

Please see our response to Comment (3). Briefly, our ICs are continuous total abundances (conserved moieties), not binary high/low states; many IC configurations converge to the same qualitative attractors, so we estimate distributional properties rather than enumerate all combinations. Our convergence diagnostics (independent replicates and sample-size doubling) show that the meta-dynamic distributions stabilise well before N=100,000 (see Supplementary Figure S12). We have clarified this in the Supplementary Information (Error Convergence section) with the new convergence results.

(6) The authors implement a parameter selection step in the manuscript, where they filter out parameter sets that lead to what they term non-biological simulations. However, the rationale for determining if a given parameter set results in a stiff system of ODEs remains unclear. The authors cite references [38,39] to support the claim that stiff equations are not biologically plausible. Still, upon review, it is evident that [38] does not include the term "stiff," and [39] discusses using implicit methods to simulate stiff ODE models without specifically commenting on the biological plausibility of stiff systems. The manuscript lacks direct evidence to justify the conclusion that filtering out parameter sets that result in stiff ODE systems is reasonable. Since the filtering step accounts for the majority of discarded parameter sets, a stronger foundation is required to support the statement that stiff equations are non-biological.

We thank the reviewer for pointing out the issue in our original justification. The reviewer is correct: stiff systems are a common feature of biological models, and our claim that they are likely ‘biologically implausible’ was not well substantiated. The filtering of these model instances was, in fact, due to a computational limitation rather than a biological principle. The issue was that these parameter sets produced systems of ODEs that were so numerically stiff they were unsolvable within a reasonable timeframe by the SUNDIALS ODE solver suite, which is specifically designed for such systems.

Following the reviewer's comment, we investigated the source of this prohibitive stiffness. We discovered it was not an intrinsic property of the parameter sets themselves, but rather an artifact of our simulation setup. The extreme stiffness occurred almost exclusively during the initial integration timesteps, caused by the large initial discrepancy between the concentrations of active and inactive protein forms. This large discrepancy created the conditions for overtly stiff solutions i.e. unsolvable with implemented ODE solve settings. To overcome this problem, we set a large maximum number of steps in the ODE solver for the first couple of time points, enabling the solver to overcome the excessively stiff portion of the solve. We found that the vast majority of the previously 'unsolvable' model instances could now be successfully simulated. Consequently, the number of parameter sets discarded due to solver failure is now negligible (< 1%), and this filtering step no longer accounts for the majority of discarded parameter sets. Most importantly, the distributions of dynamics were not significantly altered by this adaptation.

We have revised the " Sampling and filtering of model instances (page 5: lines 174 – 189)" part in the Methods section to reflect this more accurate understanding. We have corrected our original claim regarding the biological plausibility of stiff systems and corrected our use of the references. Ref [38] was included to demonstrate that models of biological systems are stiff, which was a major conclusion of that paper, and [39] was originally included to demonstrate that solving ODEs is reliant on solvers that can integrate stiff systems. Upon review, ref [39] has been removed.

Overall, this investigation has made our analysis more robust by allowing us to include a wider, more representative range of parameter sets, and has tangibly improved the quality of our study.

(7) Additionally, it is important to consider the standard method for accounting for stiff systems, as presented in [39], which involves using implicit numerical methods for ODE simulation. The authors mention using numerical methods from the SUNDIALS suite, which includes implicit methods, but the specific numerical method used remains unclear. Furthermore, it would be valuable for the authors to disclose the number of parameter sets that were filtered to obtain the final set of 100,000 accepted parameter sets. This information would provide insights into the extent of filtering and the proportion of parameter sets that were excluded during the selection process.

We apologise for the lack of specific detail and have now updated the text. To clarify, all ODE simulations were performed using the CVODE solver from the SUNDIALS suite. This solver employs an implicit, variable-order, variable-step Backward Differentiation Formula (BDF) method, which is robust and specifically designed for handling the stiff systems common in biological network modelling. We have now explicitly stated this in the "ODE model construction, modelling, and simulations (page 4: lines 162 – 164)" section of the Methods.

Regarding the filtered parameters, we have included a revised and detailed discussion of this in the "Sampling and filtering of model instances (page 5: lines 174 – 189)" part in the Methods section (see our response to comment (6) above). Briefly, after applying the filters, ~40–45% of instances did not reach steady state within the simulation timeframe, and ~50–55% did not meet the minimum drug-response criterion. Approximately 10% satisfied all criteria and were retained for analysis. Importantly, we employed ‘rejection sampling’ and continued drawing until we had N = 100,000 accepted instances that satisfied all the criteria.

(8) An important step in the simulation process described by the authors is the simulation of the "fasted" and "fed" states until an equilibrium is reached. However, it is not clear how the authors determine if the system has reached an equilibrium. It would be helpful if the authors could provide more information regarding the criteria used to assess equilibrium in the simulations. Regarding the "fed" state, it is not explicitly stated whether the mitogen stimulus is assumed to be constant throughout the "fed" experiment. Considering the dynamic nature of mitogen stimulation in biological systems, it would be beneficial if the authors could clarify this assumption and discuss its biological relevance.

We apologise for the lack not specifying this in the original text. A simulation was considered to have reached equilibrium when the concentration of every protein species changed by < 1% over the final 100 time steps of the simulation phase. We have now added this criterion to the "Sampling and filtering of model instances (page 5: lines 177 – 179)" part of the Methods section.

Regarding the second part of the comment, in our simulations, both the mitogenic and the drug inputs were modelled as constant, stepwise functions that, once turned on, remained at a fixed concentration for the remainder of the simulation. The biological rationale for this choice was to rigorously test for bona fide adaptive resistance. By maintaining a constant mitogenic and drug pressure, we can ensure that any observed recovery in the activity of downstream proteins is due to the internal rewiring and adaptation of the signalling network itself, rather than an artefact of the removal or decay of the external stimulus/drugs. We have now clarified this rationale in the "ODE model construction, modelling, and simulations (page 4: lines 168 – 171)" part of the Methods section.

(9) The "Description of Model Scope and Construction" section in the Supplementary Information should include explicitly the model reactions and some discussion about their specific form (e.g., why is '(((kc2f1*pIR*PI3K) / (1 + (pS6K/Ki2))) + (kc2f2*pFGFR*PI3K))' representing the phosphorylation rate of PI3K, with pS6K in the denominator?).

The reviewer is right to ask for model justification. We have expanded the Supplementary “Description of Model Scope and Construction” section (page 2: line 63 – page 5: line 185) to include a complete reaction list with rate laws and a brief rationale for each. We also explain the specific PI3K phosphorylation term: activation by pIR and pFGFR is attenuated by pS6K via a denominator, which captures the well-described S6K-mediated negative feedback that reduces activation (e.g., via IRS1 phosphorylation).

(10) In line 349, the statement "Given that CDK46cycD is only strongly suppressed in just under 60% of the model instances (Figure 3C)" lacks clarity regarding where to look to interpret the 60% value. If this means that 4 out of the 7 model instances are resistant, and the other 2 proteins also have the same percentage of resistance, then there is no apparent reason to focus solely on CDK46cycD.

The reviewer is correct; the figure reference was an error, which has been rectified in the main text (page 9: line 355). The actual figure reference was to Supplementary Figure 2A, which shows the heatmap of all the frequencies for each protein dynamics for all the active protein forms. CDK4/6cycD shows a sustained decreasing dynamic for 59.93% of model instances, which is where this number was derived. We have also now explicitly referenced this number in the supplementary Figure 2A legend.

We focus on CDK4/6cycD because it is the direct pharmacological target of CDK4/6 inhibitors. Our point was to suggest that even when the target is suppressed in the majority of instances (~60%), this does not reliably propagate to uniform downstream inhibition across the network, thus highlighting emergent, network-driven adaptive responses.

(11) We observed that in Fig. 5A, the authors show that multiple pathways are blocked. However, it is unclear whether they reduced the value of one parameter in the experiment or simulated multiple combinations of parameter inhibition. Considering the large number of parameters (94) in the model, if the authors simulated all possible combinations of parameter inhibition, the number of combinations would be significantly more than 94. An actual inhibitor typically has an inhibitory effect on multiple molecules. Therefore, it would be necessary to identify the parameters that lead to drug resistance when multiple molecules are inhibited. However, examining the inhibition patterns for all 94 parameters would be practically impossible. As a potential approach, we suggest using ensemble learning techniques, such as random forests, to handle this problem efficiently. With a dataset of binary outputs indicating the presence or absence of resistance for a sufficient number of inhibition patterns, ensemble learning can be applied to find the parameters that contribute to drug resistance. Popular feature selection algorithms like Boruta could be utilised to identify the most relevant parameters. The results obtained by ensemble learning are similar to the ranking in Fig. 5C, potentially providing a more robust validation of the authors' findings. By incorporating these additional analyses, the authors could strengthen the reliability and significance of their results related to parameter inhibition and drug resistance.

We appreciate the suggestion and the opportunity to clarify. Figure 5A depicts multiple pathways were interrogated, but in the analysis, parameters were inhibited one at a time (OAT) - not in combination. We have revised the figure legend and added a section named “Protein knockdown perturbation analyses (page 6: lines 228 – 233)” in the Methods section to make this explicit. Moreover, some additional text in the main text has been slightly modified to make this clearer (page 11: lines 462-463, page 24: lines 856-857).

We chose the OAT design intentionally to obtain causal, first-order attribution of control points across a broad parameter ensemble without confounding from simultaneous co-inhibition. This provides an interpretable ranking of primary drivers (Figure 5C) that is consistent with the paper’s mechanistic focus. We agree that a multi-target inhibition approach could be a useful next step; however, an exhaustive combinatorial screen is beyond the scope of this proof-of-concept. In such future studies, the ensemble learning, as suggested by the reviewer, could be layered onto our MDN framework to assess robustness of the ranking under co-inhibition.

(12) In explaining the parameterization of the model, we find an implication of a quantitative model. However, upon examining the results in Fig. 7D, we observe that they are only qualitatively correct. When comparing Figs. 7A and 7C, we note that many model instances are immediately suppressed, and the time scale remains unknown. We believe it would be essential for the authors to explain how the model of this study maintains its quantitative nature despite the results in Fig. 7. If such an explanation cannot be provided, it raises concerns regarding the biological reliability of several findings within this study.

While our framework is built on quantitative ODEs, the validation we present in Figure 7 is indeed qualitative. This is an intentional and key feature of our study's design. Our goal was not to build a calibrated, quantitative model of a specific cell line (e.g., MCF10A), but rather to establish a proof-of-concept theoretical framework that systematically explores the full spectrum of dynamic behaviours a given network topology can possibly generate. To achieve this, we intentionally sampled parameters from a very broad, unbiased range to delineate the theoretical upper limit of heterogeneity. This in silico population is therefore designed to be far more heterogeneous than any single isogenic cell line.

The striking qualitative agreement seen between our meta-dynamic distributions and the single-cell data in Figure 7D is thus not a failure of quantitative prediction, but rather a strong validation of our core premise: that a significant degree of signalling heterogeneity exists in cell populations and that our framework can effectively capture its emergent properties.

Regarding the specific comment on Figure 7C, we apologise for the lack of clarity. Nominally, we chose to simulate for 24 hours however, the x-axis in our simulations represents arbitrary time units, as the timescale is dependent on the meaning/units of the parameter values. The goal is to compare the qualitative shape of the response (e.g., rebound, sustained decrease), not the absolute time in hours. Moreover the rapid initial suppression seen in many of our model instances (Fig 7C) is a direct parallel to the rapid suppression seen in the experimental data (Fig 7A). This initial phase is followed by a wide variety of adaptive behaviours (or lack thereof) in both our simulations and the real cells, which is the key phenomenon we are studying.

We have revised the text (page 14: lines 598-601) and Figure 7’s legend to state more explicitly that our validation is qualitative and to clarify the purpose of our broad, uncalibrated approach. We have also added a note in the Discussion (page 18: lines 744-747) that calibrating this framework with cell-line-specific data is a natural next step for generating quantitative, context-specific predictions.

(13) Related to the previous point, the experimental data is presented as fold-change during CDK4/6 inhibition, and we notice that the initial fold-change at time 0 varies between 1 and 1.8. The difference in initial fold-change is unclear to us, as our understanding of fold-change typically corresponds to the change from baseline, typically represented by the protein concentration at time 0.

Furthermore, while the experimental data exhibits uniformly decreasing CDK4/6 activity, a substantial number of simulations indicate constant CDK4/6cycD, showing a significant qualitative discrepancy between the simulations and experimental findings. This disparity makes it difficult for us to interpret the comparison between the two datasets effectively, given the complexities in comprehending the experimental fold-change figure.

As Figure 7 serves as the primary validation of model simulations in the manuscript, we believe that the current presentation may not provide a compelling reason to believe that the model accurately captures experimental data. To enhance clarity and validation, we suggest overlaying the experimental data over the simulations or considering the median and 10/90% percentile of the experimental data, which may potentially offer improved readability and facilitate a more robust interpretation of the comparison.

The experimental data from Yang et al. (ref 55, main text) measures kinase activity using a nucleus-to-cytoplasm translocation reporter system, wherein a bait protein is phosphorylated by the target kinase causing it to translocate from the nucleus to the cytoplasm. Hence, the y-axis represents the ratio of nuclear vs. cytoplasmic fluorescence, not a fold-change from a t=0 baseline. The variation in the starting value (between 1 and 1.8) reflects the inherent heterogeneity in the reporter's localization across individual cells even before the drug is added. We have updated the y-axis label and revised Fig. 7’s legend to state this explicitly.

The most likely explanation for the discrepancy between experimental dynamics and our simulation dynamics is that the experimental data comes from an isogenic cell line that is largely sensitive to CDK4/6 inhibition. Our simulations are derived from a very wide parameter sweep, where the intent is to represent all possible cell states. It is quite striking that that there is such a high correlation between the experimental data and simulations, indicating that perhaps the heterogeneity of even isogenic cell lines is significantly greater than might be intuited; a point we now mention in the revised Discussion (page 17: lines 716-727).

It is worth noting again, that our analysis is intentionally constructed to be as heterogeneous as possible, and is not trained on any biological data that might otherwise constrain the output-behaviour space. The isogenic cell line almost certainly represents a much more constrained output-behaviour space than our analysis.

The y-axis label has also been updated accordingly. As mentioned in (12) this result is intended as a qualitative validation, showing that cell lines indeed have highly variable signalling dynamics. Given the range of parameters tested, we think it is surprising that the degree of agreement between the experiment and our analysis is as high as it is. Again, we believe this suggests that heterogeneity may be more prevalent than is intuited. We do not believe we have made any strong quantitative claims in the main text, and we certainly aim to work towards biological, quantitative validation in the future. Finally, we altered the wording of the results heading (page 14: line 562) to make it clear that we are only making qualitative claims and removed the claim that the evidence was strong.

With these clarifications and corrections, we believe the validation is now much more compelling. The key point is not a perfect quantitative match, but the strong similarity in the distribution of heterogeneous behaviours.

(14) The authors mention simulating treatment with 10nM of CDK4/6i or Ei, but specific details on how this treatment is included in the model simulations are not provided. This lack of information makes it challenging to fully evaluate the comparison between model simulations and experimental evidence in Figure 7. It would be highly appreciated if the authors could clarify how the treatment with CDK4/6i or Ei is incorporated into the simulations to facilitate a better understanding and interpretation of the results.

To clarify, the effects of the inhibitors were incorporated directly into the kinetic rate laws of their respective target reactions.

CDK4/6 inhibitor (CDK4/6i): This was modelled as an inhibitor of the formation of the active CDK4/6-cyclin D complex. We have now explicitly detailed this in the description for reaction R27 in the "Description of Model Scope and Construction" section of the Supplementary Information.

Estrogen Receptor inhibitor (Ei): This was modelled as an inhibitor of the estrogen-dependent activation of the Estrogen Receptor. This is now explicitly detailed in the description for reaction R15 in the same supplementary section.

It is however important to reiterate that our goal in Figure 7 is qualitative, shape-based comparison; therefore, we used a fixed fractional inhibition (reported in Methods) rather than a calibrated IC50/Hill model.

(15) The authors state strong support for their modelling conclusions based on the literature. However, we still have concerns regarding the validation of the model against CDK2 or CDK4/6 data in Figure 7, as it appears less convincing to us. Furthermore, the authors list known resistance mechanisms that are replicated in their modelling. Nevertheless, we find the conclusion somewhat weakened by Figure S10, where approximately 80% of the nodes are implicated in some form of resistance pathway. This raises questions about the model's selectivity, as many proteins included in the model seem to drive resistance in some manner. In the Supplementary Information, the authors mention excluding or abstracting some protein species from the mitogenic and cell cycle pathways to manage computational resources effectively. This abstraction makes it difficult to determine if the proteins identified as potential drivers of resistance genuinely drive resistance or might represent abstractions of other potential drivers. To enhance the manuscript's clarity and address potential concerns about the model's selectivity and abstraction, we suggest providing more details and discussion in the main text.

The reviewer's observation that a large number of nodes are implicated in resistance pathways in Figure S10 is correct. However, we argue this is not a weakness of the model's selectivity, but rather a key finding that reflects the biological reality of adaptive resistance. The literature is replete with a wide and growing number of distinct mechanisms of resistance even to a single class of drugs (1,2), which supports the idea that cancer can co-opt a wide variety of network nodes to survive.

Figure S10 is not a binary map where every implicated node is equal, instead it is a likelihood map, where the colour and weight of the connections represent how often a particular interaction participates in driving resistance across the theoretical full range of possible network dynamics. The figure shows that while many nodes can contribute to resistance, they do so in a hub-like manner i.e. small subsets of nodes coordinate to drive resistance. This provides a rationalised, data-driven prioritisation of the most dominant and recurrent resistance strategies. We draw two important conclusions from this work 1) Resistance likely occurs due to resistance hubs, not individual proteins, and 2) that the frequency of a resistance hub in an MDN analysis is likely proportional to the frequency of that hub emerging as a resistance mechanism in a population of cells and patients.

Regarding the issue of abstraction, the reviewer is correct that this is an inherent feature of any tractable systems model. In our case, several species in the mitogenic/cell-cycle pathways are module-level proxies to control model size. The highly implicated "hub" nodes in our model likely represent critical cellular processes that are themselves composed of several individual protein interactions.

To address these concerns, we have significantly revised the Discussion (page 16: lines 681 – 694) to: (1) frame resistance as a network-level phenomenon; (2) show that our frequency-based ranking is selective, prioritising the most probable, recurrent mechanisms; and (3) clarify that - given model abstraction -our findings implicate critical processes (modules), not just single proteins, as the drivers.

Overall, these changes do not alter our main conclusions: adaptive resistance is an emergent, network-level property; many routes exist, but a smaller set of nodes/modules consistently carry the largest influence across heterogeneous contexts.

(16) We consider that the figures and legends, including the supplementary information, are inadequately explained. The information provided is insufficient for us to comprehend the figures fully, leading to the need for interpretation on our part as readers. This could potentially introduce biases when trying to understand the claims made by the authors. To improve our understanding, it would be essential for the authors to assign appropriate labels to the figures and provide comprehensive explanations in the legends. For example, in Fig 3, we suggest labelling the tree diagrams in panels A and B, as well as the colour bars. We also recommend applying the same approach to other figures, adding accurate axis labels and descriptions of colour gradients to enhance clarity.

We thank the reviewer for this critical feedback. To address this comment, the figure legends have been revised where appropriate and greatly expanded to improve their comprehension. Moreover, we have added explicit labels to all previously unlabelled components, such as the cluster dendrograms and colour code bars in Figure 3A, B.

(17) To enhance readability, we recommend interchanging the order of Figures 1 and 2 in the sequence they appear in the main text. Alternatively, the text can be adjusted to refer to the figures in the correct order. Additionally, attention should be given to the bottom of Fig 1, which appears to be cropped or cut off. Furthermore, the incorrect word spacing in some figure elements, such as Fig. 3A title, Fig. 5B title, and Fig. 6B y-label, should be corrected for improved visual presentation.

Following the reviewer’s comment, the order of Figures 1 and 2 has been switched to reflect the order in which they are referred to in the main text. These Figures have been re-exported to fix unintentional word spacing errors.

(18) We recommend that the language used to refer to the initial conditions in the manuscript is clarified and homogenised. Currently, the authors use different terms such as "basal expression," "protein expression," "state variable values," or "initial conditions" to refer to them. This variation in terminology can be confusing for readers. In particular, the use of "basal expression" is problematic, as it typically refers to the leaky value of a reaction in the absence of an inducer, making it another biophysical parameter of the system rather than an initial condition. To enhance clarity and consistency, we suggest the authors decide on a single term to refer to the initial conditions throughout the manuscript and provide a clear explanation of its meaning to avoid any confusion. This will help readers better understand the concept being discussed and prevent any potential misinterpretations.

We thank the reviewer for this very helpful suggestion. To resolve this and improve clarity, we have homogenized the language throughout the manuscript. We now clarify the use the following 3 terms in their specific contexts:

We use “protein abundances” exclusively for the conserved total abundances of multi-state species (e.g., Xtot = X + pX + complexes) that are sampled across instances to represent expression heterogeneity.

We use ‘initial conditions’ to refer to initial values of the state variables in a model simulation. This term is related to protein abundance as the setting of initial conditions for conserved species sets the protein abundance. This is explicitly stated in the text (page 3: lines 87 - 91).

We use “state variables” to refer to the time-dependent model species.

We avoid the term “basal expression” in technical descriptions. Where a biology-facing phrase is helpful, we use “protein expression level”. This is used when referring to the biological concept that the initial conditions are intended to represent, i.e. the heterogeneity in protein amounts across a cell population.

We have performed a thorough search-and-replace to ensure this new convention is applied consistently and have removed the potentially confusing term "basal expression" from the revised manuscript.

(19) Why are saturable functions (e.g., Michaelis-Menten functions) ignored in the model? What are the potential consequences?

The main objective of this work was to perform a large-scale, systematic exploration of a high-dimensional parameter space (94 parameters) to map the full repertoire of qualitative dynamic behaviours a network topology can support. Using saturable functions like Michaelis-Menten kinetics would have roughly doubled the number of parameters to be explored (from k to Vmax and Km for each enzymatic reaction), making a parameter sweep of this scale computationally intractable. We therefore prioritised the breadth of the parameter search over the depth of kinetic detail, which we believe is the appropriate choice for a proof-of-concept study focused on heterogeneity.

This simplification has potential consequences. A major one is that our model cannot capture phenomena that arise specifically from enzyme saturation, such as zero-order kinetics or certain forms of ultrasensitivity (switch-like responses). However, we argue that this is an acceptable trade-off for two main reasons: (1) Our analysis is based on classifying broad, qualitative response shapes (increasing, decreasing, rebound, etc.). Mass-action kinetics are fully capable of generating this rich spectrum of behaviours; and (2) by varying the mass-action rate constants over nine orders of magnitude (from 10^-5 to 10<sup4></sup>), our parameter sweep effectively samples a vast range of reaction efficiencies. A very low rate-constant can approximate the behaviour of a saturated, low-efficiency enzyme, while a high rate-constant can approximate a highly efficient, non-saturated one. In this way, the broad sweep of the rate parameter partially reflects the effects that would be captured by varying Vmax and Km.

For transparency, we have added a brief rationale to the “ODE model construction, modelling, and simulations” part of the Methods (revised main text, page 4: lines 153-155) and the "Description of Model Scope and Construction" section in the Supplementary file (Supplementary text page 2: lines 63-73).

(20) Given the relevance of the concept of "heterogeneity" in this work, a short discussion about biochemical noise and its implications on the analysis (e.g., why it is not included, and if it will be a next step) would be appreciated.

Our MDN modelling framework represents heterogeneity by creating an ensemble of deterministic models, where each model instance has a unique set of kinetic parameters and/or initial protein abundances. We propose that this is a powerful way to mechanistically represent the functional consequences of all sources of cellular variation. Over time, the effects of genetic mutations, epigenetic states, and even the time-averaged impact of intrinsic biochemical noise will manifest as changes in the effective interaction strengths and protein concentrations within a cell. Our large-scale parameter/IC sweep is designed to systematically explore the full range of dynamic behaviours that can emerge from this underlying biological variation. Therefore, our approach does not compete with stochastic modelling but is complementary to it. While stochastic simulations can capture the dynamic trajectories of single cells, our framework provides a panoramic view of the entire spectrum of possible stable phenotypes that can emerge at the population level. We agree that modelling intrinsic biochemical noise (stochasticity arising from finite copy numbers), e.g. using chemical Langevin or SSA, is a possible extension in future work but expected to be very computationally expensive. We have added a brief discussion on this as future direction in the revised Discussion.

(21) We have noticed that the first four paragraphs of the Discussion section overlap with the Introduction, as they mainly reiterate the significance of the study itself rather than focusing on the specific results obtained. To avoid redundancy and provide a more cohesive and informative discussion, we recommend that the authors shift the focus of the Discussion section towards presenting potential interpretations, even if they are not definitive, of the results obtained. By doing so, the Discussion will serve as a valuable platform for deeper analysis and insightful observations, allowing readers to better comprehend the implications and significance of the research findings.

We thank the reviewer for this structural feedback. Following the reviewer's feedback, we have significantly rewritten and restructured the Discussion section. The redundant introductory material has been removed.

The rewritten Discussion centres on interpretation, implications, and connect our findings to the literature. It now: (i) frames MDN as a systems-level framework that links molecular heterogeneity to qualitative signalling “meta-dynamics” and adaptive escape under constant drug pressure; (ii) highlights two key findings: an asymmetry in control (interaction kinetics exert stronger, more consistent influence than protein abundance) and a topology-driven convergence whereby a vast parameter space funnels into a finite set of recurrent behaviours; (iii) shows that resistance is a network-level property, with many possible routes but a small set of recurrent hubs/modules dominating; and (iv) provides a qualitative alignment with single-cell reporter data while clarifying the intent and limits of that comparison. Moreover, we now explicitly discuss limitations (rate-law simplifications, broad priors, determinism, and modular abstractions) and outline next steps for future research, including data-constrained priors and stochastic extensions.

We believe this substantial revision has transformed the Discussion into a much more insightful and valuable part of the manuscript that directly addresses the reviewer's concerns.

(22) The supplemental text file containing the model equations can be a bit challenging to read and understand. It would be greatly beneficial if the authors could consider generating a file using a typesetting program.

We have now included a typeset list of state variable equations and ODEs, along with the original model files.

(23) The authors mentioned that some model parameterizations result in negative solutions, which is surprising. Access to the model equations would help understand why this happens and is crucial for researchers who may want to use this approach. Clarifying the model equations' presentation would enhance transparency and aid other researchers in applying this method for similar research questions.ach. Clarifying the model equations' presentation would enhance transparency and aid other researchers in applying this method for similar research questions.

The reviewer is correct to be surprised by the mention of negative solutions, as negative concentrations are physically impossible. We clarify that these are not a result of any structural flaw in our model's equations but are a well-known, although rare, numerical artifact of floating-point arithmetic in computational solvers.

Our model is constructed using standard mass-action and first-order kinetics, which structurally guarantee non-negativity. However, when a species' concentration approaches the limits of machine precision (i.e., becomes a very small number extremely close to zero), the ODE solver can, in rare instances, numerically undershoot zero, resulting in a small negative value. If this occurs, it can lead to instability in subsequent integration steps.

This is not a biological phenomenon but a computational one. Therefore, the standard and appropriate procedure, which we follow, is to implement a filter that discards any simulation trajectory where such a numerical instability occurs.

(24) The reference listed for the CDK4/6 and CDK2 measurements is Yang et al. [55] in the figure caption, but as Xe et al. in lines 559-561 of the manuscript.

The text has been updated to match citation.

(25) We suggest that the authors revise and cite a previous study conducted by Yamada et al. (Scientific Reports, 2018), which presents an approach to expressing cell heterogeneity as a probability distribution of model parameters.

Following this suggestion, we have revised the Discussion (see response to comment (21)) to include and discuss Yamada et al. (Scientific Reports, 2018), which models cell heterogeneity as a probability distribution over parameter values.

(26) In the manuscript, on line 677, the authors state, "This indicates that there is an upper limit to the degree to which parameter sets can influence the qualitative shape of a protein's dynamic within a given network topology." We wish to highlight that this finding may not be particularly surprising. Given that the parameters were randomly determined within a specific range, it is understandable that altering the number of parameter samples would not substantially impact the distribution of model instances.

We thank the reviewer for this insightful comment, which allows us to clarify the significance of this finding. While it is true that any sampling from a fixed distribution will eventually converge statistically, our conclusion is not about statistics but about the intrinsic, constraining properties of the network's topology. The novelty is not that the distribution converges, but that it converges to a surprisingly limited and finite repertoire of qualitative dynamic behaviours. A complex, non-linear network with nearly 100 free parameters could theoretically generate an almost endless variety of complex dynamics. Our finding is that this specific biological topology acts as a powerful filter, robustly channelling the vast majority of the near-infinite parameter combinations into a small, recurring set of functional outputs (increasing, decreasing, rebound, etc.).

The reason for this finite limit is mechanistic, as the reviewer's comment prompted us to investigate further. Our parameter sweep already covers an extremely wide, 9-order-of-magnitude range. As we pushed parameter values to even greater extremes in exploratory simulations, we found they do not generate novel, complex dynamic shapes. Instead, they tend to drive network nodes into saturated states- either permanently "on" (maximally activated) or permanently "off" (minimally activated). In both cases, the node becomes unresponsive to upstream perturbations.

Therefore, further expanding the parameter range would be unlikely to uncover new behavioural categories; it would simply increase the proportion of model instances classified as "no-response." This demonstrates a fundamental principle: the network topology itself enforces an upper limit on its dynamic complexity. We think this inherent robustness is what allows for reliable cellular signalling in the face of constant biological variation. We believe this is a non-trivial finding, and we have revised the Discussion (page 16: lines 664 - 680) to state this conclusion and its implications more clearly.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Xiong and colleagues presents a compelling validation of UniDesign, a fully computational protein design framework, by using it to engineer a novel, PAM-relaxed variant of Staphylococcus aureus Cas9 (SaCas9) named KRH. The core achievement is the successful de novo generation of a high-performance nuclease (E782K/N968R/R1015H) solely through in silico modeling, without any subsequent experimental optimization or directed evolution. The authors demonstrate that KRH expands the SaCas9 PAM specificity from NNGRRT to NNNRRT, achieving genome editing and base editing efficiencies across multiple human cell types that are comparable to, and sometimes exceed, the well-known evolution-derived KKH variant. The work positions UniDesign not merely as an analytical tool, but as a powerful engine for the generative design of complex molecular functions, offering a scalable and mechanistically insightful alternative to traditional experimental screening.

Strengths:

This is an outstanding manuscript that serves as a powerful proof-of-concept for the next generation of computational protein design. The primary selling point-the raw predictive and generative power of UniDesign-is convincingly demonstrated throughout.

The manuscript shows that the tool can:

(1) successfully navigate a complex sequence landscape to identify a minimal set of three mutations (KRH) that remodel a critical protein-DNA interface;

(2) accurately model and balance the delicate interplay between specific base contacts and non-specific backbone interactions to achieve relaxed PAM specificity;

(3) deliver a final product whose performance is indistinguishable from, and in some cases superior to, a variant that required extensive wet-lab evolution.

The experimental validation is rigorous, thorough, and directly supports the computational predictions. This work will stand as a landmark study for the field, illustrating that computational design has matured to the point where it can reliably generate sophisticated tools for genome engineering.

(1) Demonstration of Generative Power:

The most significant finding is that UniDesign, without any experimental feedback, generated a variant (KRH) that matches the performance of the evolution-derived KKH. This is a remarkable achievement. The iterative design strategy-first reducing PAM bias (R1015H), then restoring binding through non-specific interactions (e.g., N968R, E782K)-is a textbook example of rational design, but it is executed entirely by the algorithm. This validates UniDesign's energy function and search algorithm as capable of capturing the subtle biophysical principles governing PAM recognition.

(2) Mechanistic Insight as a Built-in Feature:

A key advantage of UniDesign highlighted by this work is its inherent ability to provide mechanistic explanations. The computational models not only predicted which mutations would work (e.g., N968R over N968K in the KRH variant) but also why they work. The structural and energetic analyses showing the bidentate salt bridge formed by Arg968 versus the single bond formed by Lys968 (Figure 4A) is a perfect example of how the tool's output can rationalize functional differences, a level of insight that is rarely attainable from directed evolution campaigns alone.

(3) Scalability and Accessibility for Engineering:

The authors explicitly contrast UniDesign's efficiency (minutes to hours per design run) with the computational expense of methods like COMET and the experimental overhead of directed evolution. The improvements to UniDesign v1.2, specifically the mutation-count and sequence-uniqueness penalties, directly address a key challenge in computational design (generating diverse, low-energy point-mutant libraries). This positions the tool as a highly accessible and scalable platform for engineering other CRISPR systems, a point that will be of immense interest to the community.

We sincerely thank the reviewer for the comprehensive summary and the highly positive and encouraging comments on our manuscript.

Weaknesses:

(1) Title and Abstract Emphasis:

The title and abstract are effective but could be slightly sharpened to emphasize the primary message. Consider a title like "Fully computational design of a PAM-relaxed SaCas9 variant with UniDesign demonstrates power to match directed evolution." The abstract could more explicitly state upfront that the design was achieved without any experimental iteration.

Thank you for this valuable suggestion. We have revised the title and abstract accordingly to better reflect your feedback.

(2) Figure 1, Panel M:

The data points in panel M are currently presented at a font size that makes them difficult to read, particularly the labels for the many triple-mutant variants. This density obscures the clear identification of the top-performing designs, such as the KRH variant selected for experimental validation. I recommend that the authors increase the font size of all text elements within this panel, including axis labels, tick marks, and data point labels, to improve legibility. If necessary, the panel dimensions can be adjusted or the layout reorganized to accommodate the larger text without compromising clarity. Ensuring this figure is readable is important, as it visually communicates the energetic convergence that led to the selection of KRH.

Thank you for this helpful suggestion. We have increased the font size the Figure 1M, as well as in Figure 1C and Figure 1E, to improve the readability in the revised manuscript.

(3) Generality of the Design Strategy for Other PAM Positions:

The design strategy focused on relaxing specificity at the highly constrained third position of the PAM (the guanine in NNGRRT). How transferable is this specific strategy (i.e., disrupting a key specific contact and compensating with non-specific backbone binders) to relaxing other positions in the PAM or to other Cas enzymes with different PAM-interaction architectures? A short discussion on this point would help readers understand the broader applicability of the "fine-tuning the balance" principle.

Thank you for this insightful question and suggestion. The current study builds upon our previous work on CRISPR–Cas PAM recognition modeling using UniDesign (PMID: 37078688), in which eight Cas9 proteins and two Cas12 proteins (each has a different PAM) were investigated. Our computational results demonstrated that UniDesign can effectively capture the mutual preferences between natural PAMs and native PAM-interacting amino acids (PIAAs). For example, UniDesign accurately predicted the canonical PAMs of SpCas9 and SaCas9 as NGG and NNGRRT, respectively; conversely, given their canonical PAMs, UniDesign successfully recapitulated the corresponding PIAAs in both systems.

These findings provide the foundation for the present study and motivate our selection of SaCas9 as a representative system to explore PAM relaxation, thereby further demonstrating UniDesign’s predictive power through experimental validation. Although we did not perform similar PAM relaxation designs for other Cas9 or Cas12 proteins, we believe that the UniDesign framework is broadly generalizable and can be readily extended to these systems. We have included additional discussion to clarify this point and highlight the broader applicability of our design strategy.

Reviewer #2 (Public review):

Summary:

This manuscript describes the fully in silico design of a new variant of Staphylococcus aureus Cas9 (SaCas9) using an improved UniDesign workflow.

The design strategy consists of three sequential steps:

(1) reducing positional bias at PAM position 3;

(2) restoring DNA binding through nonspecific interactions;

(3) combining individually favorable substitutions.

The overall pipeline is conceptually elegant and logically structured, and the genome-editing activity of the designed variants is comprehensively characterized. The resulting KRH variant exhibits relaxed PAM specificity, expanding the targeting range of SaCas9 across diverse cell types. Notably, the KRH variant demonstrates performance comparable to that of the evolution-derived KKH variant, underscoring the effectiveness of the proposed computational design framework.

Strengths:

The design pipeline is entirely computational and does not rely on experimental data for pretraining or iterative optimization.

We thank the reviewer for the concise and accurate summary of our manuscript.

Weaknesses:

The computationally generated KRH mutant differs from the experimentally evolved KKH variant by only a single residue, which may reflect insufficient exploration of the available sequence space.

Thank you for this insightful critique. In the present study, our strategy was not to allow UniDesign to freely explore all 27 mutable positions simultaneously, but rather to constrain the search to point mutations (e.g., double or triple mutants) within the full sequence space (approximately 20²⁷). Even with this constraint, UniDesign effectively samples a substantially large design space compared to traditional protein engineering approaches.

Through iterative design, we observed that only certain residue types became enriched at a subset of positions when identifying effective double mutants. These enriched residues were then systematically combined to generate performance-enhancing triple mutants in an automated manner. Although we ultimately selected the KRH mutant for experimental validation due to its high similarity to the known KKH variant, UniDesign also proposed additional multi-mutants that are distinct from KKH (see Figure 1M).

Reviewer #3 (Public review):

Summary:

This study reports KRH, a SaCas9 variant computationally engineered via UniDesign to recognize an expanded NNNRRT PAM with substantially enhanced editing efficiency at non-canonical sites. KRH achieves genome- and base-editing efficiencies comparable to or exceeding the evolution-derived KKH variant across multiple human cell types, demonstrating that computational design can effectively remodel PAM specificity while preserving nuclease activity.

Strengths:

The research follows a clear line of reasoning, and the results appear sound. The computational design strategy presented offers a valuable alternative to directed evolution, with potential applicability beyond Cas9 engineering.

We thank the reviewer for the concise and accurate summary of our manuscript.

Weaknesses:

The benchmarking of the UniDesign method is insufficient. How its performance compares to other protein design algorithms, whether the energy function parameters were systematically optimized, and if the design strategy can be generalized to other Cas9 orthologs or genome engineering tasks.

Thank you for this valuable critique. The present study builds upon our previous work on CRISPR–Cas PAM recognition modeling using UniDesign (PMID: 37078688), in which many of these concerns were systematically addressed. In that study, UniDesign was benchmarked against Rosetta, a well-established protein design platform, across eight Cas9 proteins and two Cas12 proteins, each recognizing distinct PAM sequences.

Our results demonstrated that UniDesign effectively captures the mutual preferences between natural PAMs and native PAM-interacting amino acids (PIAAs) across these CRISPR–Cas systems. For example, UniDesign accurately predicted the canonical PAMs of SpCas9 and SaCas9 as NGG and NNGRRT, respectively; conversely, given their canonical PAMs, UniDesign successfully recapitulated the corresponding PIAAs in both systems.

These findings provide the foundation for the present study and motivate our selection of SaCas9 as a representative system to explore PAM relaxation, thereby further demonstrating UniDesign’s predictive power through experimental validation. Although we did not perform analogous PAM relaxation designs for other Cas9 or Cas12 proteins in this work, we believe that the UniDesign framework is broadly generalizable and can be readily extended to these systems. We have incorporated additional discussion in the revised manuscript to address these points and clarify the broader applicability of our approach.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) SaCas9 is highlighted for its AAV compatibility, but the manuscript does not further discuss how the KRH variant may benefit AAV-based genome editing applications. A brief discussion on how expanded PAM compatibility could facilitate target selection in AAV-constrained therapeutic settings would strengthen the translational relevance of the work, potentially reducing the need for split-Cas9 or dual-vector strategies.

Thank you for your helpful suggestion. We have added a brief discussion in the revised manuscript highlighting how the KRH variant’s expanded PAM compatibility may enhance AAV-based genome editing applications. Specifically, this property can broaden the range of targetable genomic sites and may reduce the need for split-Cas9 or dual-vector delivery strategies in size-constrained AAV therapeutic contexts.

(2) The study shows that a fully computational workflow can recapitulate the performance of an evolution-derived variant. A short discussion comparing the scalability and practical advantages of computational design versus directed evolution for future PAM engineering would help emphasize the broader methodological significance of UniDesign.

Thank you for your valuable suggestion. We have added a brief discussion in the revised manuscript comparing the scalability and practical advantages of computational design with directed evolution for PAM engineering. Specifically, we highlight that UniDesign enables rapid and scalable exploration of sequence space without requiring iterative experimental screening, thereby offering a complementary—and in some cases more efficient—approach to directed evolution for future protein engineering applications.

(3) The noticeable variation in editing efficiency across cell types, particularly the lower activity in A549 cells. Could the authors explain why the differences in editing efficiency are so large?

Thank you for this insightful comment. We agree that the variation in editing efficiency across cell types—particularly the lower activity observed in A549 cells—warrants clarification, and we have added a corresponding discussion in the revised manuscript. We attribute this observation to two main factors. First, transfection efficiency varies substantially across cell lines; in our experiments, A549 cells exhibited lower transfection efficiency compared to HEK293T, HeLa, and U2OS cells, which likely contributes to the reduced editing efficiency. Second, the intrinsic performance of genome editing systems can differ across cellular contexts due to variations in DNA repair pathways, including chromatin accessibility and the expression levels of key repair-related genes. Importantly, despite this cell-type-dependent variability in absolute editing efficiency, the KRH variant consistently outperformed wild-type SaCas9 across all tested cell lines, underscoring the robustness and general applicability of our design.

(4) Given that the computationally generated KRH mutant differs from the experimentally evolved KKH variant by only a single residue, it would be valuable to discuss whether R968 (or saturation mutations at this site) has previously been explored experimentally, and to elaborate on strategies for further expanding the diversity of mutations identified through the computational design framework.

Thank you for your suggestion. We have added a brief discussion in the manuscript noting that, to the best of our knowledge, R968 has not been experimentally characterized prior to this study. It was identified solely through our computational design workflow, highlighting the strength of our approach.

Reviewer #3 (Recommendations for the authors):

(1) During the protein amino acid conformational sampling process in UniDesign, were nucleic acid conformational changes taken into consideration?

Thank you for this question. Nucleic acid conformational changes were not explicitly considered during the protein sequence design stage in UniDesign after the four specific PAM variants (e.g., TTAGGT, TTCGGT, TTGGGT, and TTTGGT) were defined. We consider this assumption reasonable, as the base conformations in these PAM sequences are expected to remain largely stable, with minimal structural variation due to preserved base-stacking interactions.

(2) The authors used a mutation-count penalty to control the number of mutations generated during the design process, which appears to occasionally yield results that exceed the intended limit. Is this an efficient approach? Could the count be controlled more directly by imposing constraints within the design procedure itself?

Thank you for these insightful questions. You are correct that the design process may occasionally yield variants exceeding the intended mutation limit. This occurs because the mutation-count penalty is implemented as a soft constraint, where violations incur a penalty rather than being strictly excluded. Based on our benchmarking, this strategy—combined with the duplicate-design penalty—has been effective in generating multimutant variants with mutation counts close to the desired range. However, we acknowledge that this approach may not achieve optimal efficiency. We are currently developing improved strategies in UniDesign to more directly control mutation counts by incorporating explicit constraints during the sequence simulation process, which we expect will further enhance design precision and efficiency.

(3) Is the new version of UniDesign developed specifically for the Cas9 design task in this study? What are its advantages and disadvantages compared to other state-of-the-art protein design algorithms?

Thank you for this important question. The new version of UniDesign (v1.2) was not developed specifically for Cas9 engineering. Rather, it is intended as a general framework for protein engineering tasks that focus on introducing point mutations to improve protein properties, as opposed to de novo design. Compared to current state-of-the-art protein design methods—many of which are deep learning–based—UniDesign offers distinct advantages and limitations. Deep learning approaches are often highly efficient and powerful but may lack interpretability in their predictions. In contrast, UniDesign is a well-benchmarked, lightweight, physics-based method that provides greater interpretability, allowing users to better understand the underlying basis of the design decisions. On the other hand, a limitation of UniDesign is that it is less straightforward to incorporate experimental feedback for iterative refinement, such as fine-tuning the scoring function for specific design tasks.

(4) The study employed a three-round design process to obtain the mutants. Is there a conformational correlation between the mutation sites identified in these three rounds? Could this have been accomplished in a single computational run instead of three separate calculations?

Thank you for these insightful questions. We adopted a multi-round design strategy for SaCas9 PAM relaxation because this task inherently involves multi-objective optimization: enhancing PAM compatibility—particularly relaxing base recognition at the third PAM position—while preserving editing activity comparable to wild-type SaCas9. In our view, identifying the key mutations (e.g., E782K, N968R, and R1015H) in a single UniDesign run would be highly challenging due to competing energetic requirements. In the first round, R1015H emerged from single-site mutational scanning as the most favorable PAM-relaxing mutation based on its minimal MAD score. However, this mutation also significantly increased the binding energy relative to wild-type SaCas9 with its native PAM, suggesting a likely reduction in editing activity due to weakened binding. To address this, the second round focused on compensatory mutations. Variants such as E782K and N968R (along with several additional candidates) were identified in the context of R1015H to reduce binding energy and partially restore affinity. In the third round, we further combined compatible mutations from the second round, resulting in variants that more effectively lowered binding energy and restored it to levels comparable to wild-type SaCas9 with its native PAM. Notably, the design objectives in rounds one and two drive binding energy in opposite directions, making it unlikely that all key mutations could be identified simultaneously in a single run. During the design process, we also observed conformational correlations among mutation sites. For example, R1015H can form hydrogen-bonding interactions with residue E993, and we observed multiple alternative mutations at position 993 (e.g., E993S, E993P, E993A, E993G, E993K, and E993R), suggesting local structural coupling between these positions.

(5) In Figure 4D, for the FANCF-1 site, there appears to be a noticeable difference in editing efficiency between KKH-ABE and KRH-ABE. Is this difference statistically significant? If so, please provide an explanation for this observation.

Thank you for this question. For the FANCF-1 site shown in Figure 4D, we performed statistical analyses and found that the differences in editing efficiency between KKH-ABE and KRH-ABE are not statistically significant: P(A4) = 0.1239, P(A10) = 0.0671, P(A12) = 0.0942, and P(A13) = 0.1349 (two-tailed unpaired Student’s t-test). These results indicate that KRH-ABE and KKH-ABE exhibit comparable editing efficiencies at this site, supporting our overall conclusion that the computationally designed KRH variant achieves performance on par with the KKH variant.

(6) Does the evolutionary term within the UniDesign scoring function bias the designed sequences towards pre-existing protein features?

Thank you for this question. In this study, as well as in our previous work on Cas9 PAM recognition modeling (PMID: 37078688), the evolutionary term in the UniDesign scoring function was completely disabled. Therefore, it does not introduce any bias toward pre-existing protein features in the designed sequences.

Author response:

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

We thank the editor and reviewers for their thoughtful and constructive feedback. We appreciate that all reviewers recognized the value of our study in linking adult neurogenesis and synaptic plasticity to representational drift in the olfactory system. They described the model as elegant and well-motivated, and agreed that it provides new theoretical insight into how stability and adaptability can coexist in sensory representations. The reviewers also identified areas where our manuscript could be strengthened, and as outlined in our revision plan we have:

(1) Refined our description of mitral/tufted cell stability and expand on within-session and across-day variability.

(2) Substantially expanded the Discussion to compare our modeling assumptions with experimental findings and recent anatomical evidence. Additionally, we have included the limitations of the study and areas for future investigation.

(3) Included a clearer description of the STDP implementation, plastic synapses, and their functional effects.

(4) Add a short section outlining model-based predictions that can guide future experiments. We also made minor textual edits to improve precision and flow, including citing prior conceptual work and clarifying model procedures.

These changes have strengthened both the conceptual framing and technical clarity of the paper. We are grateful for the reviewers’ careful reading and valuable suggestions.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors build a network model of the olfactory bulb and the piriform cortex and use it to run simulations and test their hypotheses. Given the model's settings, the authors observe drift across days in the responses to the same odors of both the mitral/tufted cells, as well as of piriform cortex neurons. When representing the M/T and PCx responses within a lower-dimensional space, the apparent drift is more prominent in the PCx, while the M/T responses appear in comparison more stable. The authors further note that introducing spike-time dependent plasticity (STDP) at bulb synapses involving abGCs slows down the drift in the PCx representations, and further link this to the observation that repeated exposure to the same odorant slows down drift in the piriform cortex.

The model is clearly explained and relies on several assumptions and observations:

(1) Random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity, and random piriform to bulb connectivity.

(2) Higher dimensionality of piriform cortex representations compared to M/T responses, which enables superior decoding of odor identity in the piriform cortex.

(3) Spike time-dependent plasticity (STDP) at synapses involving the abGCs.

The authors address an open topical problem, and the model is elegant in its simplicity. I have however, several major concerns with the hypotheses underlying the model and with its biological plausibility.

Concerns:

(1) In their model, the authors propose that MTC remain stable at the population level, despite changes in individual MTC responses.

The authors cite several experimental studies to support their claims that individual MTC responses to the same odors change (some increase, some decrease) across days. Interpreting the results of these studies must, however, take into account the variability of M/T responses across odor presentation repeats within the same session vs. across sessions. In the Shani-Narkiss et al., Frontiers in Neural Circuits, 2023 study referenced, a large fraction of the variability across days in M/T responses is also observed across repeats to the same odorant in the same session (Shani-Narkiss et al., Figure 4), while the authors have M/T responses in the same session that are highly reproducible. This is an important point to consider and address, since it constrains how much of the variability in M/T responses can be attributed to adult neurogenesis in the olfactory bulb versus to other networks' inhibitory mechanisms, which do not rely on neurogenesis. In the authors' model, the variability in M/T responses observed across days emerges as a result of adult-born neurogenesis, which does not need to be the main source of variability observed in imaging experiments (Shani-Narkiss et al., Figure 4).

We agree with the reviewer and believe this is a critical discussion point. Indeed, both in Shani-Narkiss et al, Kay and Laurent, 1999, and in our lab, we observe trial-to-trial variability that occurs in the same recording session; as the reviewer correctly points out, this cannot be due to neurogenesis. These fluctuations may be trial to-trial noise, or reflect dynamics associated with other behaviors such as running (Chockanathan, et al. 2021) and decision making (Kay and Laurent, 1999). There is growing repertoire of literature showing that neural variability in early sensory coding appears to depend on behavioral fluctuations and internal states (Niell and Stryker for example). This variability that happens within a session in the Shani-Narkiss et al work may reflect some of these behaviorally relevant features of early olfactory coding, something that our model cannot account for. This is an excellent discussion point and we have included text (line 153-157, and line 321-330) in the manuscript to note this aspect of the data and how one can think of it in the context of our results.

Another study (Kato et al., Neuron, 2012, Figure 4) reported that mitral cell responses to odors experienced repeatedly across 7 days tend to sparsen and decrease in amplitude systematically, while mitral cell responses to the same odor on day 1 vs. day 7 when the odor is not presented repeatedly in between seem less affected (although the authors also reported a decrease in the CI for this condition). As such, Kato et al. mostly report decreases in mitral cell odor responses with repeated odor exposure at both the individual and population level, and not so much increases and decreases in the individual mitral cell responses, and stability at the population level.

Thank you for raising this important point regarding the findings of Kato et al. (2012). We agree that their results suggest increased sparsening and stability in M/T cell odor responses with repeated exposure. However, as noted in Yamada et al. (2017), the experimental literature on this question remains mixed. Yamada and colleagues reported a “drastic reorganization of ensemble odor representation” across days and emphasized that “sensory experience does not necessarily cause a major sparsening of the odor response,” explicitly contrasting their findings with those of Kato et al. (2012).

Our model captures the dynamics observed in Yamada et al. (2017), providing a mechanistic explanation for how significant reorganization can emerge in M/T ensembles despite stable low-dimensional population structure. In both Yamada et al (2017) and Kato et al (2012) the investigators have nuanced differences in experimental design (method of head fixation, behavioral paradigm used, training etc.), all of which are known to affect olfactory responses and therefore the degree of sparsity and overlap in population codes. Our model does not include any of these behavioral features that may differentially engage the olfactory circuit and thus affect population responses. Notably, in previous work, we highlight how even simple changes to top down feedback that reflect one phenomenological manipulation to functional connectivity in the olfactory circuit could have disparate effects on the degree of sparsity in neural representations over time whereby this manipulation would be activated by some behavior broadly. In our current model, there is no behavior that would allow us to study the critical features of the neural activity code in the M/T cells. Instead we focus on one specific aspect, adult neurogenesis which we can explicitly manipulate and affect in a biologically meaningful way. The review’s point however is well taken and important, and we have added text to the Discussion (line 336-344) to highlight the differing experimental outcomes and to clarify how our model aligns with the Yamada et al. results.

(2) In Figure 1, a set of GCs is killed off, and new GCs are integrated in the network as abGC. Following the elimination of 10% of GCs in the network, new cells are added and randomly assigned synaptic weights between these abGCs and MTC, GCs, SACs, and top-down projections from PCx. This is done for 11 days, during which time all GCs have gone through adult neurogenesis.

Is the authors' assumption here that across the 11 days, all GCs are being replaced? This seems to depart from the known biology of the olfactory bulb granule cells, i.e., GCs survive for a large fraction of the animal's life.

Thank you for raising this important point regarding the lifespan of granule cells (GCs). We agree that developmentally born GCs are not fully replaced. Indeed, multiple studies indicate that some developmentally born GCs can survive for very long periods, up to 18-24 months, essentially the lifetime of the animal (Kaplan, 1985; Petreanu & Alvarez-Buylla, 2002). However, the fraction of total GCs that such long lived GCs constitute remains an open question, in part because of challenges to measure the lifetime survival of newborn neurons. What there is consensus on is the significant size of the granule-cell population undergoing continuous turnover through adult neurogenesis (reviewed in Lepousez et al., 2013).

We should clarify that we do not assume that 100% of the granule cell population turns over in an 11 day period. We use “day” to represent a static epoch over which we can implement plasticity rules across two time scales. Critically, we also randomize the turnover treating every cell in the GC population as equally likely to be replaced. Prior experimental evidence suggests that some GCs are more likely to persist (possibly as a result of experience, Magavi et al., 2005) which may in some regards make our result on stabilization following repeated sensory exposure more dramatic (as the GCs that show the largest change following STDP may also be the ones that are the most stable, and therefore least likely to turnover). We do not include this in our model as we could not identify a framework for “selecting” which GCs would persist that would not be tautological. The point the reviewer raises is critical, and a discussion of these points is warranted - which we now include in the manuscript (line 352-361).

Additionally, there is some evidence that behaviors, such as novelty, can increase the rate of adult neurogenesis (Kamimura et al., 2022, H.van Praag et al.,1999, Gheusi and Lledo., 2014) , suggesting a complex reciprocal relationship between the mechanisms that generate the cells shaping how olfactory stimuli are encoded for and the encoding process itself; our model also does not include any of these dynamic features which represent an additional layer of complexity, which may further provide an intermediate time scale, one of behavioral selection and action, that is slower than the milliseconds on which spike time dependent plasticity happens, but faster than the time scale of neurogenesis. We include this point in the discussion also (line 352-361). 

Our 11-day simulation however is designed to uncover how plasticity across multiple timescales (STDP and adult neurogenesis) at the network level shapes odor representations as multiple rounds of GC turnover occur. Changing the timescale and magnitude replacement in the simulations (either in terms of days or percent cells replaced) would affect the degree to which drift happens, but not phenomenon. Additionally, the representational structure in our model at intermediate time points (e.g., days 8~10) would correspond well to scenarios in which some fraction of developmentally born GCs persists in the circuit. Thus, our simulations span a range of possible empirical regimes, from high turnover to partial preservation. We have added discussion to the revised manuscript (line 352-361) clarifying this point and acknowledging the biological heterogeneity in GC lifespans.

(3) The authors' model relies on several key assumptions: random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity, and random piriform to bulb connectivity. These assumptions are not necessarily accurate, as recent work revealed structure in the projections from the olfactory bulb to the piriform cortex and structure within the piriform cortex connectivity itself (Fink et al., bioRxiv, 2025; Chae et al., Cell, 2022; Zeppilli et al., eLife, 2021).

How do the results of the model relating adult neurogenesis in the bulb to drift in the piriform cortex representations change when considering an alternative scenario in which the olfactory bulb to piriform and intra-piriform connectivity is not fully distributed and indistinguishable from random, but rather is structured?

Thank you for pointing us to these important studies. We fully agree with the reviewer that the structure of the olfactory system might not be purely random, but we do not believe these papers contradict the level of abstraction used in our model.

Zeppilli et al. (2021) map molecularly defined projection neuron subtypes and their preferential targeting of different cortical and subcortical regions, but they do not report any fine-scale topographic organization of bulb → piriform connectivity that would contradict a view of randomly distributed input to piriform cortex. Studies from our lab using retrograde tracers in the blub show some spatial clustering of piriform cortical neurons whose axons project to the bulb (Padmanabhan et al., 2016, 2019), but these studies do not identify any “functional organization” or structure. Chae et al., (2022) focus on distinct long-range functional loops (mitral ↔ piriform vs tufted ↔ AON) and the differential role of cortical feedback, but again, at the level of cortical regions rather than individual cells and connectivity. Notably, our model does not consider AON.

Finally, Fink et al. (2025) reports a “like-to-like” excitatory connectivity motif within the piriform cortex and an experience-dependent reorganization of inhibitory synapses. As the authors note, “... this like-to-like motif is unlikely to reflect common input from the olfactory bulb”, so it does not conflict with our assumption of broadly random bulb → piriform input. This “like-to-like” motif is reflected in our model by wiring a certain subpopulation of piriform cells. On the other hand, we agree that the experience dependent changes in inhibitory connectivity within PCx are highly relevant for learning related plasticity but fall outside the scope of our study. We intentionally omitted piriform plasticity to isolate the contributions of adult neurogenesis in the bulb and plasticity acting on adult-born granule cells. But incorporating such cortical plasticity is an important direction for future work. We added a discussion (line 395-405) on this important point raised by the reviewer in the revised manuscript.

(4) I didn't understand the logic of the low-dimensional space analysis for M/T cells and piriform cortex neurons (Figures 2 & 3). In the authors' model, the full-ensemble M/T responses are reorganized over time, presumably due to the adult-born neurogenesis. Analyzing a lower-dimensional projection of the ensemble trajectories reveals a lower degree of re-organization. This is the same for the piriform cortex, but relatively, the piriform ensembles displayed in a low-dimensional embedding appear to drift more compared to the M/T ensembles.

This analysis triggers a few questions: which representation is relevant for the brain function - the high or the low-dimensional projection? What fraction of response variance is included in the low-dimensional space analysis? How did the authors decide the low-dimensional cut-off? Why does STDP cause more drift in piriform cortex ensembles vs. M/T ensembles? Is this because of the assumed higher dimensionality of the piriform cortex representations compared to the mitral cells?

Thank you for these thoughtful questions. We clarify the logic and purpose of the low-dimensional analyses and address each point below.

(1) Which representation is relevant for brain function, the high-dimensional or low-dimensional one?

We believe both representations are meaningful, with each capturing different aspects of the neural code. The high-dimensional activity reflects the full variability of individual cell responses, while the low-dimensional projection captures the dominant population level components that downstream areas are most likely to use for readout. We found that the low-dimensional representations are more stable in the bulb than in PCx, suggesting that information is used differentially between the two areas. The bulb provides a stable, sensory-anchored population code that reliably represents odor identity over time, consistent with both electrophysiological and behavioral studies (Nagayama et al., 2004, Chen et al., 2009, Davison and Katz, 2007, Cavaretta et al., 2018). This is consistent with its role as the first stage of information processing in the olfactory system which provides faithful representations that downstream circuits receive. The piriform cortex, by contrast, transforms this stable input into a more flexible representation. Drift in its low-dimensional space may reflect ongoing plasticity (Schoonover et al., Nature, 2021), integration of contextual signals, or higherdimensional computations characteristic of PCx (Fink et al., bioRxiv, 2025), suggesting its role more as an associative cortex instead of a pure sensory cortex.

(2) What fraction of variance is included in the low-dimensional space, and how was the cutoff chosen?

In our simulations, these PCs captured the majority of variance relevant for odor identity (~60–70% for M/T cells and ~55–65% for piriform cortex). We now report these fractions explicitly in Methods (line 937-939).

(3) Why does STDP cause more drift in piriform-cortex ensembles than in M/T ensembles? Does this reflect higher dimensionality in piriform cortex?

In our model, STDP does not cause more drift in PCx. It actually reduces drift and stabilizes PCx representations relative to the condition without STDP (as shown in Fig. 4C2). STDP has a much smaller effect in the bulb because: (1) M/T cells continue to receive stable odor input from the glomeruli and (2) the low-dimensional M/T representation is already stable even without plasticity. We have edited the manuscript to reiterate this point in both the results and discussion.

The reviewer is correct that the piriform cortex naturally exhibits more drift than the bulb, and their comment that this is due to its substantially higher representational dimensionality is spot on. The PCx contains many more neurons, receives highly divergent OB → PCx inputs, and has dense recurrent connectivity, all of which create many more degrees of freedom through which representations can drift. Additionally, because individual PCx neurons are sampling from a substantially more diverse combinatorial space of inputs (include feedback to piriform from an array of regions, Illig, 2005, Majak et al., 2004, Chapuis et al., 2013), the “dimensionality” of the population code is likely higher dimensional. While STDP stabilizes the dimensions of the PCx representation that are reinforced during plasticity, due to the large number of orthogonal dimensions available, some residual drift remains. Additionally, as the reviewer notes, there are some forms of plasticity, such as inhibitory plasticity in PCx that are not included in the model, that may also have an impact on both the representations, and the underlying dimensionality of those representations. We include these points in the discussion (line 381-394).

(5) Could the authors comment whether STDP at abGC synapses and its impact on decreasing drift represent a new insight, and also put it into context? Several studies (e.g., Lledo, Murthy, Komiyama groups) reported that abGC integrates in the network in an activity-dependent manner, and not randomly, and as such stabilizes the active neuronal responses, which is consistent with the authors' report.

Related, I couldn't find through the manuscript which synapses involving abGCs they focus on, or what is the relative contribution of the various plastic synapses shown in the cartoon from Figure 4 A1 (circles and triangles).

We thank the reviewer for raising this question. As the reviewer pointed out, several studies have shown that abGCs integrate into the bulb circuit in an activity dependent manner. They preferentially form synapses onto mitral/tufted cells that respond to behaviorally important odors, this “selection of surviving cells” is not included in our model. Instead, we use STDP at the synaptic level. This is of course not analogous, but provides a computational framework wherein the selection of surviving abGCs could be incorporated in future studies. It is perhaps notable that in our large scale simulations, synaptic changes at the population level may reflect some of this activity-dependent selection.

To that end, our model provides a new insight and suggests a broader function for adult neurogenesis. For example, when certain odors are reinforced in an activity dependent manner, abGCs born during that period may stabilize the circuits that respond to those odors. The resulting reduction of drift would help keep the representation of those odors stable over time, even while other parts of the circuit continue to change. We now highlight this idea in the Discussion (line 366-373).

For the second part of the question: in our model, STDP acts on two sets of connections. It applies to the synapses onto abGCs from M/T cells, GC/SAC cells, and PCx neurons. It also applies to the synapses that abGCs project to, including those onto M/T cells and GC/SAC cells. We have clarified this in the revised Methods (line 10011004).

(6) The study would be strengthened, in my opinion, by including specific testable predictions that the authors' models make, which can be further food for thought for experimentalists.

How does suppression of adult-born neurogenesis in the OB impact the stability of mitral cell odor responses? How about piriform cortex ensembles?

We appreciate the reviewer’s suggestion and formalize the following two predictions from our model:

Prediction 1: Suppressing adult neurogenesis will reduce spontaneous representational drift in the PCx. Increasing spike-timing-dependent plasticity during periods of experience with a specific odor will selectively stabilize representations of that odor.

Prediction 2: Adult neurogenesis will not affect AON representations of odor identity or concentration in the same way that PCx representations are altered and drift.

We include these two ideas in the discussion as experimentally testable predictions.

Reviewer #2 (Public review):

Summary:

The authors address a critical problem in olfactory coding. It has long been known that adult neurogenesis, specifically in the form of adult-born granule cells that embed into the existing inhibitory networks on the olfactory bulb, can potentially alter the responses of Mitral/Tufted neurons that project activity to the Piriform Cortex and to other areas of the brain. Fundamentally, it would seem that these granule cells could alter the stability of neural codes in the OB over time. The authors develop a spiking network model to explore how stability can be achieved both in the OB over time and in the PC, which receives inputs. The model recapitulates published activity recordings of M/T cells and shows how activity in different M/T cells from the same glomerulus shifts over time in ways that, in spite of the shift, preserve population/glomerular level codes. However, these different M/T cells fan out onto different pyramidal cells of the PC, which gives rise to instability at that level. STDP then, is necessary to maintain stability at the PC level as long as odor environments remain constant. These results may also apply to a similar neurogenesis-based change in the Dentate Gyrus, which generates instability in CA1/3 regions of the hippocampus

Strengths:

A robust network model that untangles important, seemingly contradictory mechanisms that underlie olfactory coding.

Weaknesses:

The work is a significant contribution to understanding olfactory coding. But the manuscript would benefit from a brief discussion of why neurogenesis occurs in the first place - e.g., injury, ongoing needs for plasticity, and adapting to turnover of ORNs. There is literature on this topic. It seems counterintuitive to have a process in the MOB (and for that matter in the DG) that potentially disrupts the ability to generate stable codes both in the MOB and PC, and in particular a disruption that requires two different mechanisms - multiple M/T cells per glomerulus in the MOB and STDP in the PC - to counteract.

We appreciate the reviewer’s suggestion and added discussion on this point in the revised manuscript (line 431-435).

Given that neurogenesis has an important function, and a mechanism is in place to compensate for it in the MOB, why would it then be disrupted in fan-out projections to the PC? The answer may lie in the need for fan-out projections so that pyramidal neurons in the PC can combinatorially represent many different inputs from the MOB. So something like STDP would be needed to maintain stability in the face of the need for this coding strategy.

This kind of discussion, or something like it, would help readers understand why these mechanisms occur in the first place. It is interesting that PC stability requires that odor environments be stable, and that this stability drives PC representational stability. This result suggests experimental work to test this hypothesis. As such, it is a novel outcome of the research.

We agree with the reviewer. The fan-out from the bulb to the piriform cortex is essential for the combinatorial coding that allows PCx neurons to represent many odor features and mixtures. This architecture gives the piriform cortex great coding capacity, but it also makes the system sensitive to small changes in its inputs. As a result, drift that originates in the bulb can spread more easily in PCx. A stabilizing mechanism is therefore needed downstream. In our model, STDP provides this stabilization by reinforcing the dimensions that carry meaningful odor structure. This allows the piriform cortex to keep a stable population code even when its inputs change over time. Neurogenesis supplies the flexibility, the fan-out supplies the expressive power, and STDP supplies the stability. All three elements work together to support a system that must recognize odors reliably while still adapting to new sensory experiences. We have added discussion on this point in the revised manuscript (line 395-405).

Reviewer #3 (Public review):

Summary

The authors set out to explore the potential relationship between adult neurogenesis of inhibitory granule cells in the olfactory bulb and cumulative changes over days in odorevoked spiking activity (representational drift) in the olfactory stream. They developed a richly detailed spiking neuronal network model based on Izhikevich (2003), allowing them to capture the diversity of spiking behaviors of multiple neuron types within the olfactory system. This model recapitulates the circuit organization of both the main olfactory bulb (MOB) and the piriform cortex (PCx), including connections between the two (both feedforward and corticofugal). Adult neurogenesis was captured by shuffling the weights of the model's granule cells, preserving the distribution of synaptic weights. Shuffling of granule cell connectivity resulted in cumulative changes in stimulus-evoked spiking of the model's M/T cells. Individual M/T cell tuning changed with time, and ensemble correlations dropped sharply over the temporal interval examined (long enough that almost all granule cells in the model had shuffled their weights).

Interestingly, these changes in responsiveness did not disrupt low-dimensional stability of olfactory representations: when projected into a low-dimensional subspace, population vector correlations in this subspace remained elevated across the temporal interval examined. Importantly, in the model's downstream piriform layer, this was not the case. There, shuffled GC connectivity in the bulb resulted in a complete shift in piriform odor coding, including for low-dimensional projections. This is in contrast to what the model exhibited in the M/T input layer. Interestingly, these changes in PCx extended to the geometrical structure of the odor representations themselves. Finally, the authors examined the effect of experience on representational drift. Using an STDP rule, they allowed the inputs to and outputs from adult-born granule cells to change during repeated presentations of the same odor. This stabilized stimulus-evoked activity in the model's piriform layer.

Strengths

This paper suggests a link between adult neurogenesis in the olfactory bulb and representational drift in the piriform cortex. Using an elegant spiking network that faithfully recapitulates the basic physiological properties of the olfactory stream, the authors tackle a question of longstanding interest in a creative and interesting manner. As a purely theoretical study of drift, this paper presents important insights: synaptic turnover of recurrent inhibitory input can destabilize stimulus-evoked activity, but only to a degree, as representations in the bulb (the model's recurrent input layer) retain their basic geometrical form. However, this destabilized input results in profound drift in the model's second (piriform) layer, where both the tuning of individual neurons and the layer's overall functional geometry are restructured. This is a useful and important idea in the drift field, and to my knowledge, it is novel. The bulb is not the only setting where inhibitory synapses exhibit turnover (whether through neurogenesis or synaptic dynamics), and so this exploration of the consequences of such plasticity on drift is valuable. The authors also elegantly explore a potential mechanism to stabilize representations through experience, using an STDP rule specific to the inhibitory neurons in the input layer. This has an interesting parallel with other recent theoretical work on drift in the piriform (Morales et al., 2025 PNAS), in which STDP in the piriform layer was also shown to stabilize stimulus representations there. It is fascinating to see that this same rule also stabilizes piriform representations when implemented in the bulb's granule cells.

The authors also provide a thoughtful discussion regarding the differential roles of mitral and tufted cells in drift in piriform and AON and the potential roles of neurogenesis in archicortex.

In general, this paper puts an important and much-needed spotlight on the role of neurogenesis and inhibitory plasticity in drift. In this light, it is a valuable and exciting contribution to the drift conversation.

We appreciate the reviewer’s comment and thank them for their thoughtful feedback.

Weaknesses

I have one major, general concern that I think must be addressed to permit proper interpretation of the results.

I worry that the authors' model may confuse thinking on drift in the olfactory system, because of differences in the behavior of their model from known features of the olfactory bulb. In their model, the tuning of individual bulbar neurons drifts over time.

This is inconsistent with the experimental literature on the stability of odor-evoked activity in the olfactory bulb.

In a foundational paper, Bhalla & Bower (1997) recorded from mitral and tufted cells in the olfactory bulb of freely moving rats and measured the odor tuning of well-isolated single units across a five-day interval. They found that the tuning of a single cell was quite variable within a day, across trials, but that this variability did not increase with time. Indeed, their measure of response similarity was equivalent within and across days. In what now reads as a prescient anticipation of the drift phenomenon, Bhalla and Bower concluded: "it is clear, at least over five days, that the cell is bounded in how it can respond. If this were not the case, we would expect a continual increase in relative response variability over multiple days (the equivalent of response drift). Instead, the degree of variability in the responses of single cells is stable over the length of time we have recorded." Thus, even at the level of single cells, this early paper argues that the bulb is stable.

This basic result has since been replicated by several groups. Kato et al. (2012) used chronic two-photon calcium imaging of mitral cells in awake, head-fixed mice and likewise found that, while odor responses could be modulated by recent experience (odor exposure leading to transient adaptation), the underlying tuning of individual cells remained stable. While experience altered mitral cell odor responses, those responses recovered to their original form at the level of the single neuron, maintaining tuning over extended periods (two months). More recently, the Mizrahi lab (Shani-Narkiss et al., 2023) extended chronic imaging to six months, reporting that single-cell odor tuning curves remained highly similar over this period. These studies reinforce Bhalla and Bower's original conclusion: despite trial-to-trial variability, olfactory bulb neurons maintain stable odor tuning across extended timescales, with plasticity emerging primarily in response to experience. (The Yamada et al., 2017 paper, which the authors here cite, is not an appropriate comparison. In Yamada, mice were exposed daily to odor. Therefore, the changes observed in Yamada are a function of odor experience, not of time alone. Yamada does not include data in which the tuning of bulb neurons is measured in the absence of intervening experience.)

Therefore, a model that relies on instability in the tuning of bulbar neurons risks giving the incorrect impression that the bulb drifts over time. This difference should be explicitly addressed by the authors to avoid any potential confusion. Perhaps the best course of action would be to fit their model to Mizrahi's data, should this data be available, and see if, when constrained by empirical observation, the model still produces drift in piriform. If so, this would dramatically strengthen the paper. If this is not feasible, then I suggest being very explicit about this difference between the behavior of the model and what has been shown empirically. I appreciate that in the data there is modest drift (e.g., Shani-Narkiss' Figure 8C), but the changes reported there really are modest compared to what is exhibited by the model. A compromise would be to simply apply these metrics to the model and match the model's similarity to the Shani-Narkiss data. Then the authors could ask what effect this has on drift in piriform.

The risk here is that people will conclude from this paper that drift in piriform may simply be inherited from instability in the bulb. This view is inconsistent with what has been documented empirically, and so great care is warranted to avoid conveying that impression to the community.

We thank the reviewer for highlighting this important issue. We agree that the interpretation of our model requires care to avoid implying that the olfactory bulb exhibits spontaneous drift. As the reviewer points out, the empirical literature shows that M/T-cell tuning is highly stable for infrequently experienced odors, but can change with daily, persistent odor exposure (e.g., Kato et al., 2012; Yamada et al., 2017).

We thank the reviewer for highlighting the Bhalla and Bower paper, as it is foundational and actually raises a number of interesting and important points. As the authors noted, there was significant variability in trial-to-trial responses over sessions and days in single neurons. This is likely due to on-going dynamics (Laurent, 1999), the impact of behaviorally relevant top-down feedback (Chen and Padmanabhan, 2022), decision making (Kay and Laurent, 1999), and an array of factors that our model does not include. In that manuscript, the authors note “the variability of the same neuron recorded over different days…was not statistically different from the within day comparisons.” While these results appear prima facie to be different from our results, there are several reasons why they may not be the case.

First, different metrics are used for measuring neuronal stability, which may contribute to some of the differences. Second, and perhaps more importantly and interestingly, the authors in that study noted the significant trial-to-trial variability within day, which is not present in our study because our model has none of the richness of behavior that Bhalla and Bower found in the freely behaving rat. This variability within day (which is much higher than what we report) would reduce the impact of drift across days - a result that would complicate how plasticity across multiple timescales occurs. We thank the reviewer for the insights on this critical study and include these points in our discussion (line 321-330).

Neural responses to odor representations are incredibly variable across different time scales (Padmanabhan and Urban 2010, Angelo et al 2011, Kapoor and Urban 2006, Friedrich and Laurent, 2001, Smear et al 2011, Wesson et al 2008). In our model, none of this selection of survival related to behavior is included, nor are there specific rules about which synapses may be preferentially strengthened (due to neuro modulation corresponding to behavioral choice and reinforcement learning). Instead, we aimed to recapitulate the experimental design of a few studies (Kato et al 2012, Yamada et al, 2017) to understand how neurogenesis and drift are related. Over the simulated 10 days, the odor is presented every day, and the network is otherwise frozen between sessions—meaning the model lacks mechanisms that would normally support recovery during intervals without odor exposure. Under these conditions, adult neurogenesis effectively interacts with repeated experience, producing gradual changes in individual M/T-cell tuning. Thus, our results should be interpreted as modeling experience dependent changes over the timescale of neurogenesis, not as evidence for spontaneous drift in the bulb. We now state this explicitly in the Discussion to prevent confusion and expand the discussion to incorporate some of these critical ideas (line 321-330).

Major comments (all related to the above point)

(1) Lines 146-168: The authors find in their model that "individual M/T cells changed their responses to the same odor across days due to adult-neurogenesis, with some cells decreasing the firing rate responses (Fig.2A1 top) while other cells increased the magnitude of their responses (Fig. 2A2 bottom, Fig. S2)" they also report a significant decrease in the "full ensemble correlation" in their model over time. They claim that these changes in individual cell tuning are "similar to what has been observed by others using calcium imaging of M/T cell activity (Kato et al., 2012 and Yamada et al., 2017)" and that the decrease in full ensemble correlation is "consistent with experimental observations (Yamada et al., 2017)." However, the conditions of the Kato and Yamada experiments that demonstrate response change are not comparable here, as odors were presented daily to the animals in these experiments. Therefore, the changes in odor tuning found in the Kato and Yamada papers (Kato Figure 4D; Yamada Figure 3E) are a function of accumulated experience with odor. This distinction is crucial because experience-induced changes reflect an underlying learning process, whereas changes that simply accumulate over time are more consistent with drift. The conditions of their model are more similar to those employed in other experiments described in Kato et al. 2012 (Figure 6C) as well as Shani-Narkiss et al. (2023), in which bulb tuning is measured not as a function of intervening experience, but rather as a function of time (Kato's "recovery" experiment). What is found in Kato is that even across two months, the tuning of individual mitral cells is stable. What alters tuning is experience with odor, the core finding of both the Kato et al., 2012 paper and also Yamada et al., 2017. It is crucial that this is clarified in the text.

We thank the reviewer. As the issue raised here is related to the previous comment, we have clarified this in the revised text to avoid any misleading comparison and specify what aspects of our computational model map onto experimental studies and what aspects we cannot recapitulate and as a result, the places where our comparisons are limited.

(2) The authors show that in a reduced-space correlation metric, the correlation of lowdimensional trajectories "remained high across all days"..."consistent with a recent experimental study" (Shani-Narkiss et al., 2023). It is true that in the Shani-Narkiss paper, a consistent low-dimensional response is found across days (t-SNE analysis in Shani-Narkiss Figure 7B). However, the key difference between the Shani-Narkiss data and the results reported here is that Shani-Narkiss also observed relative stability in the native space (Shani-Narkiss Figure 8). They conclude that they "find a relatively stable response of single neurons to odors in either awake or anesthetized states and a relatively stable representation of odors by the MC population as a whole (Figures 6-8; Bhalla and Bower, 1997)." This should be better clarified in the text.

We agree with the reviewer that some of the cells in Shani-Narkiss Figure 8B showed relatively stable responses (while others did not). However, there is a clear monotonic increase in the “Average differences” over time, from “Same day” to “1 month” to “6 month”, as quantified in their Figure 8B. Although the author concluded that they "find a relatively stable response of single neurons”, we would argue that their data also provided evidence for what we would term “relatively unstable responses” as found in our model. But per reviewer’s suggestion, we better clarify it in the text now (line 194197).

(3) In the discussion, the authors state that "In the MOB, individual M/T cells exhibited variable odor responses akin to gain control, altering their firing rate magnitudes over time. This is consistent with earlier experimental studies using calcium-imaging." (L3146). Again, I disagree that these data are consistent with what has been published thus far. Changes in gain would have resulted in increased variability across days in the Bhalla data. Moreover, changes in gain would be captured by Kato's change index ("To quantify the changes in mitral cell responses, we calculated the change index (CI) for each responsive mitral cell-odor pair on each trial (trial X) of a given day as (response on trial X - the initial response on day 1)/(response on trial X + the initial response on day 1). Thus, CI ranges from −1 to 1, where a value of −1 represents a complete loss of response, 1 represents the emergence of a new response, and 0 represents no change." Kato et al.). This index will capture changes in gain. However, as shown in Figure 4D (red traces), Figure 6C (Recovery and Odor set B during odor set A experience and vice versa), the change index is either zero or near zero. If the authors wish to claim that their model is consistent with these data, they should also compute Kato's change index for M/T odor-cell pairs in their model and show that it also remains at 0 over time, absent experience.

We appreciate the reviewer’s suggestion and edited the text to make it more accurate (line 319-320).

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Line 28 "a graduate alteration in sensory perception". We do not know if drift results in changes in perception. If anything, behavioral evidence suggests that perception remains stable in spite of drift. For example, in Driscoll et al. (2017) mice are able to successfully navigate a virtual T maze despite drift, and in Schoonover et al. (2021), mice maintain aversive responses following fear conditioning, despite drift in the piriform. Finally, spatial navigation appears unimpaired despite pronounced drift in the hippocampus (e.g., Climer et al., 2025). It would be more appropriate to say "stimulusevoked activity patterns" than "sensory perception" or other words that refer to neuronal activity rather than cognition or behavior.

We edited the text to make it more accurate per the reviewer’s suggestion (line 27).

(2) In the introduction, the authors state: "This representational drift has led to the hypothesis that PCx, rather than being a primary sensory area, may be more like an association cortical region." (L76-78). However, the hypothesis that PCx operates as an association cortex comes originally from Haberly's work and thinking (e.g., Haberly and Bower, 1984, elaborated in extensive detail in Haberly, 2001). I think it would be appropriate to acknowledge that here.

We added the references to make acknowledge that per the reviewer’s suggestion (line 77).

(3) In the methods, the authors elegantly describe how they induce neurogenesis in their model using weight reshuffling (L805-814). I think it could really help the reader understand the model if this idea were also included in the results section. As the results section currently reads, it seems as if their model implemented neurogenesis in a different fashion: "To do this, following elimination of 10% of the GCs in the network, we added new cells and randomly assigned synaptic weights between these abGCs and M/Ts". I appreciate that in their model, shuffling all the weights of a given GC randomly is akin to "elimination", but I feel like at first blush the results section risks giving an impression a bit different than that actually used in the model.

We edited the text to make it more accurate per the reviewer’s suggestion (line 110-112).

Author response:

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

Reviewer #1 (Public review):

This work develops a simple, rapid, low-cost methodology for assembling combinatorially complete microbial consortia using basic laboratory equipment. The motivation behind this work is to make the study of microbial community interactions more accessible to laboratories that lack specialized equipment such as robotic liquid handlers or microfluidic devices. The method was tested on a library of Pseudomonas aeruginosa strains to demonstrate its practicality and effectiveness. It provided a means to explore the complex functional interactions within microbial communities and identify optimal consortia for specific functions, such as biomass production.

The primary strength of this manuscript lies in its accessibility and practicality. The method proposed by the authors allows any laboratory with standard equipment, such as multichannel pipettes and 96-well plates, to readily construct all possible combinations of microbial consortia from a given set of species. This greatly enhances access to full factorial designs, which were previously limited to labs with advanced technology.

Another strength of the manuscript is the measurement and analysis of the biomass of all possible combinations of 8 strains of P. aeruginosa. This analysis provides a concrete example of how the authors' new methodology can be used to identify the best-performing communities and map pairwise and higher-order functional interactions.

Notably, the authors do exceptionally well in providing a thorough description of the methodology, including detailed protocols and an R script for customizing the method to different experimental needs. This enhances the reproducibility and adaptability of the methodology, making it a valuable resource for researchers wishing to adopt this methodology.

We thank the reviewer for their thoughtful comments and positive assessment of our work. Below we detail the changes we have introduced in the manuscript to clarify issues raised by the reviewer.

While the methodology is robust and well-presented, there are some limitations that should be acknowledged more thoroughly. First, the method's scalability is an important factor. The authors indicate that it should be effective for up to 10-12 species, but there is no discussion of what sets this scale: time, amount of labor, consumables, the likelihood of error, sample volume, etc.

The 10-12 species estimation is based on our own experience implementing the protocol, and set primarily by time, labor, and consumables (as rightly pointed out by the reviewer) rather than conceptual limitations of the approach. We have added clarifications in the Discussion (lines 401-405) regarding these scalability-limiting factors.

Second, this methodology is tailored to construct communities where the abundance of each strain is identical in each combination. Therefore, combinations with a different number of strains also differ in the total initial amount of microbial cells. Second, variations in the initial proportions of the same set of strains cannot be readily explored.

Note that the “density homogenization” step is optional and it could be skipped entirely, which would result in a same species being present at variable densities across consortia: specifically, skipping this step would make the density of a species in a consortium inversely proportional to the number of species in that consortium. Further variations in initial abundance could be explored by treating a same strain at two (or more) starting abundances as distinct inputs of the protocol – though this would naturally increase the number of combinations to test.

We have included a paragraph in the Discussion (lines 416-423) describing how we can, in principle, extend our protocol to explore abundance effects.

Third, the manuscript only discusses how to construct the combinations, and not how to assay them afterward (e.g. for community function, interspecific interactions, etc.). While details on how to achieve these goals are clearly outside the scope of this work, the use of biomass as an example function may obfuscate this caveat, which should be stated more explicitly.

We agree that the manuscript focuses exclusively on the construction of microbial communities and does not address how these communities should be assayed afterward. This is an intentional scope decision. The proposed protocol is fully compatible with a wide range of functional, interaction-based, or omics-based assays. Absorbance is mentioned as an illustrative example of a possible readout, rather than as a recommended or exclusive parameter. We have revised the text to explicitly state that the assessment of community function or interspecific interactions lies outside the scope of this work and must be tailored to the specific biological question being addressed.

Reviewer #1 (Recommendations for the authors):

A few specific technical notes and notes about clarity:

(1) It may be worth being more explicit about how to produce replicates. For example, producing technical replicates by inoculating multiple times from the same set of combinations, while biological replicates require making the combinations multiple times.

We have updated the main text to clarify this point (line 780-781).

(2) Figure 2C: May be worth adding some context to these performance numbers. What are typical accuracies? What would they be in a liquid handler?

Assessing typical accuracies is nuanced since the error depends not only on the assembly steps, but also on potential intrinsic variation of the specific community function being tested and the method used to quantify it. One of the main reasons for including the experiment using colorant combinations was precisely to minimize these other sources of variation. In this experiment, we find that the error we quantify is consistent with cumulative pipetting variation (as a reference, a typical lab micropipette has an error of 0.5-1%). This is now explicitly mentioned in the manuscript.

(3) Figure 5A: I realize it is unlikely that strains go extinct in these experiments. But it is still worth clarifying that the number of strains is the number inoculated, rather than the one present at the time of measurement.

We updated the caption of Figure 5A as recommended by the reviewer.

(4) Figure 5B: I realize this is just for illustration purposes, but you should provide more information about the magnitude of the difference in performance of these combinations and the confidence in their ranking (or variability in performance across replicates).

Following this suggestion, we have added a paragraph where we report the variation across replicates for the highest-performing consortia (lines 318-323). Indeed, while variation across replicates is small, it is enough to produce an overlap between the confidence intervals of the function of some of the highest-performing consortia. This is now explicitly acknowledged in the manuscript.

(5) Figure 5C: I believe the bold black lines indicate the combinations shown in panel D, but that is not explicitly stated.

We have updated the caption of Figure 5C.

Reviewer #2 (Public review):

A simple and effective method for combinatorial assembly of microbes in synthetic communities of <12 species.

Overall, this manuscript is a useful contribution. The efficiency of the method and clarity of the presentation is a strength. It is well-written and easy to follow. The figures are great, the pedagogical narrative is crisp. I can imagine the method being used in lots of other contexts too.

The authors could better clarify what HOIs mean. They could address challenges with assaying community function. However, neither of these “weaknesses” affects the primary goal of the paper which is methodological.

We thank the reviewer for the positive assessment. With respect to HOIs, we recognize that defining and quantifying them is a non-trivial subject within the broader field of microbial ecology (see e.g. ref. 24 within the manuscript). Since our aim with this manuscript is methodological, as the reviewer notes, here we have done our best to avoid introducing new or ambiguous definitions. For this reason, we simply adopt a definition given in previous works (including refs. 10, 19, 24, 29, 37, and 38 in the manuscript), where the context-dependence of pairwise interaction terms is taken as a signature of HOIs. With respect to the challenges in assaying community function, please see our responses below.

Reviewer #2 (Recommendations for the authors):

Overall, this manuscript is a useful contribution, I appreciate the authors taking the time to write it up! I have a few relatively minor comments.

(1) It would be nice in the introduction to address why we might want the full factorial construction of communities in the first place. This is an especially relevant question in light of the authors' 2023 Nat E&E paper where they showed that the function of communities can often be learned even when only a fraction of all possible communities is measured. This is addressed in part in the paragraph on line 34, but I think it might be worth expanding a bit given the focus on the paper.

We sincerely appreciate the reviewer’s feedback. In fact, one of the reasons that make full factorial construction desirable is precisely to test theoretical and computational models of community function, including (but not only) the statistical models developed in our 2023 Nature E&E paper. In that work, we showed that low-order models can explain a substantial fraction of the variation in community function in previously-published datasets, but we also predict that the same models could fail under complex structures of microbial interactions (e.g., strong high-order interactions). The protocol we present here enables the empirical quantification of such interactions, making this prediction (and others) directly testable. We have included that clarification in the revised manuscript (lines 56-58).

(2) Around line 74, I think it is worth mentioning that even this elegant design will face insurmountable practical challenges (time, liquid handling operations, number of plates will explode) for full factorial design with 20, 30, 40 species or more. This is relevant for some very complex synthetic consortia that some microbiome groups are constructing (e.g. hCom2 from Huang/Fishbach groups) https://www.sciencedirect.com/science/article/pii/S0092867422009904.

We agree with the reviewer that full factorial designs become impractical for very large species pools. These limits are now more clearly mentioned in the revised manuscript. We refer the reviewer to our response to comment #1 by Reviewer 1 for further details.

(3) The binary construction is a really nice clean way to explain the protocol. Appreciate the pedagogy!

We thank the reviewer for the appreciation.

(4) In the experiment with pseudomonas strains the consortia are grown in LB. This medium will support growth to relatively high OD (>1). At these densities, the change in OD with density is almost certainly not linear with cell density, and this nonlinearity likely depends on strain identity. In this case, the assumption of additivity may not hold. As a result, some of the observed "interactions" may simply be non-linearity in the assay and not the abundance of bacteria in the communities. Of course, this does not affect the assembly protocol in any way, but it does complicate the interpretation of interactions via this assay. I think this is worth pointing out since other researchers may have to think carefully about the assay they use when constructing these synthetic consortia. I think in this methods paper it is important to emphasize this so other researchers do not mistakenly identify interactions due to issues with the assay.

We thank the reviewer for pointing out this important aspect. In our experiment, we use Abs₆₀₀ simply as an example of a measurable community-level function. The reviewer is absolutely correct in that mapping absorbance to biomass is nuanced at large OD values, where this relationship becomes non-linear. While this is not an issue from the perspective of the protocol itself, it is indeed an important consideration for users who may want to obtain reliable quantifications of biomass. We have updated the manuscript to explicitly mention this potential issue (lines 307-313). We have also emphasized the fact that our focus on Abs₆₀₀ is strictly for illustrative purposes, and we have removed all instances where a direct mapping from Abs₆₀₀ to biomass was implied in the text.

(5) Subtle point regarding HOIs. HOI (or pairwise) statistical interactions need not quantitatively be the same as interactions in a lotka volterra sense. I realize the authors do not explicitly use the term "interaction" in an gLV model formalism but this is how the majority of readers will interpret this term. I believe it is a research question as to how pairwise gLV interactions manifest themselves in terms of functional interactions. For example, a purely pairwise LV model could easily have HOI "functional interactions" if the function is total abundance since abundances depend nonlinearly on LV interactions. I think this part of the manuscript could be confusing to readers for this reason. I think the term "functional interaction" really helps with this issue, but just asking the authors to make sure this is clear.

I say this because ref: 37 is focused on HOIs in an LV sense. Here, as the authors are aware, they are computing statistical "interactions" in the sense of epistasis. Given that they are computing this epistasis averaged across all community compositions a more appropriate citation might be [https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004771] where the same quantity is computed in a protein context.

We thank the reviewer for pointing out this important issue. Indeed, we use the term “interaction” in a statistical sense (as the deviation of the observed community function from a null, additive expectation) rather than in a Lotka-Volterra sense. We agree that the reference suggested by the reviewer is more appropriate in this context. We have updated the reference list accordingly.

(6) Figure 5G - a little hard to see. Any way to show this data more clearly? It looks like all interactions have a mean of 0 because of the way the data are presented.

The reviewer is indeed correct in that, as defined, the interactions that we quantify are back ground dependent, and their average across backgrounds lies near zero for all species. More than an issue with the representation, we think that this is an important empirical observation: it indicates that a same species pair may interact positively or negatively depending on its ecological context. We believe that the current representation is most appropriate for making this clear, but we would be open to discussing alternatives if the reviewer had a specific suggestion in mind.

Reviewer #3 (Public review):

The authors developed a useful methodology for generating all combinations of multiple reagents using standard lab equipment. This methodology has clear uses for studying microbial ecology as they demonstrated. The methodology will likely be useful for other types of experiments that require exhaustive testing of all possible combinations of a given set of reagents (e.g., drug-drug antagonism and synergy).

The authors provided a useful R script that generates a detailed experimental protocol for building the desired combination from any number of reagents. The produced document is useful and has clear instructions. The output of the computer script will be strengthened if graphical output is also provided (similar to the one provided in Figure 1C).

The authors show that the error rate of the method doesn't go up with the number of combinations using dyes (Figure 2).

The authors demonstrate the value of their methodology for studying interactions within microbial consortia by assembling all possible combinations of eight strains of Pseudomonas aeruginosa. The value of their methodology for this application is well-founded. However, it is also unclear why specific experimental choices were made for this application. It is unclear why authors continue to show the absorbance measurements of strain assemblies over the entire wavelength spectrum and not just for ABS 600 nm (Figures 3 and 4). It is also unclear why the authors provided information on the "sum of the three spectra" as this reference line is meaningless and not a reasonable null model for estimating how well specific strain combinations will grow together.

Figure 5 illustrates the various analysis types that can be performed on the data collected from growing combinations of eight Pseudomonas aeruginosa strains. It is a very informative figure since it provides a "roadmap" on the various ways in which the dataset produced can be explored. The information in Figures 5 and S6 will likely be very useful for a wide audience.

Reviewer #3 (Recommendations for the authors):

(1) Congratulations. I think the manuscript lays out a simple and very elegant methodology that will be useful for many. While I think the method is overall well explained and rationalized, the paper can greatly benefit from further expansion of Figure 5 at the expense of Figures 3 and 4.

We thank the reviewer for their thoughtful assessment of our work. We have considered the recommendations and discuss the following points in response.

(2) Unless I am missing something, there is no reason to present data collected across the entire wavelength spectrum for microbial assemblies (Figures 3 and 4). Moreover, using the same color palette for bacterial strains (Figure 3A) and colorants (Figure 2) is highly confusing. I suggest considering using only the 600 nm wavelength for any data collected from microbial assemblies and using a very different color palette for bacteria and colorants to avoid misinterpretation of the data.

We thank the reviewer for this suggestion. Our goal with Figures 3-4 was to illustrate the convenience of the protocol and the ease with which many measurements can be performed in parallel once the combinatorial assembly has been completed. While we focus on Abs₆₀₀ for all subsequent analyses, we chose to display the full spectra in Figs. 3-4 in hopes that future studies can make use of our rich dataset to interrogate questions on microbial interactions, with the option to focus on other wavelengths (which can effectively be treated as different community-level functions in their own right; for instance, we have previously used Abs₄₀₅ as a proxy for siderophore concentration). We think there is value in Figs. 3-4 in their current form to make this clear to readers.

(3) Unlike dye absorbance, bacterial carrying capacity has an upper limit, so summing individual population absorbance as a reference line seems unjustified. If the summation of absorbance is meant to provide a "null model" for expected growth, a more suitable model should be considered (e.g., max spectra or a weighted sum of the spectra from individual members).

We agree with the reviewer that our null model is not biologically constrained, and we did not intend to imply that the additive expectation was derived from biological principles. Instead, this additive expectation should be interpreted as a simple statistical baseline with minimal assumptions. The use of an additive baseline for quantifying microbial interactions has been addressed in the literature (see, e.g., references 10, 19, 24, 29, 37, and 38), and so here we chose to conform to this convention to avoid introducing new, non-standard quantifications of pairwise and higher-order interactions. We have revised the text to make this more explicit.

(4) The R script is a valuable tool. I think that a valuable improvement will be to also generate visual representations as part of the script’s output such as the colored plates in Figure 1C that are specific to the generated protocol.

We have updated the script so that it now also outputs a table specifying the location of each consortium within the plates. We chose to make this a text, rather than a graphics output, to ensure cross-device compatibility.

(5) The discussion rightly acknowledges the potential to extend the protocol to larger libraries using liquid handlers. To facilitate this implementation, it might be beneficial to modify the script output so that the ‘volume’, ‘plate’, and ‘column’ values are tab- or comma-delimited.

We thank the reviewer for the suggestion. We have modified the output so that it is now tab-delimited.

(6) Figures 3 and 4 do not provide a lot of insight. I would suggest combining them into a single figure and using only absorbance values at 600 nm. It would also be interesting to add a histogram of these absorbance values and possibly show histograms for subgroups (e.g. all assemblies with more than 3 strains vs all assemblies with 3 or fewer strains).

With respect to Figs. 3 and 4, we refer the reviewer to our response to comment #2. With respect to the histogram/subgroups plot, we understand that this would be a slightly modified version of the current Fig. 5A, where we show means and standard deviations across all subgroups of 1 to 8 species, and so we find it unclear what this figure would add.

(7) With the recommendations of removing or reworking Figures 3 and 4, and the fact that Figure 5 is data-rich (and extremely useful), it would be beneficial to split Figure 5 and include the data shown in Figure S6 in the main figure. The analysis in Figure 6S is valuable and it might be beneficial to elevate this analysis to a primary figure and provide a detailed explanation of its rationale and methods in the main text.

We appreciate this suggestion. In our view, we find that both the text and the figures benefit from a heavy focus on the assembly protocol, as this is the main contribution of this work. While we do think it is valuable to highlight the type and amount of data that can be collected with a full factorial assembly, as well as the types of analyses that can be performed with this data, we are afraid that allocating more space to these analyses may distract readers from the methodology itself. We have therefore chosen to keep the original structure for Figs. 5 and S6.

Author response:

Reviewer 1:

We thank the reviewer for bringing a critical theoretical distinction to our attention. We agree that the Temporal Generalization (TG) results specifically rule out the reinstatement of post-onset neural codes, the idea that the brain pre-activates the same neural representation evoked by the stimulus. In fact, we mention in the discussion: "This temporal variability underscores the need for a more nuanced view of what constitutes predictive pre-activation, as no stable representational state appears to persist after word presentation that could serve as its target.".

To our understanding, prediction is rarely explicitly defined in the literature, and the distinction between predictive pre-activation and other forms of prediction is seldom made. Moreover, the idea of compressed or abstract forms of pre-activated representations has not, to our knowledge, been explicitly articulated in the literature. Our TG findings therefore, put meaningful constraints on theories of prediction. In the revisions we will expand on this more and include a broader description of potential forms of pre-activation. We will emphasize that the TG results specifically rule out that the brain pre-activates the same neural code used for sensory-evoked processing.

Moreover, although TG analysis does not rule out alternative notions of predictive pre-activation, we believe our second analysis (the inclusion of future word embeddings) provides independent evidence that argues against more abstract forms of prediction. Unlike the TG analysis, this encoding approach is not constrained to a specific neural code; if the brain represented upcoming words in any linearizable format (abstract, probabilistic, or latent) incorporating those embeddings should have improved the brain score at the current word's onset. We found no such improvement until the word was actually heard. In the revised manuscript, we will reformulate the narrative to clarify that while TG alone rejects a specific form of pre-activation, the combined evidence from both analyses suggests there is a broader lack of predictive pre-activation.

Reviewer 2:

We thank the reviewer for their constructive feedback and for bringing to our attention the missing information in our Methods section. We realized that the final two sections were inadvertently omitted during formatting changes before submission. These will be restored in the revised version.

We appreciate the reviewer's careful reading of this analysis and agree that the concern whether the decorrelation in figure 4 forces the model to unlearn the associations between pre- and post-onset activity is a valid one. To clarify, this is not what we intended to claim. Rather, our argument follows a different logic: if we assume that pre-onset encoding is purely a signature of predictive pre-activation, then decorrelating the pre- and post-onset brain responses should effectively remove that signature. The fact that pre-onset encoding remains largely intact after this procedure suggests that our initial premise was false; the observed pre-onset encoding is likely not a signature of pre-activation. We would also like to note that in this analysis, we use both residualized neural data and we use decorrelated embeddings. Therefore, the majority of stimulus dependencies are removed. Nevertheless, as the reviewer notes, some dependencies such as bi-grams and other word-co-occurrences, inevitably remain. These dependencies might explain the remaining pre-onset encoding we observed. This aligns with our main message of the paper. In the revisions, will provide a detailed description of the decorrelation process and we will make this interpretive logic more explicit in the main text.

Reviewer 3:

We are grateful for the reviewer’s detailed comments and for raising several points that will significantly improve the clarity and comparability of our study. Specifically, the reviewer’s feedback helped us realize that our evidence for postdiction required further clarification. While the encoding of the immediate preceding word ($d-1$) may involve recognition lags, we observe that word $d-2$ further improves the brain score even after the current word's onset, beyond what is explained by word $d-1$ alone. This may extend beyond simple recognition delays. To address this we will visualize this effect further in the upcoming version and expand the manuscript to include alternative explanations for this observation, such as extended lexical processing or integration delays.

To ensure our results are not biased toward high-frequency or function words, we will re-run our analyses including multi-token words. Given that these words constitute a small part of the datasets, we expect our core findings to remain stable.

In line with our response to reviewer 2, we will more clearly emphasize that despite our extensive controls, we cannot be sure that we accounted for all regularities inherent to natural speech.

Additionally, we will increase the context windows of the LLM to match the larger windows used in previous literature and add significance tests, error bars, and noise floor indications to our figures to ensure the reliability and variability of our findings are clearly communicated.

Author response:

Public Reviews:

Reviewer #1 (Public review):

(1) Completeness and clarity of Methods (Weakness #1).

We will substantially expand the Methods section to include:

(a) Detailed information on C. difficile strain ribotype 1382 (correcting the typographical error "1482"), including its virulence characteristics, toxin production dynamics, and rationale for its selection.

(b) Step-by-step protocols for on-chip bacterial quantification by flow cytometry, including sample collection volume, processing, and the specific normalization procedure (with clarification that normalized values are intended for within-experiment comparisons only).

(c) Full description of mouse experiments: antibiotic pre-treatment regimen, inoculation details (spores vs. vegetative cells, justification of the 1×10^9 CFU dose), animal numbers, housing conditions, and cage-effect considerations. The IACUC approval statement will be moved from Acknowledgments to Methods.

(2) Mucin layer characterization under anoxia (Weakness #2a).

We will clarify in the Methods that mucin staining was performed after the initial oxic culture phase to confirm differentiation prior to anaerobic challenge. We will cite relevant literature discussing the stability of pre-formed mucin layers under short-term anoxic conditions and incorporate this discussion to contextualize our experimental design in the revised Methods.

(3) Discrepancy in C. difficile counts and mechanism of LXA4 action (Weakness #2b, #3).

We will provide a detailed explanation of our flow cytometry normalization algorithm, emphasizing that values are only comparable within a given experimental batch. We plan to perform additional in vitro experiments to directly assess the effect of LXA4 on bacterial growth and toxin secretion. These data will help distinguish between direct antibacterial effects and host-mediated protection, and the revised Discussion will incorporate this analysis.

(4) Missing controls and experimental timelines (Weakness #2c–d).

We will clarify that Figure 4 presents gut-on-chip experiments, not animal studies. The corresponding methods will be fully described. Additionally, we will include cross-experiment alignment analyses (using the CDI group as a common reference) to integrate negative control data from separate experimental batches. We also plan to generate additional data examining the effect of LXA4 alone (without infection) on epithelial barrier integrity and inflammatory status, which will be included as supplementary controls.

(5) C. difficile strain characterization (Weakness #1g).

A comprehensive section on ribotype 1382 will be added to the Methods, detailing its in vitro growth kinetics, toxin production profiles, and disease dynamics in the murine model, with appropriate literature citations.

(6) Dysbiosis definition and phrasing adjustments (Other comments #b–d).

We will revise the text to provide a clear definition of dysbiosis in the context of CDI. We will also temper the phrasing in line 82 to more accurately describe the advantages of our GOC system relative to other in vitro models, and correct the description of C. difficile as an obligate anaerobe.

Reviewer #2 (Public review):

(1) Synergy between LXA4 and vancomycin in vivo.

We agree that the synergistic effect observed in the GOC model requires validation in an animal model. We are currently conducting mouse experiments to test the combination of prophylactic LXA4 with vancomycin treatment. The results will be included as a new Figure 5 in the revised manuscript.

We are confident that these planned revisions will fully address the reviewers' concerns and significantly enhance the rigor and impact of our study.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This paper presents a reanalysis of a large existing dataset to examine whether serial dependence effects-systematic influences of recent stimulus history on current perceptual judgments-are associated with generalization in perceptual learning. The central hypothesis is that extended, longer-range history effects (beyond the most recent trials) are beneficial for transfer across locations. The authors re analyze data from a texture discrimination task in which observers discriminated peripheral target orientation against a line background, with performance quantified by stimulus-onset asynchrony thresholds. Three training conditions were compared: a fixed single location condition, a two-location alternating condition, and a dummy-trial condition with frequent target-absent trials. Transfer was assessed after training at new locations. Serial dependence was quantified using history-sequence analyses and linear mixed effects models estimating bias weights across stimulus lags, with summary measures distinguishing recent (1-3 trials back) and more distant (4-6 trials back) dependencies.

The authors report extended serial dependence effects, persisting up to 6-10 trials back, with substantial cumulative bias that remains stable across multiple days of training and is not correlated with overall performance thresholds. Recent history effects are stronger for faster responses, suggesting a contribution from decision- or responserelated processes, whereas more distant effects decline within sessions, potentially reflecting adaptation dynamics. Critically, longer-range serial dependence is significantly stronger in training conditions that promote generalization than in the single-location condition. Individual differences in the strength and decay profile of distant history effects predict the magnitude of transfer across locations, whereas recent history effects do not. History effects are also correlated across trained locations, suggesting stable individual differences.

The authors interpret longer-range serial dependence as reflecting integrative processes that extract task-relevant structure over time, thereby supporting generalization, while shorter-range effects are attributed to more transient mechanisms such as priming or decision-level bias. The discussion connects these findings to Bayesian accounts of perceptual stability and to concepts of overfitting in machine learning.

The study offers a novel and thoughtful link between short-term serial dependence and long-term generalization in perceptual learning, helping bridge two literatures that are often treated separately. The large dataset enables robust estimation of individual differences, and the use of mixed-effects modeling appropriately accounts for variability across observers. The empirical distinction between recent and more distant history effects is well-supported and adds important nuance to interpretations of serial dependence. Converging evidence from both group-level comparisons and individuallevel correlations strengthens the central conclusions.

Several limitations should be addressed. First, the study relies entirely on previously collected data, without experimental manipulations designed to selectively isolate serial dependence mechanisms. Filtering choices, while theoretically motivated, may amplify history effects in ways that are difficult to quantify. Second, sequential dependencies can arise from multiple sources, including gradual updating of internal weight structures, adaptation processes, and history-dependent biases in decisionmaking. The current analyses do not clearly separate these contributions, limiting mechanistic attribution of long-range effects. Third, the conclusions are based on a single perceptual task, leaving open questions about generality across paradigms. Finally, while the discussion references computational ideas, no explicit modeling is provided to test whether plausible learning rules can jointly account for the observed history profiles and transfer effects.

We now address these issues in the manuscript (see below for detailed responses) and provide a toy model (supplementary material) where the observed effects are explained by simple learning mechanisms.

The findings align with theoretical frameworks that conceptualize perceptual learning as gradual reweighting of stable sensory representations at the decision stage (e.g., Petrov et al., 2005). Trial-by-trial updates in these models naturally give rise to sequential dependencies and sensitivity to training statistics. The observation that longer-range history effects predict generalization is consistent with broader temporal integration supporting more flexible learning, while narrower integration may lead to specificity. The results also indicate that multiple mechanisms - including decisionlevel biases and adaptation - may coexist with reweighting processes, highlighting the value of hybrid accounts.

In summary, this is a careful and data-rich reanalysis that highlights a potentially important role for serial dependence in enabling generalization during perceptual learning. While the underlying mechanisms remain underspecified, the evidence supporting the reported associations is strong, and the work provides a valuable empirical foundation for further experimental and modeling efforts.

Reviewer #2 (Public review):

This manuscript investigates how people's perceptual reports are influenced by events and trials in the past, and how this long-range dependence relates to broader learning across locations in a visual learning task. The authors present clear and internally consistent analyses showing that extended temporal integration is associated with greater generalization of learning. The study is thought-provoking and may contribute meaningfully to understanding how short-term influences and long-term improvement interact, although several interpretational points would benefit from clarification.

Strengths:

(1) The manuscript identifies unusually long-range perceptual biases extending up to ten trials back, which is a striking and potentially important finding.

(2) The association between strong long-range dependence and greater learning generalization is clearly documented and supported by consistent analyses.

(3) The dataset is large and rich, and the authors apply repeated and well-controlled analyses that give confidence in the stability of the effects.

(4) The writing is generally clear, and the manuscript raises interesting conceptual links between temporal integration and generalization of learning.

Weaknesses / Points Requiring Clarification:

(1) The manuscript repeatedly equates generalization with increased efficiency, but this relationship is not universally true. In some populations or tasks, excessive generalization can reduce task-specific efficiency. The authors should discuss this context-dependence to clarify when generalization is beneficial versus detrimental.

We agree with the reviewer that generalization does not strictly imply increased efficiency; in some contexts, over-generalization can indeed be detrimental. We now explicitly note in the Introduction that serial dependence can impair performance when stimuli vary randomly across trials. We have reviewed the manuscript to ensure we do not explicitly equate generalization with efficiency. Our argument is specifically that long-range SDEs support the transfer of learning (generalization).

(2) Serial dependence is also present, though smaller, in the central fixation task. It remains unclear whether this bias could contribute to the serial dependence observed in the main task. The authors should clarify whether the two biases are independent or whether the central-task bias might partially influence orientation judgments in the main task.

These two tasks are independent, one requires T/L discrimination the other V/H discrimination. See our detailed response below.

(3) Several figure captions and labels contain minor inconsistencies in formatting and terminology. Careful proofreading would improve clarity.

We thank the reviewer for pointing this out and have proofread the captions to improve formatting and terminology consistency throughout.

Reviewer #3 (Public review):

This reanalysis of a classic study of visual perceptual learning in a texture discrimination task convincingly demonstrates the presence of sequential dependence effects, commonly seen in response time analyses in 2-alternative tasks, on response accuracy in the texture task in the visual periphery and in a simultaneous central letter report at fixation. Overall, this paper provides a new and interesting analysis of the effects of sequential dependencies from trial to trial on performance, learning, and generalizability in perceptual learning.

Strengths:

This new analysis of sequential dependency effects (SDEs) extends commonly observed sequential effects in two-choice reaction times to accuracy and relates them to response accuracy during visual learning in a frequently used perceptual learning task. The paper makes a convincing case that different conditions known to impact generalization of learning to a second visual location also express quantitatively distinct n-back SDEs.

Weaknesses:

Most of the new analyses emphasize the effects of SDEs, including trials designed to enhance the size of the effects, specifically when the current trial is low visibility, and the prior trial is of high visibility. Unless there is an argument that learning and subsequent generalization primarily occur in low-visibility trials, the presentation should also include displays and an emphasized discussion of analysis for all trials, unfiltered.

We analyze effects on close to threshold (small-medium SOA) current targets preceded by above threshold (high SOA) reference targets. This is motivated by both technical issues and theoretical assumptions. In psychophysics, when using percent correct as a measure of performance, bias cannot be reliably estimated at or near ceiling performance, as correct responses leave little room for bias to manifest. Regarding the ‘easy’ targets used as a reference, having them at low SOA introduces uncertainty as for the reference orientation against which bias is measured, with their perceptual effect being ambiguous. Theoretically, we note that in perceptual learning with threshold targets, the introduction of clear targets in the absence of feedback enables learning (see Discussion, where we added: 'Most interestingly, in our experiments without feedback on the texture task, the experimental conditions yielding the strongest bias were also found to enhance learning in the absence of feedback (Liu et al., 2012)')

We have addressed this concern also by conducting additional robustness analyses with unfiltered prior-trial history. We analyzed data without the prior-visibility filter; results are presented in a new Supplementary Figure S3 and confirm our main findings (see addition to Methods: "Finally, to verify that our findings are not artifacts of these filtering choices, we also conducted control analyses including all prior-trial history regardless of visibility; these results are presented in Supplementary Figure S3 and confirm the robustness of our main findings.").

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) How manipulations of stimulus statistics, uncertainty, or feedback could selectively engage different forms of serial dependence

We expect serial dependence to be modulated by all these parameters. In classical SDT, stimulus statistics are known to affect response bias, as are temporal correlations in stimulation sequences. We note in the manuscript that we employed random sequences (50% chance for V and 50% for H targets), eliminating expectation-based biases toward either orientation. Stimulus uncertainty is known to increase serial dependence, as we also found here. Feedback is also expected to have an effect, the literature is somewhat ambiguous about this, but this may also depend on experimental design. We note that the main task studied here (TDT) had no feedback while the central T/L task did have feedback, both showing serial dependencies. In the manuscript we point to reviews of SDE where much of this is discussed.

(2) How explicit computational models could help distinguish decision bias from structural learning

We use the drift diffusion model (DDM) to distinguish decision bias (starting point in DDM) from structural learning (changes in drift rate). DDM predicts that decision bias is short lived, mainly affects fast reaction times (RT) while biases due to drift rate asymmetry persists to long RTs. We present these results in Figure 3.

(3) Whether similar relationships are observed in other perceptual domains

We are not aware of any other study linking serial dependence and perceptual learning or reporting such a link. We expect the link between long-range serial dependence and learning generalization to extend beyond the TDT (see new paragraph in Discussion). We hope this framework will motivate similar analysis in other labs where comparable datasets exist.

(4) How sensitive are the results to the filtering choices used in the analysis?

We analyze effects on close to threshold (small-medium SOA) current targets preceded by above threshold (high SOA) reference targets. This is motivated by both technical issues and theoretical assumptions. In psychophysics, when using percent correct as a measure of performance, bias cannot be reliably estimated at or near ceiling performance, as correct responses leave little room for bias to manifest. Regarding the ‘easy’ targets used as a reference, having them at low SOA introduces uncertainty as for the reference orientation against which bias is measured, with their perceptual effect being ambiguous. Theoretically, we note that in perceptual learning with threshold targets, the introduction of clear targets in the absence of feedback enables learning (see Discussion, where we added: 'Most interestingly, in our experiments without feedback on the texture task, the experimental conditions yielding the strongest bias were also found to enhance learning in the absence of feedback (Liu et al., 2012)')

We have addressed this concern also by conducting additional robustness analyses with unfiltered prior-trial history. We analyzed data without the prior-visibility filter; results are presented in a new Supplementary Figure S3 and confirm our main findings (see addition to Methods: "Finally, to verify that our findings are not artifacts of these filtering choices, we also conducted control analyses including all prior-trial history regardless of visibility; these results are presented in Supplementary Figure S3 and confirm the robustness of our main findings.").

Reviewer #2 (Recommendations for the authors):

(1) Clarify mechanisms underlying long-range serial dependence. Please better distinguish possible sources of serial dependence (e.g., decision bias, adaptation, reweighting) and clarify which interpretations are supported or remain ambiguous given the current analyses

Our manuscript discusses the mechanisms underlying the dissociation between recent and distant SDEs in the Discussion section. Specifically, we report that:

Recent SDEs are RT-dependent (stronger with faster responses) consistent with decision-level criterion shifts (Dekel & Sagi, 2020)

Distant SDEs are RT-independent consistent with neural reweighting/template updating

We also discuss the role of sensory adaptation in truncating long-range integration, supported by within-session decline of SDEs, reduced distant SDEs in the 1loc condition, and the original findings by Harris et al. (2012).

We have added an explicit acknowledgment that our correlational approach cannot definitively establish causality (see addition to Discussion: "While these converging findings support distinct mechanisms for recent and distant SDEs, our correlational approach cannot definitively establish causality, and targeted experimental manipulations would further strengthen these interpretations.").

(2) Test robustness to analytic choices

We have conducted robustness analyses by removing the prior-trial visibility filter. The results are presented in a new Supplementary Figure S3 and confirm that our key findings remain qualitatively unchanged (see addition to Methods referencing Supplementary Figure S3).

(3) Strengthen the computational link

We have expanded the Discussion to reference relevant computational models and specify predictions for future modeling work. We now cite Petrov et al. (2005). We provide a toy model implementing trial-by-trial template update that show SDE that is correlated with learning transfer. Importantly, in this model, long range SDE is a consequence of learning dynamics (see new paragraph in Discussion, and model simulation in supplementary material).

(4) Discuss generality and experimental tests. Briefly address whether similar effects are expected across other tasks or sensory domains, and outline experimental manipulations that could causally test the role of serial dependence in generalization.

We have added discussion of generality across perceptual domains and outlined the prediction that future work could test the SDE-generalization link in other tasks where both phenomena have been documented (see new paragraph in Discussion).

Reviewer #2 (Public Review - Point 2): Central task SDE independence

The SDEs observed in the central letter task and peripheral TDT are likely independent, as they involve different stimulus features (letter identity vs. orientation), different response mappings, and show distinct performance patterns across conditions. The absence of condition differences in central-task SDEs (described in the Results section under "SDE differences between conditions" end of paragraph), despite robust differences in TDT SDEs, further suggests that the peripheral orientation biases are not contaminated by central-task response tendencies. Note that the central task was fixed across conditions, stayed at fixation when location was changed, and when dummy trials were presented.

Reviewer #3 (Recommendations for the authors):

(1) Reference to Falmagne, Cohen, & Dwivedi (1975)

We have added this reference to the Introduction, acknowledging the historical foundation of sequential effects in perceptual decisions

(2) The SDE data of Figure 1 are (per the figure legend) from the 1 loc data of Harris et al., "pooled over all testing days", and filtered for trials with low-visibility current targets (SOA < SOA-threshold+20ms). Specify whether this threshold criterion is on a per-subject basis. State in the legend that "all testing days" includes Days 1-8 (4 days with the first location and another 4 days testing generalization to a second location).

We have revised the Figure 1 legend to clarify:

"Days 1–8; 4 days at the first location and 4 days at the second location to assess generalization"

"calculated on a per-subject basis"

(3) The leadup emphasizes that the analysis in the figure emphasizes trials where the effect is expected to be as large as possible (cited as 40 +/- 3%), while visible current targets (at n) biases were 5+/-1%.

See below, after (4).

(4) Unless a theoretical position associates learning just with low visibility (if so, explain), consider including two other panels showing the sequential dependencies for all trials, and the linear model weights over the last 10 trials for all trials.

We acknowledge that the main analyses emphasize conditions that maximize SDE expression. To verify robustness, we conducted control analyses including all prior-trial history regardless of visibility; these results are presented in Supplementary Figure S3 and confirm our main findings.

There are both theoretical and technical justifications for the filtering applied:

It is well known that learning, in particular without feedback (as in our TDT), is facilitated by a mixture of threshold level stimuli and suprathreshold easy trials (e.g., Liu et al., 2012).

Technically, it is impossible to measure bias with highly discriminable stimuli where performance is perfect or close to it, thus such trials are expected to dilute the measured effect. On the other hand, when considering serial effects from low sensitivity trials, we face an uncertainty involved in defining the actual orientation relative to which the bias needs to be computed.

(5) Figure S1 seems to indicate that average thresholds over all days (location 1 and location 2) are unrelated to the sequential dependence across subjects and that the amount of learning in location 1 is unrelated to the sequential dependencies across subjects in all the varied conditions. Since Figure S1 includes all 50 subjects, it includes some conditions with dummy trials interspersed. Clarify in the description whether the dummy trials are ignored for the purposes of the SDE analyses.

We have clarified in the Methods how trials are handled in the analysis: "To preserve the precise temporal structure of the data, all trials were included in the sequential n-back count across all experimental conditions, thus dummy trials were counted as time bins but their contribution was ignored. In the Linear Mixed Effects (LME) analysis, we modeled these trial types using distinct regressors: each n-back lag included separate predictors for visible and invisible targets, further differentiated by trial type (dummy vs. target) and relative location (ipsilateral vs. contralateral) where applicable. The SDE values reported here reflect only the influence of relevant target-present history trials; the effects of other history types (e.g., dummy trials), while estimated to ensure the temporal integrity of the model, are not presented."

(6) The conclusion from this analysis seems to be that the overall average threshold and the amount of initial learning are both uncorrelated with the strength of sequential dependencies across subjects. This conclusion should be added to the description in the main paper.

This finding is now discussed in the Discussion section, referring to the main Results section [ No significant correlation was found between biases and SOA thresholds across observers (r = -0.13, p = 0.37, average across days 1-8), nor between biases and improvements in performance at the first location (r = -0.09, p = 0.54, average across days 1-4), suggesting that the magnitude of serial dependence does not predict the overall amount of perceptual learning (Supplementary Figure S1)].

(7) Decay of SDE section clarifications

We have made the following clarifications:

RT definition: Added to Methods: "The reaction time (RT) used in the analysis was defined as RT(TDT) – RT (fixation task), where RT for each task was measured from stimulus onset."

N-back counting: Clarified in Methods (see response to point 5 above): all trials were included in the chronological sequence; the LME analysis assigned separate predictors at each lag for visible/invisible targets and for trial categories (dummy vs. target) and locations (ipsilateral vs. contralateral). The results reported do not include effects of dummy trial, except where response dependent SDE was reported (Fig 2a, SDE for response key).

2loc n-back effect: The longer-range effects in the 2loc condition likely reflect reduced adaptation allowing longer temporal integration, combined with the location-selective nature of SDEs.

RT and mechanism interpretation: The manuscript discusses that the critical observation is the qualitative difference in RT sensitivity between recent and distant SDEs, consistent with the drift-diffusion framework where criterion shifts are RTdependent while drift bias is RT-independent (Dekel & Sagi, 2020). We have added an acknowledgment of the correlational limitations of this interpretation.

Moving figures to supplement: We prefer to keep Figures 4 and 5 in the main text as they document important dynamics supporting our mechanistic interpretation.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Here, Pinto and colleagues set out to investigate whether the cow udder is a potential mixing site for the influenza virus. The authors have demonstrated that bovine mammary epithelial cells can be infected with both avian and human influenza A viruses, supporting the idea that the cow udder may be a potential site for reassortment. Furthermore, they demonstrate that the bovine-adapted IAV replicates to similar titers in avian epithelial cells when compared to an AIV precursor virus. Thus, suggesting there is no fitness trade-off, and confirms the potential for spill-back of the cattle B3.13 into poultry, which has already been observed. Overall, I believe the authors achieved their aims. However, there are instances in which the results do not entirely support the conclusions (noted in weaknesses). Given the ongoing questions surrounding highly pathogenic avian influenza A virus in dairy cows, this work provides valuable evidence for the potential of the cow udder as a site of reassortment. These findings highlight the need for surveillance of influenza A virus incursions into livestock species, particularly cows. Some specific strengths and questions regarding weaknesses have been outlined below.

Strengths:

(1) The authors use a diverse range of cell types and influenza A virus strains, as well as a wide range of techniques to address the questions at hand.

(2) The use of cells from multiple bovine breeds for the MAC-T, bMEC and explants suggests the phenomenon is not unique to a single breed.

(3) The results suggesting there is no fitness trade-off for Cattle Texas in an avian host are interesting, and confirm the potential for spill-back of the cattle B3.13 into poultry, which has been observed.

Weaknesses:

I have listed my complete questions/concerns below. However, there are two main weaknesses of the article in its current state. Firstly, there is no apples-to-apples comparison in terms of determining a preference for IAV to infect the cow udder over other organs (Q4). The mammary gland and respiratory tract are represented by epithelial cells, but for other organs, fibroblasts were chosen. I think the fairer comparison would be to compare epithelial cells from different organs to demonstrate a preference for the mammary gland. Secondly, the main premise of the article relies on bMEC and MAC-T (primary and immortalised mammary epithelial cells), facilitating higher viral growth than the cells from other organs. Yet throughout the article, a 10x higher dose of IAV is used in the bMEC cells compared to everything else (Q6). This raises the question of how much of the results are due to a preference for the mammary epithelial cells, and how much is simply due to the increased dose.

When we set out to test if cow mammary gland cells were particularly susceptible to IAV infection compared to other bovine cell types, we used what was available in the Roslin Institute in the first instance – a mix of primary and continuous cells from various anatomical sites: three epithelial cell types (two mammary, one respiratory tract) two immune cell types and four sets of fibroblasts from various organs. Given the representation of different anatomical sites, cell types and differentiation statuses, we considered this a suitably diverse panel with which to characterise infection dynamics of a broad range of IAVs, before more focussed investigations using the mammary bMEC and explant tissues. Both mammary epithelial cell types grew our library of influenza challenge strains significantly better than the BAT-II respiratory epithelial cells, as well as the two immune cell types and all four fibroblast populations. Of the fibroblast cells, those derived from the brain grew IAV significantly better than the skin and turbinate fibroblasts, while blood-derived macrophages grew virus significantly better than the lymphocytes and non-brain fibroblasts. Therefore, there are “apple to apple” comparisons as well as apple to pear comparisons that give significant differences. We therefore think that our conclusions (in the abstract) that mammary cells are particularly replication competent for IAV, (at the end of the introduction) that “a wide range of cow-derived cells are susceptible” and that (in the results section) that “mammary cells showed the highest susceptibility” are entirely justifiable. We do not claim that mammary cells are the only permissive bovine cells, but our evidence suggests they are highly susceptible.

We used a higher MOI for bMECs because test experiments with WT PR8 and the Cattle Texas 6:2 reassortant showed that MOI 0.01 infections gave more variable results than ones run at MOI 0.1, perhaps because of the intrinsic variability of mixed primary cell populations. We therefore chose to go with the higher MOI. However, the end-point titres between the two conditions were not significantly different, so we do not think this choice is a confounding issue. We will add the comparison of the two MOIs as a supplementary figure in the formal revision.

Reviewer #2 (Public review):

The authors use a library of influenza A viruses from different strains, classified in lab-adapted, human, avian, and swine according to the animal from which they were isolated. They propose that the cow mammary gland serves as a mixing vessel for influenza A viruses. As a first approach, the authors assess susceptibility to infection across different cell types, including continuous and primary cell lines, bovine mammary cells, and mammary explants. All these cells support polymerase activity. Then, they analyzed changes in the bovine virus's viral fitness relative to an avian precursor. The authors use single-gene replacement to study whether and which RNP segments improve viral transcription. As part of this section, they also test IFN-specific antagonism by NS1 to assess the input of segment 8. Quantitative glycomic analysis was performed on the continuous bovine mammary cell line to demonstrate the presence of both a2,3 and a2,6, which is consistent with their observation that these cells can be co-infected with human and avian IAVs simultaneously. The main question, however, is: what is the glycome in the explants, or directly from tissues?

We report quantitative glycomics for the primary bovine mammary epithelial cells as well as the continuous line the referee highlights. However, we agree with R2 that a detailed glycomic analysis of primary bovine mammary tissue would allow a better understanding of the actual glycosylation status in vivo. This has now been undertaken by the authors and is available as a bioRxiv preprint:

Bovine H5N1 influenza viruses have adapted to more efficiently use receptors abundant in cattle

Jack A. Hassard, Jiayun Yang, Bernadeta Dadonaite, Jonathan E.Pekar, Jin Yu, Samuel A. S. Richardson, Rute M. Pinto, Kristel Ramirez Valdez, Philippe Lemey, Jessica L. Quantrill, JinghanXue, Tereza Masonou, Katie-Marie Case, Jila Ajeian, Maximillian N. J. Woodall, Rebecca A. Ross, Nicolas Hudson, Kan Zhong, Hongzhi Cao, Samuel Jones, Hannah J. Klim, Brian R. Wasik, Desi N. Dermawan, Jean-Remy Sadeyen, Dirk Werling, DylanYaffy, Joe James, Alessandro Nunez, Paul Digard, Ian H. Brown, Daniel H. Goldhill, Pablo R. Murcia, Claire M. Smith, Yan Liu, Jesse D. Bloom, Munir Iqbal, Wendy S. Barclay, Stuart M.Haslam, Thomas P. Peacock: bioRxiv 2026.04.02.715584; doi:https://doi.org/10.64898/2026.04.02.715584

Overall, the manuscript is clearly written and provides new insights into the behaviour of the cattle isolate, now compared with a representative group of model or precursor HAs of different origins.

It would be great if a consistent nomenclature for the IAV strains could be used in the study. There is a mix of origin (Texas), animal from which the virus was isolated (mallard), or abbreviations that do not follow guidelines (IAV07). Are the USSR and Udorn not lab-adapted?

We chose the abbreviated names for a variety of reasons. Partly from common usage (e.g. PR8, Udorn), partly for consistency with other already published papers from the FluTrailMap consortia (e.g. Cattle Texas; Dholakia et al 2026), partly to make diversity obvious in certain figures (e.g. H3N1, H5N2 etc) and partly to avoid confusion between viruses that originate from the same geographic area (e.g. AIV07, AIV09, H5N8-20 etc which are all Ck/England/isolate numbers). Overall, we found it more confusing to use the expanded nomenclature. Re AIV07 which the referee criticises for not following naming guidelines – if this is a reference to the EURL nomenclature, AIV07 is the abbreviation for the specific virus A/Chicken/England/053052/2021, our representative virus for EURL genotype EA-2020-C, as we say in the text. We should however have included this nomenclature in Table 1, which otherwise provides a cross-reference for all the names. This will be added in the formal revision to help with clarity.

As to whether USSR and Udorn are lab adapted – that depends on definitions. There is a continuum of adaptive changes and/or sequence drift starting from the very first growth of an isolate in the laboratory. The viruses we define here as lab adapted are ones that have been deliberately adapted to other hosts or which have very long passage histories in multiple host species resulting in known functionally significant changes. For example, PR8, with 100s of passages in mice, ferrets and embryonated hens eggs (doi: 10.3390/v12060590), makes it unarguably lab-adapted. We admit that A/USSR/77 and A/Udorn/307/1972 are probably further along this adaptive pathway than more recent isolates such as A/Norway/3433/2018, but are unaware of any specific reason that would put them into our lab adapted category.

The experimental setup includes bovine mammary primary and continuous cells, as well as mammary explants. Some of the most significant differences, for example, in viral fitness studies and co-infection experiments, are observed in these explants. Perhaps there could be some additional focus on this observation. The implications in comparison to the results obtained in cultured cells could be described. How will the human and other HA subtype viruses fare in the explants?

We agree that this is an important and interesting question, and have tested the strains we used for co-infections, human seasonal H1N1 “Norway” and low pathogenic avian influenza “H3N1”, in the mammary explants. Both replicate, the avian virus to 20-fold higher titres. We will add this new information to the revised manuscript.

Reviewer #3 (Public review):

Summary:

This excellent manuscript by Pinto, Sharp, and colleagues examines bovine tissue tropism for influenza viruses. They find that bovine flu, as well as other strains, has strong replication in mammary tissue. They also map the genetic changes to influenza that improve replication in bovine cells. Overall, the study is well designed and executed, and the results are very timely.

Strengths:

(1) The experiments are well-controlled.

(2) The figures are well-constructed and easy to follow.

(3) The Methods and legends are detailed, with sufficient information.

Weaknesses:

(1) A comparison to human cells would strengthen the overall impact of the results. Are human mammary cells also uniquely susceptible to influenza? Are bovine mammary cells special in some way?

This is an interesting question but we have not tested mammary gland cells from humans (or any other species of mammal), but we have reported elsewhere (Dholakia et al., Nat Commun. 2026 Jan 16;17(1):1603. doi: 10.1038/s41467-026-68306-6.) that Cattle Texas grows well in a variety of human respiratory cells. Here we are considering the bovine mammary organ as a potential reassortment site for IAVs; human mammary organs are unlikely to create this opportunity.

(2) For the virus infection studies with segment 8 swaps, it should at least be noted that some of the phenotypes could be driven by NEP.

We agree, and will change the text to acknowledge this in a revised version.

(3) The data demonstrating that bMEC can support co-infection are compelling and important, but would be strengthened with a comparison from a different cell type or species. Do mammary cells uniquely support higher co-infection?

We have data showing that co-infection also occurs in the continuous MAC-T udder cell line and will include these data in a revision. We have not tested bovine cells from other organs for co-infection potential as they do not seem to be significant sites of infection in vivo.

Author response:

We sincerely thank the Reviewing Editor, Senior Editor, and both reviewers for their careful and constructive assessment of our manuscript. We are encouraged that the reviewers recognize the value of our dataset and its potential contribution. We greatly appreciate the thoughtful comments and have carefully considered the reviews. We plan to revise the manuscript accordingly. 

First, we will revise and refine the cross-species comparative analysis, with particular attention to clarifying the basis of the comparisons between ascidian and mouse endodermal lineages. In particular, we will adopt a more cautious and precise comparative framework, clarify the scope and limitations of the mouse comparison, and broaden the context by incorporating additional vertebrate and invertebrate deuterostome systems where relevant.

Second, we will strengthen the gene-level interpretation of the identified endodermal populations and clarify the molecular basis for the similarities and differences. In particular, we will more clearly identify the key marker genes defining each population, better explain their relationship to previously described developmental sources. 

Third, we will improve the clarity of the Results presentation, including the description of the two major endodermal progenitor populations and their subcategories, as well as the organization of the text, figures, and figure legends. 

Fourth, we will substantially rewrite the Discussion, especially the sections dealing with evolutionary implications, to ensure that our interpretations are presented in a more cautious manner.

These revisions are intended to address the reviewers’ concerns regarding both the evolutionary framing and the presentation of the data. We believe that these revisions, which will include both rewriting and additional analyses, will improve the clarity and rigor of the manuscript. We look forward to submitting a revised version.

We thank the editors and reviewers again for their time and expertise.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their manuscript, Andriani et al. show intracellular zinc is exported from sperm during capacitation and suppresses the alkalinization-induced hyperpolarization in sperm. Intracellular zinc inhibits Slo3 current, which is enhanced by the co-expression of gamma subunit Lrrc52. Computational studies reveal that the Zn binding site on mSlo3 is located near E169 and E205, which are involved in the sustained zinc inhibition of mSlo3 current. The authors propose that intracellular zinc plays a key role in sperm capacitation by inhibiting the Slo3 channel.

Strengths:

Overall, the work appears well-designed (e.g., oocyte patch-clamp experiments), and clearly presented. Three-dimensional structural modeling and flooding simulations are executed.

Weaknesses:

The simple mutagenesis analysis of E169 and E205 showed partial abolishment, but the molecular mechanism by which zinc inhibits Slo3 current is not yet fully shown. The authors should consider performing more extensive experiments, such as creating double mutants or combination mutants involving other residues. Additionally, could other mechanisms explain the role of zinc in regulating the Slo3 current?

We thank the reviewer’s thoughtful comments regarding the mutagenesis analysis and the possible mechanisms underlying zinc regulation of Slo3. Regarding the suggestion to perform double or combination mutants, we agree that such experiments would provide valuable mechanistic insight. However, due to limited resources, we were not able to perform these additional experiments within the scope of this study. Our current results show that mutations at E169 and E205 partially abolish zinc inhibition, which suggests that the inhibitory mechanism is not mediated through a single residue and is likely more complex.

Alternative mechanisms that may contribute to zinc modulation of Slo3 include indirect effects through modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites within Slo3 channel other than the sites discovered through this study. At present, these mechanisms remain speculative and further studies will be required to clarify their contributions. This study provides the foundational basis for understanding how zinc inhibits the Slo3 channel and serves as an important starting point for defining the molecular mechanism in more detail.

We already acknowledged in the Discussion section that the precise molecular basis of zinc inhibition remains unknown and that future work involving more extensive mutational and structural analyses will be essential to fully resolve this issue.

We also added the discussion section as follows:

“It is worth noting that the incomplete loss of zinc sensitivity in these mutants suggests that additional mechanisms may participate in zinc modulation of Slo3. These may include modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites. Comparisons with Slo2.2 (J. Zhang et al., 2023), KCNQ4 (Gao et al., 2017), and voltage-gated calcium channels (Sun et al., 2007) further support the possibility of diverse molecular determinants for zinc inhibition. Our VCF, mutagenesis, and simulation data together indicate that zinc influences voltage sensor movement in mSlo3, which may suggest a distinct inhibitory mechanism that warrants further investigation.”

While elucidating the mechanism of Slo3 is interesting, there is substantial literature indicating how zinc regulates channel functions at a molecular level. Given this, the manuscript should provide a deeper understanding by clearly elucidating the molecular mechanism of the regulation of Slo3 current by zinc.

Thank you for highlighting a very important point that requires deeper discussion and explanation regarding how zinc regulates Slo3 current at the molecular level. As reported, Slo3 is gated by membrane depolarization and, at the same time, this channel is also gated by intracellular pH, particularly alkalinization (Leonetti et al., 2012; Schreiber et al., 1998; X. Zhang et al., 2006). This makes the gating mechanism of this channel complex. The molecular mechanism underlying pH regulation of the Slo3 channel remains unknown (M. D. Lyon et al., 2023). We tested different pH conditions and membrane voltage to elucidate the effect of zinc on the Slo3 channel. Our data suggests that zinc inhibition in mSlo3 channels is dependent on pH (Fig. 2A-E), voltage (Fig. 2G-H; Fig.2—figure supplement 1A, B) and exhibits a long-lasting inhibitory effect (Fig. 2I, K).

However, as much as we are aware that these data alone cannot explain the molecular mechanisms of zinc’s effect on Slo3 current, our mutagenesis experiments also did not provide a straightforward answer. The single amino acid mutations examined in this study, which contain clustered negative residues, did not significantly alter zinc-mediated current reduction compared to the wild type. As the reviewer pointed out, mutating one single amino acid may not be sufficient to fully identify other contributing residues within the predicted mSlo3 zinc-binding site. Therefore, more extensive mutagenesis studies will be required to fully elucidate the molecular mechanism of zinc inhibition in mSlo3, which could not be fully understood in this study.

On the other hand, when we analyzed the percentage of current recovery of all the mutants, E169A and E205A showed significant current recovery upon the wash-out by pH 8.0 alone. Consistent with MD simulations, our electrophysiological recordings demonstrated that the long-lasting inhibitory effect of zinc was partly abolished by these mutations. Thus, our findings highlight the contribution of E169A, located at the lower end of S3 domain and E205A, located at the lower region of S4 domain, to zinc-mediated inhibition of mSlo3 current.

Additionally, since the molecular mechanism of pH regulation on Slo3 channel remains unknown, the molecular basis of its dual gating has yet to be elucidated, making it difficult to draw a single definitive conclusion from our current research data on how zinc inhibits mSlo3 current. Nevertheless, this study provides the foundation for understanding possible mechanisms of zinc inhibition. Our VCF data suggest that zinc influences the movement of VSD of mSlo3, and together with our mutagenesis and MD simulations results, these findings represent an important first step toward elucidating the molecular mechanism of zinc inhibition of the mSlo3 current.

Intracellular zinc exerts inhibitory effect on mSlo3, similar to what has been reported for Slo2.2 channels (J. Zhang et al., 2023), high- and low-voltage activated calcium channel families (Sun et al., 2007) and KCNQ4 channels (Gao et al., 2017). These studies identified different regions, amino acids, and possible mechanisms of zinc inhibition among these ion channels. For instance, in Slo2.2 channels, which belong to the same Slo family as Slo3, the zinc-binding site was identified in the RCK2 domain, where cysteine and histidine residues form a canonical zinc binding motif (J. Zhang et al., 2023). In KCNQ4 channels, zinc inhibits the channel activity in a non-canonical manner that depends on its physiological activator, the membrane lipid PI(4,5)P₂ (Gao et al., 2017). Although zinc exerts the inhibitory effects on those various voltage-gated potassium and calcium channels, the mechanisms differ. Our data suggests another distinct mechanism of zinc inhibition in the mSlo3 channel with the identified sites located in the VSD, where zinc influences the voltage-sensor motion, and consequently affects the complex gating of Slo3.

We revised the discussion section as follows, which is also related to the previous comment:

“It is worth noting that the incomplete loss of zinc sensitivity in these mutants suggests that additional mechanisms may participate in zinc modulation of Slo3. These may include modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites. Comparisons with Slo2.2 (J. Zhang et al., 2023), KCNQ4 (Gao et al., 2017), and voltage-gated calcium channels (Sun et al., 2007) further support the possibility of diverse molecular determinants for zinc inhibition. Our VCF, mutagenesis, and simulation data together indicate that zinc influences voltage sensor movement in mSlo3, which may suggest a distinct inhibitory mechanism that warrants further investigation.”

The manuscript includes no experimental data on the mechanism of intracellular zinc export during sperm capacitation, despite being crucial for the regulation of sperm function.

We thank the reviewers for the valuable comment in this regard. We agree that mechanism of intracellular zinc export during capacitation is crucial for the regulation of sperm function, and it would be an important finding if we could provide the experimental data on this. However, there are significant technical difficulties in performing such experiments. Two protein families facilitate the transport of zinc across cellular and intracellular membranes in opposite directions: ZnT and ZIP. ZIP12 has been reported to be highly expressed in mouse testis (Zhu et al., 2022), as well as ZnT-1 (Elgazar et al., 2005). To date, there are no known inhibitors for zinc transporters, and there is also no suitable antibodies available for these transporters, which makes it difficult to design experiments to examine the intracellular zinc transport during sperm capacitation. Apart from the two reported zinc transporters, the functional significance of other ZnTs and ZIPs, particularly those related to capacitation, remains largely unclear, leaving the mechanisms of zinc transport in sperm during capacitation poorly understood. Moreover. homozygous Znt-1 knockout mice exhibit a lethal phenotype (Andrews et al., 2004).

Reviewer #2 (Public review):

Summary:

In this paper, Andriani and colleagues are examining the potential role of Zn flux in sperm and its effect on Slo3 channels. This is an interesting question that is likely critical to how sperm function properly and Slo3 channels are a possible candidate for a downstream molecule that is impacted by Zn. In this paper, the authors use Zn imaging, sperm motility assays, and electrophysiology to show that Zn flux impacts sperm function. They then go on to look at the impact Zn has on Slo3 current and propose a binding site based on MD simulations. While the ideas are interesting, the experiments are not well described in many places making understanding the results very difficult. In addition, critical controls are missing throughout the paper.

Strengths:

The question of how Zn flux impacts membrane potential and sperm motility is an important one. Moreover, Slo3 presents an interesting candidate or the target of Zn regulation. The combination of methods used here also has the potential to uncover mechanisms of Zn regulation of Slo3.

Weaknesses:

Much of the paper lacks experimental description which makes interpretation quite difficult, or a detailed discussion is missing. Examples include:

(1) Figure 1, particularly the Zn imaging, is not sufficiently described. How is the fluorescence intensity measured? A representative ROI? The whole tail and head? Are the sperm immobile? If not, there is evidence that motion artifacts can significantly distort these sorts of measures from Calcium measurements in Cilia. Were there controls done? Is the small amount of Zn seen in the tail above the background?

We sincerely thank the reviewer for pointing out important details that we should provide in this study in order to make it well understood. We would like to answer and respond to the points raised by reviewer as follows:

Fluorescence intensity is measured by the signal taken from the whole head and the proximal part of tail in sperm. We have included this in the materials and methods.

Materials and Methods

“Fluorescence intensity is measured by the signal taken from the whole head and the proximal part of tail in sperm.”

Yes sperm is immobile during zinc imaging.

We added the control data of zinc imaging without capacitation medium and incorporated the data into the graph in Figure 1B. For the control in non-capacitation medium, we use HS medium as newly explained in the methods, results, related figure (Figure 1B), and figure legends.

Yes the small amount of Zn seen in the tail above the background. As shown in Fig. 1A we confirmed that the signal intensity at the proximal region of the tail was higher than the background. Therefore, the data for this region were calculated after background subtraction.

(2) The second half of Figure 1 is also not well described. What is the extracellular solution in the recordings? When you apply the Zn ionophore, do you expect influx or efflux? I assume efflux is based on the conclusions but this should be discussed explicitly.

The extracellular solution in the recordings for Figure 1 is HS solution (HEPES-buffered saline solution), a standard non-capacitation medium. We will include this information in the materials methods.

Materials and methods

“HS-based solution was used as the extracellular solution.”

We assume that intracellular zinc levels increase upon application of zinc ionophore. Previous work has reported that sperm contain approximately 35.7 ng/10⁶ cells in the head and flagellum (Henkel et al., 1999). When zinc pyrithione is applied, it facilitates the influx of Zn²⁺ from the surrounding medium into the cell, thereby increasing intracellular zinc concentration. Zinc pyrithione functions both as a zinc source and as a transport facilitator, allowing Zn² to cross the otherwise impermeable lipid membrane without compromising membrane integrity.

(3) Figure 2H labels the Y axis, "normalized current". Normalized to what? Why do neither of the curves end at 1? A better description of what this figure represents is needed.

Normalization for figure 2H was performed by dividing the absolute current of mSlo3 at pH 8.0 of each voltage by the absolute current at the pre-determined highest voltage that still produced a stable mSlo3 current (i.e., good patch, good clamp). In this analysis, +140 mV was chosen as the highest voltage for normalization, since in few cells the patch was lost at +160mV and +180mV. Similar to the control condition, the absolute current of mSlo3 in the presence of 100 µM zinc was normalized to the absolute current of the control at +140 mV. This information has been included in the figure legends and the Materials Methods section of the revised manuscript.

Materials Methods section:

Figure legends for figure 2H has been updated.

(4) The alpha fold simulations are not well described. How many Zn binding sites were found? Are all of the histidine mutations in Figure 4 Supplement 1 the ones that were found?

We thank the reviewer for the question. In our AlphaFold3 input, we only input the transmembrane region of the protein. From there, we found four sites located as follows:

Given that we are only interested in the intracellular side of the membrane, we are only interested in the site with the highest pLDDT value (confidence values). On the IC side, there are only two sites, where the other sites are located near the pore domain. The site is near E310 and K319.

Author response image 1.

AlphaFold3 prediction of the Zn binding site on IC side of Slo3

The histidines in Fig. 4—figure supplement 1 are all histidines that are not in the transmembrane region. These residues were not included in the initial inputs for AlphaFold3. However, we conducted MD simulations including these residues and we were able to show that a few of these residues are in contact with Zn. We have now plotted the minimum distance between each of these residues and Zn in the flooding simulations.

Author response image 2.

MD simulations of histidines residues located in IC of Slo3

Minimum distances between histidines in Fig. 4—figure supplement 1 and Zn²⁺ from the flooding simulations. Different colors indicate different repeats.

(5) There is no discussion of physiological intracellular Zn concentration. How much Zn is inside the sperm? How much if likely Free vs buffered? Is 100uM a reasonable physiological concentration?

We estimated the intracellular zinc concentration in sperm based on human sperm data, which report a zinc concentration of approximately 35.7 ng/10⁶ cells in the head and flagellum (Henkel et al., 1999). Considering the volume of a typical human sperm is about 15 µm³ (Laufer et al., 1977), this translates to an estimated intracellular zinc concentration of approximately 400 mM, although the concentration of free zinc must be much lower than this level. Although exact intracellular zinc concentrations in mouse sperm are not well-documented, this estimate supports the observation of elevated zinc in non-capacitated sperm.

There are a number of areas where the interpretation is not well supported by the data including:

(6) You say in the Figure 4 supplement, that "we did not observe any significant decrease in the percentage of current inhibition." But that is a pretty misleading statement. There are large changes (increases) in the amount of zinc inhibition. These might be allosteric changes but I don't think you can safely eliminate these as relevant Zn binding sites. Also, some of these mutations appear to allow at least some unbinding of Zn.

In our MD simulations, H720 is not at the zinc binding site and therefore, mutation to arginine would indeed eliminate its binding. We are showing this in the minimum distance analysis between Zn and H720 and show that they are further than 4 Å from each others (n=3), as shown in author response image 2.

Chimera of Slo3/Slo1 RCK2 also showed large increases in the amount of zinc inhibition, and this might serve as a potential binding site. We agree that the statement: “we did not observe any significant decrease in the percentage of current inhibition.” is misleading, therefore we revised our interpretation and statement into:

We revised the result section as follows:

“However, the percentage of current inhibition varied across the mutated constructs, showing either increases or no appreciable change (Fig. 4—figure supplement 1B, C).”

(7) Following up on the above point, it seems unfair to conclude that the D162S, E169A, and E205 mutants are part of the inhibitory binding site for Zn when the mutation has no effect on inhibition and only an effect on the washout. The mutations on the intracellular side also had an impact on the washout so it seems equally likely that they are the critical residues based on your data.

We thank the reviewer for this important point. We agree that the absence of a strong reduction in the initial zinc inhibition makes it challenging to assign any single residue as a definitive zinc binding site. However, our interpretation is based not only on the electrophysiological data but also on the MD simulations, which consistently identified E169 and E205 as residues that frequently interact with zinc and stabilize zinc occupancy within the VSD region. Although the mutations did not markedly reduce the peak level of zinc inhibition, both E169A and E205A significantly altered the long-lasting inhibitory component during washout, which is consistent with the MD-predicted interactions. In contrast, the intracellular mutations affected washout but were not supported by MD simulations as potential zinc interaction sites. Taken together, these combined datasets support the idea that E169 and E205 contribute to zinc modulation of Slo3 in the VSD, even though additional residues or mechanisms are likely involved.

(8) Nowhere in the paper do you make the specific link between Zn flux and membrane hyperpolarization via Slo3. You show that Zn flux changes the ability of the sperm to hyperpolarize and you show that Slo3 is inhibited by Zn but the connection between the two is not demonstrated. There appears to be a specific Slo3 blocker. If you use this in sperm, do you no longer see the Zn effect?

Thank you for pointing out the need for clarifying this point. It is already known that sperm capacitation is well associated with the increase of intracellular pH (Vredenburgh‐Wilberg & Parrish, 1995; Y. Zeng et al., 1996), the hyperpolarization of the membrane (Arnoult et al., 1999; Y. Zeng et al., 1995) and the elevation of intracellular Ca²⁺ concentration level (Breitbart, 2002; Publicover et al., 2007) through diverse ion channel activities. To explore whether these pathways are influenced by intracellular zinc, we used patch-clamp techniques to measure the membrane potential (Vm) as shown in Fig. 1D-K. It has been reported that under the whole-cell current clamp of mouse epididymal spermatozoa, resting membrane potential is hyperpolarized after intracellular alkalinization (Navarro et al., 2007). We mentioned this in line 100-108 in the manuscript.

Next, our findings from the experiments using mouse spermatozoa suggest that intracellular zinc inhibits a key process in sperm capacitation, specifically the alkalinization-induced hyperpolarization. Previous studies have identified the pH-and voltage-dependent potassium channel Slo3 is responsible for the principal K⁺ current (I_KSper) in mouse spermatozoa (Navarro et al., 2007; Santi et al., 2010; Schreiber et al., 1998; X. H. Zeng et al., 2011). During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010). Given this context, we next investigated whether intracellular zinc acts directly on the Slo3 channel and found that zinc inhibits mSlo3 current. We explained this rationale of the experiment in line 143-150.

We add following sentence to add more clarity to the text:

“During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010).”

Therefore, the text was modified into:

“Our findings suggest that intracellular zinc inhibits a key process in sperm capacitation, specifically the alkalinization-induced hyperpolarization. Previous studies have identified the pH-and voltage-dependent potassium channel Slo3 is responsible for the principal K⁺ current (I_KSper) in mouse spermatozoa (Navarro et al., 2007; Santi et al., 2010; Schreiber et al., 1998; X. H. Zeng et al., 2011). During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010). Given this context, we next investigated whether intracellular zinc acts directly on the Slo3 channel.”

Regarding the specific inhibitor, as has been pointed out by the reviewer that a new Slo3 inhibitor, VU0546110, exhibited more than 40-fold selective for human Slo3 over Slo1 (M. Lyon et al., 2023). However, the effect of VU0546110 in mSlo3 has not been tested yet. Both mouse and human Slo3 exhibit similar responses to certain inhibitors, but mouse and human Slo3 is also differ in their responses to several other inhibitors (M. D. Lyon et al., 2023), making it uncertain if this VU0546110 will work on mSlo3.

(9) In the second half of Figure 1, the authors suggest that there is "no hyperpolization in 100uM Zn. That is not really true. It is reduced but not absent.

We modified the wording of “no hyperpolarization in 100 µM Zn” to “alkalinization-induced hyperpolarization was reduced in the 100 µM ZnCl₂ group.”

“In contrast, alkalinization-induced hyperpolarization was reduced in the 100 µM ZnCl₂ group”

(10) The claim that Lrcc52 with Slo3 shows a higher current inhibition at pH 7.5 than pH 8 is not well supported because there are only 3 replicates in the 7.5 case. In addition, the claim is made in the test that 100uM ZnCl2 "already inhibited mSlo3+Lrcc52 at pH7.5", contrasted with mSlo3 alone, is not tested statistically.

Thank you for the valuable comment. Although Fig. 3F shows a statistical difference, we agree that having only three replicates at pH 7.5 may somewhat weaken the conclusion. Following this suggestion, we have revised the sentence as follows:

“Alkalinization appeared to increase the percentage of current inhibition by 100 µM ZnCl₂.”

We provided statistical analysis to compare pH 7.5 between mSlo3 alone and mSlo3+Lrrc52 in the Figure 3—figure supplement 1D:

The statistical analysis showed that 100 µM zinc significantly inhibited the mSlo3 + Lrrc52 current at pH 7.5 compared to the mSlo3 current alone. We have incorporated the necessary changes into the revised manuscript and updated the figure legends accordingly.

In a number of places, better controls are needed.

(11) How specific is this effect for Zn? Mg2+, for instance, is also a divalent cation that is in the hundreds of uM range inside the cell. Does it exert the same effect? Each ion certainly has unique preferred coordination geometries, does your predicted binding with MD show what you might expect for tetrahedral coordination with Zn? Did you test other divalent cations functionally or in silicon?

To answer this question, we have tested this by building another AlphaFold3 model, with Mg²⁺ instead of Zn²⁺. We did not opt for the all-atoms MD simulations due to the cost of the simulation. Here, the model shows that Mg are all clustered at the pore domain and does not reside anywhere near the Zn²⁺ site from both MD simulations and the AF3 model.

Author response image 3.

AlphaFold3 model of Slo3 channel with Mg²⁺

The Slo3 AlphaFold model from residue M1 to L330. The colour gradient reflects the pLDDT score range from 1.73 to 95.69. Purple sticks highlighted E169, N171 and E205. In this study, we did not examine other divalent cations in our electrophysiological recordings. Exploring their effects will be an important direction for future research.

(12) For the VCF experiments, a significantly higher concentration of Zn was used (10mM). What is the reason for this? There is no discussion of how much a "puff" is. Assuming you are using the RNA injector it is probably on the order of 50nL or less. Assuming the volume of an oocyte is 1uL that would argue that the final concentration is 500uM or higher. But this is also complicated by potential local effects of high Zn at the injection site, artifacts of injecting that much metal, and the fact that a great deal of the Zn will likely be bound to other things inside the cell. Better controls are needed for this experiment.

As pointed out by the reviewer, the volume of the oocytes is estimated to be approximately 1 µL. We performed manual injections using glass needle typically used for RNA injection. However, because the injections were done manually during real-time VCF recording (as illustrated in the experimental scheme), the exact volume of the solution injected into each oocyte could not be precisely controlled. We estimated that each drop to be approximately 50 nL, resulting in a final concentration around 500 µM, as described by the reviewer.

The rationale for using relatively high concentration was to ensure that the zinc concentration inside the oocyte reached an effective level, since manual injection may sometimes deliver less than 50 nL of solution. In some cases, injections failed entirely due to the technical difficulty of the method. Because VCF recordings are already technically difficult, we aimed to ensure that zinc injection was successful in oocytes that exhibited robust fluorescence signal by injecting an excess amount of zinc that would not disrupt normal oocyte conditions. For example, 10 mM zinc was prepared in an acidic solution (pH 2.5). We verified that this acidic condition did not affect mSlo3 current by performing control injections with the acidic solution alone, since the mSlo3 current is not activated under acidic pH conditions

Author response image 4.

VCF control experimentes: vehicle injection.

Reviewer #3 (Public review):

Summary:

The study titled "Zinc is a Key Regulator of the Sperm-Specific K+ Channel (Slo3) Function" aims to investigate the role of intracellular zinc in sperm capacitation and its regulation of the sperm-specific Slo3 potassium channel. Capacitation is a crucial physiological process that enables sperm to fertilize an egg, and membrane hyperpolarization through Slo3 activation is a well-established event in this process. The authors propose that intracellular zinc dynamically decreases during capacitation and inhibits Slo3-mediated K⁺ currents, thereby playing a regulatory role in sperm function.

Strengths:

(1) Novel Contribution to Sperm Physiology.

The study provides new insights into how zinc dynamics contribute to sperm capacitation, specifically through its direct inhibition of Slo3 activity.<br /> Previous research has focused primarily on extracellular zinc's effect on sperm function; this work expands the discussion to intracellular zinc regulation, an area with limited prior investigation.

(2) Strong Electrophysiological Evidence.

The study employs inside-out patch-clamp recordings in Xenopus oocytes to demonstrate zinc's direct inhibition of Slo3 currents. The observed slow dissociation of zinc from Slo3 suggests a long-lasting regulatory effect, adding to the understanding of ion channel modulation in sperm cells.

(3) Molecular Mechanistic Insights

Using Molecular Dynamics (MD) simulations and mutagenesis, the authors identify potential zinc-binding sites within Slo3's voltage-sensing domain (VSD), particularly E169 and E205. These computational predictions are supported by electrophysiological recordings, strengthening the argument that zinc directly binds and inhibits Slo3.

(4) Physiological Relevance and Functional Implications

The study suggests that zinc inhibition of Slo3 could contribute to sperm motility regulation during capacitation.

The authors provide sperm motility assays as supporting evidence, showing that zinc chelation affects motility only after capacitation has begun, suggesting a dynamic role of intracellular zinc in the capacitation process.

Weaknesses:

While the study presents compelling electrophysiological data and molecular insights, there are several critical gaps that must be addressed before fully supporting the physiological relevance of the findings.

(1) The authors should measure the effects in sperm cells using the patch-clamp technique to directly record Slo3 currents. By normalizing Slo3 currents to cell capacitance at different intracellular zinc concentrations, the authors can quantitatively assess the extent of Slo3 inhibition by zinc and strengthen the physiological relevance of their findings.

We thank the reviewer for the valuable comments to strengthen the physiological relevance of our findings. We provided additional data of Slo3 currents measured using perforated patch-clamp recording in sperm cells in experiments with zinc pyrithione (ZnPy) before and after the addition of 10 mM NH₄Cl. Control experiments were conducted in the absence of ZnPy, in which Slo3 current were recorded before and after the application of 10 mM NH₄Cl. These data have been integrated into Figure 1L-N and Figure 1—figure supplement 1A, B.

It is worth noting that Slo3 current in this recording might contain other endogenous current, as no specific blocker was used. Nonetheless, the data showed that the Slo3 current in sperm tends to be inhibited by zinc, as shown by the plot of absolute Slo3 current after the addition of 10 mM NH₄Cl in the absence of ZnPy (control) and in the presence of 100 µM ZnPy. There was a decrease in the fold change calculated from the absolute current before and after the addition of 10 mM NH₄Cl of ZnPy treated group compared to the control group.

We also provided data with the cell capacitance as suggested; however, cell capacitance obtained from the sperm recordings showed the capacitance throughout the head and midpiece of spermatozoa. On the other hand, Slo3 channels are not expressed in the entire spermatozoa, therefore the cell capacitance acquired from these recordings does not accurately reflect the area where the Slo3 channels are localized. Although we included normalization of Slo3 currents to cell capacitance before and after ZnPy application, this normalization should be interpreted with caution for the reasons mentioned above. The corresponding figure has been included in the supplementary data Figure 1—figure supplement 1A, B.

We added sentences to the result section as follows:

“We also measured Slo3 current using perforated patch-clamp recordings in spermatozoa treated with ZnPy, before and after the addition of NH₄ Cl. Control experiments were conducted in the absence of ZnPy, in which Slo3 current were recorded before and after the application of 10 mM NH₄Cl (Fig. 1L-N; Fig. 1—figure supplement 2A, B). Slo3 current in sperm tended to be inhibited by zinc, as shown by the plot of absolute Slo3 current after the addition of 10 mM NH₄Cl in the absence of ZnPy (control) and in the presence of 100 µM ZnPy (Fig. 1L, M). There was a decrease in the fold change calculated from the absolute current before and after the addition of 10 mM NH₄Cl of ZnPy treated group compared to the control group (Fig. 1N). Taken together, these results confirmed that intracellular zinc indeed inhibits alkalinization-induced hyperpolarization in mouse sperm.”

(2) Lack of Controls in Non-Capacitated Sperm

The claim that zinc is exported from sperm during capacitation needs stronger experimental validation.

The authors did not include a control group of non-capacitated sperm in key fluorescence imaging experiments, making it difficult to confirm that the observed zinc decrease is capacitation-specific rather than a general zinc redistribution process.

To strengthen this conclusion, experiments should be performed in non-capacitating conditions to determine whether intracellular zinc levels remain unchanged.

We added the control group of non-capacitated sperm in key fluorescence imaging experiments, as integrated in Figure 1B.

The following changes in the Results and Figure Legend sections are revised and added:

“We observed that there was a gradual and significant decrease in fluorescence intensity in both regions (Fig. 1B), particularly prominent in the flagellum (Fig. 1C). This decline suggests the active release of intracellular zinc from sperm flagellum occurs during capacitation. In contrast, the fluorescence intensity of the control group of non-capacitated sperm remained unchanged (Fig. 1B).”

Figure Legend 1B was modified accordingly.

(3) Unclear Role of Zinc in Physiological Capacitation

The study clearly demonstrates zinc inhibition of Slo3 but does not sufficiently establish how this affects capacitation at a functional level.

Additional motility and capacitation markers should be analyzed to confirm that zinc influences sperm behavior beyond Slo3 inhibition.

We thank the reviewer for this valuable comment. We fully agree that zinc can influence sperm physiology through multiple mechanisms and that its overall effects on capacitation are complex. However, the main goal of our study is to investigate the mechanism and to determine whether intracellular Zn²⁺ directly inhibits Slo3. Our results from both the heterologous expression system and the sperm membrane potential recordings consistently support this conclusion.

For these reasons, we believe that adding such assays would not clarify the role of Slo3 in capacitation but rather risk confounding interpretation. Instead, we have expanded the Discussion to explicitly acknowledge these limitations and to emphasize that future studies combining genetic or pharmacological modulation of Slo3 with comprehensive capacitation analyses will be required to fully define its physiological impact.

We added sentences to the discussion section in the revised manuscript as follows:

“Although these results support a mechanistic link between zinc and Slo3 activity, future studies that combine genetic or pharmacological modulation of Slo3 with comprehensive capacitation analyses will be required to define its physiological impact in more detail. Within this context, this study highlights the potential importance of intracellular zinc in the regulation of sperm capacitation.”

(4) Insufficient Data on Zinc-Slo3 Specificity

The authors should consider using quinidine, a known washable Slo3 inhibitor, to confirm that zinc acts specifically on Slo3 channels rather than other endogenous ion channels.

The study would benefit from including washout controls in the inside-out patch-clamp recordings, as seen in Figure 3-Supplement 1, to confirm that zinc inhibition is reversible or long-lasting.

We thank the reviewer for raising the point regarding the need to confirm that the current observed in our recordings indeed represents Slo3 current by using a specific blocker such as quinidine, as there is a possibility that endogenous currents might also be present and that zinc could act on those endogenous currents. Performing experiments with quinidine would indeed be crucial to demonstrate the specificity of Slo3 current in our patch-clamp recordings.

However, in our current experimental protocol, we apply ramp pulses multiple times and require a long series of recordings within a single session in one patch as described in the materials and methods as well as Figure 2I, Figure 4—figure supplement 1C, Figure 5B (pH 8.0 → 100 µM zinc → pH 8.0, to observe the washout effect). Incorporating quinidine into this sequence would make the protocol even longer (pH 8.0 → quinidine → washout → pH 8.0 → 100 µM zinc), which increases the likelihood of patch loss before completing the full set.

Furthermore, we have ensured that the recorded current corresponds to Slo3 by using appropriate experimental conditions, specifically the suitable voltage range for activation, a high intracellular pH (pH 8.0), and high-potassium solutions in our recordings.

(5) Missing Discussion of Zinc's Role in CatSper Regulation

The study focuses solely on Slo3 but does not mention CatSper, the principal Ca²⁺ channel essential for sperm capacitation.

Zinc has been reported to inhibit CatSper activity, which could significantly impact sperm function.

The discussion should address whether zinc's effect on Slo3 represents a broader regulatory mechanism influencing multiple ion channels during capacitation.

Thank you for the comment. To the best of our knowledge, there have been no reports showing that CatSper activity is directly regulated by zinc ions.

Furthermore, in our patch-clamp recordings with NH₄Cl and ZnPy, we observed that the normal CatSper current increased even in the presence of ZnPy, which makes it challenging to conclude whether zinc directly affects CatSper channel activity.

We added sentences to the discussion section in the revised manuscript as follows:

“In addition to that, to date, there are only few reports on the effect of zinc on other sperm ion channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper, a sperm-specific Ca²⁺ channel, in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, although this study does not provide direct evidence for zinc acting directly on CatSper (Jeschke et al., 2021).”

Final Assessment

This work presents important findings on zinc regulation of Slo3 channels, supported by strong electrophysiological and molecular analyses. However, the physiological relevance of these findings remains unclear due to missing controls, and needs additional functional assays. Addressing these issues would significantly enhance the manuscript's scientific rigor and impact.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Most of the specific comments and suggestions are in the public review. Minor additional comments primarily focused on presentation and textual errors are here.

(1) There is something strange happening in Figure 6D in the -100ish range. I think it's likely related to the reversal potential of K+.

Thank you for pointing it out. Yes in figure 6D there was strange plot in the range of -100 mV. As the reviewer has pointed out we also think that it is related to the reversal potential of potassium ions.

(2) There are a number of errors in the text that make following it difficult. For instance, multiple times the authors say "In consistent" (line 120 as an example) when I think they mean consistent with.

We changed the “in consistent” with “consistent with” throughout the revised manuscript.

Reviewer #3 (Recommendations for the authors):

The authors provide well-described experiments, particularly those examining the effects of intracellular zinc on Slo3 channels using inside-out patch-clamp recordings. However, some experimental designs intended to assess the physiological relevance of these findings during capacitation require additional controls and data before the authors' claims can be fully supported.

Comments

Major Concerns & Suggested Improvements

Line 65: "In the present study, we find that intracellular zinc is exported during capacitation, indicating that zinc dynamics in spermatozoa play an important role in fertilization."

This claim requires additional experimental data to be fully supported.

Thank you for pointing it out. We have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Line 79: "Intracellular zinc is exported from sperm during capacitation."

The authors should include controls in non-capacitated conditions to determine whether zinc export is specific to capacitation or a general process in sperm cells.

Again, we have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Figures - General Comment:

In all figures, please replace SEM (Standard Error of the Mean) with Standard Deviation (SD) for consistency and a more accurate representation of variability.

SEM (Standard Error of the Mean) has been replaced with SD (Standard Deviation) in all figures (main figures and supplements) as well as in numerical description accordingly.

Figure 1

Panel B:

Include a non-capacitating media control to confirm that the observed decrease in zinc-sensitive dye fluorescence is not due to artifact/photobleaching.

We have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Perform an experiment with capacitating media supplemented with a higher concentration of zinc. If intracellular zinc export is a real effect, added extracellular zinc should prevent or reduce this phenomenon.

We appreciate the reviewer’s suggestion; however, we believe that supplementing the medium with high concentrations of zinc is unsuitable for validating the export phenomenon due to confounding physiological factors. Our preliminary tests demonstrated that increasing extracellular zinc triggers a drastic increase in intracellular zinc as well (Author response image 5). Furthermore, the high concentration of BSA in the capacitation medium acts as a potent zinc buffer, precluding precise control over free Zn²⁺ levels. Therefore, the inherent difficulty in maintaining defined extracellular and intracellular Zn²⁺ gradients makes the interpretation of such data highly problematic. Future studies will focus on identifying the specific zinc transporters involved and characterizing their molecular mechanisms.

Author response image 5.

Zinc addition

Clarify whether the "n" value represents different cells or multiple recordings from the same cell.

n value represents different cells.

Supplemental Figure 1:

Incorporate Δ (delta) comparison between 10 min and 2 hours under control conditions and in the presence of TPEN.

Here we provide data:

Author response image 6.

Δ comparition between control and TPEN

Provide statistical analysis for these comparisons to make the effects of capacitation clearer.

We did the calculation and statistical analysis, however there was no statistical difference, as shown in the author response figure 6 due to high variability of individual data.

Figure 2

Panel C:

Incorporate inhibition at pH 7.4 and 6.0 for direct comparison.

Recording inhibition effect of zinc at pH 6.0 is not possible because there would be no current to begin with, as mSlo3 is gated by both voltage and alkaline pH.

Panel D:

Include a washout control, similar to what is shown in Panel A.

We included a washout control trace to Figure 2D.

Panel E:

Provide a longer reference trace in the absence of zinc to clearly visualize the control condition. The current reference segment is too short to properly assess baseline activity.

Although we do not have a longer reference trace in the absence of zinc for Figure 2E, we instead show the trace recorded under the application of 0.1 µM zinc in Figure 2—figure supplement 1A to illustrate the current behavior.

Panels G-H:

Include inside-out patch-clamp traces and quantification of zinc washout effects.

Inside out patch traces are shown in Figure 2G as we applied step-pulses protocol. The zinc washout effect could not be quantified because the patch was usually lost after the second step-pulse application.

Panels I-K:

Provide additional traces. In Panel I, the inhibition by zinc is clear, but in Panel J, the reduction appears less distinct and could be due to rundown or an artifact. Additional controls should clarify this.

Figure 2K presents the most representative trace among five recorded cells. The apparent reduction is less distinct, likely due to an artifact caused by a bubble in the rapid perfusion system during solution exchange. However, at the end of zinc application (t = 50 s), the current amplitude was clearly reduced compared with that at t = 0–10 s.

Figure 3

Panel D:

Include additional data showing the transition to pH 6 and washout with pH 7.5, similar to the experimental design in Panels A and B.

We included additional data showing raw trace of the application of pH 6.0 in Figure 3D, also included the transition to pH 6 and washout with pH 7.5 in Figure 3E.

Figure 3-Supplement 1:

Include zinc washout experiments. This approach is one of the best ways to evaluate the reversibility of zinc inhibition on the channel.

As mentioned above, in this recording we recorded step pulses up to +180 mV. The zinc washout effect could not be quantified because the patch was usually lost after the second step-pulse application.

Figure 6

Zinc Inhibition Specificity:

The authors should use quinidine, a known washable Slo3 inhibitor, to assess Slo3 activity before and after zinc injection.

This experiment would confirm that zinc specifically inhibits Slo3, rather than affecting other endogenous channels.

We sincerely thank the reviewer for this valuable suggestion. However, given the technical difficulty of these experiments, which involve lengthy VCF recordings and manual zinc injections that significantly compromise oocyte health, it is not feasible to apply quinidine at this stage.

Moreover, we observed voltage-dependent fluorescence changes around the VSD, and this change was influenced by the application of zinc, confirming that zinc specifically inhibits Slo3 rather than affecting other endogenous channels.

Discussion - Key Revisions Needed

Line 308: "Our results demonstrated that intracellular zinc is exported from spermatozoa during capacitation."

This claim needs to be supported by experiments using non-capacitated conditions.

Additionally, measuring maximum and minimum zinc concentrations under different conditions would improve the interpretation of fluorescence intensity changes.

We now include negative control in non-capacitated sperm. The data is incorporated into Figure 1B.

Line 309: "We further discovered that intracellular zinc regulates alkalinization-induced hyperpolarization in mice spermatozoa, mediated by Slo3 channel."

Additional controls are needed to substantiate this claim.

At this stage of the study, we do not have access to Slo3 knockout (KO) mice; therefore, performing additional experiments is not feasible.

Line 316: "Using FluoZin3-AM for zinc imaging, we confirmed the presence of intracellular zinc in sperm (Fig. 1A), which is consistent with previous findings (Henkel et al., 1999). Our observations revealed that treatment with capacitation medium induced a decrease in zinc fluorescence intensity (Fig. 1B, C), suggesting that zinc levels are dynamic during capacitation."

This statement must be supported by negative controls, including non-capacitated sperm conditions.

We now include negative control in non-capacitated sperm. The data is incorporated into Figure 1B.

Line 327: "We also observed that zinc chelator significantly affected the sperm motility only after, but not before, capacitation (Fig. 1-figure supplement 1)."

Data presentation should be revised to highlight the effects of capacitation itself.

The discussion should specify which motility parameters were affected and why others were not.

In the text we mentioned that:

“We incubated the isolated spermatozoa with cell permeable Zn²⁺ chelator N,N,N',N'-Tetrakis(2-pyridylmethyl)ethylenediamine (TPEN) and measured the motility parameters before and after capacitation. We found that VAP (average path velocity), VCL (curvilinear velocity), and VSL (straight-line velocity) were influenced by the TPEN treatment only after the capacitation, as shown in Fig. 1—figure supplement 1. These results demonstrate that the dynamics of zinc levels during capacitation potentially contributes to sperm motility, highlighting the importance of zinc action in sperm physiology.”

Indeed, we observed that zinc chelator significantly affected the sperm motility specifically in VAP (average path velocity), VCL (curvilinear velocity), and VSL (straight-line velocity) only after, but not before, capacitation (Fig. 1—figure supplement 1). Of note, it has been recently reported that all these motility parameters (VAP, VCL, and VSL) are reduced by Slo3-specific inhibitors in human sperm (M. Lyon et al., 2023). These findings are consistent with the idea that endogenous zinc dynamics control sperm motility through Slo3 during the capacitation process.

Figure legend is revised accordingly.

Line 369: "Structural determinants of zinc inhibition in the mSlo3 channel."

The authors should include an analysis of the evolutionary conservation of the mutated sites across Slo1, Slo2, and Slo3.

If Slo3 has a unique regulatory mechanism, these sites should show high sequence variability compared to other Slo channels.

If these sites are highly conserved, the authors should explain how Slo3 differs functionally from Slo1 and Slo2 despite this conservation.

We thank the reviewer for the valuable suggestions regarding the inclusion of additional discussion points on the structural determinants of zinc inhibition in the mSlo3 channel. We performed sequence alignment by using ClustalO between mSlo3, mSlo1, and mSlo2.2. It is worth noting that only human and frog variants of Slo2.1 sequence are available in the database, so we included only Slo2.2 subtype, as our focus was on Slo3 in mouse sperm.

Based on the alignment, E169 (mSlo3 numbering) is conserved among the Slo family channels in mice, while in contrast E205 (mSlo3 numbering) is not. To date, there have been no report examining the corresponding residues to E169 (E191 in mslo1 or E176 in mslo2.2) for their zinc sensitivity. This might be because in both channels the zinc-binding sites are well defined where they are located in RCK1 domain for Slo1 (Hou et al., 2010) and RCK2 domain for Slo2.2 (J. Zhang et al., 2023). The identified binding site in Slo2.2 is conserved in Slo2.1 but not present in Slo1 and Slo3 (J. Zhang et al., 2023), further suggesting that zinc regulation differs among Slo family members. However, this does not rule out the possibility that regions surrounding E191 or E176 could provide to additional insights into zinc regulation in these channels, which could be of interest for future studies.

Interestingly, in contrast to E169, E205 is not conserved across the Slo family, making this residue unique to the mouse Slo3 channel and potentially a determinant of zinc sensitivity in mSlo3. Given that E205 is located in the S4 domain and supported by our VCF results showing that zinc inhibition influences the motion of voltage-sensing domain of mSlo3, E205 represents an important residue to be explored in future studies. Furthermore, as this residue is unique only to Slo3, it highlights the distinct functional properties of Slo3 such as its gating mechanism as it is regulated by both membrane voltage and alkalinization, which has a different voltage range of activation compared to mSlo1 (Li et al., 2024) and involves distinct ligands and gating mechanisms compared to Slo2 (J. Zhang et al., 2023).

We add the sequence alignment results into Figure 5—figure supplement 1F.

We revised the results section as follows:

“Additionally, we performed sequence alignment by using ClustalO between mSlo3, mSlo1, and mSlo2.2. It is worth noting that only human and frog variants of Slo2.1 sequence are available in the database, so we included only Slo2.2 subtype, as our focus was on Slo3 in mouse sperm. Based on the alignment, E169 (mSlo3 numbering) is conserved among the Slo family channels in mice, while in contrast E205 (mSlo3 numbering) is not. (Figure 5—figure supplement 1F).”

We revised the discussion section as follows:

“Based on sequence alignment, E169 (mSlo3 numbering) is conserved among Slo family channels in mice, whereas E205 (mSlo3 numbering) is not (Fig. 5—figure supplement 1F). To date, no studies have examined the corresponding residues to E169 (E191 in mSlo1 or E176 in mSlo2.2) for their potential zinc sensitivity, likely because the established zinc binding sites in these channels are located in the RCK1 domain for Slo1 (Hou et al., 2010) and the RCK2 domain for Slo2.2 (J. Zhang et al., 2023). The identified zinc binding site in Slo2.2 is conserved in Slo2.1 but is absent in both Slo1 and Slo3 (J. Zhang et al., 2023), further suggesting that zinc regulation differs among Slo family members. Although regions surrounding E191 or E176 may still provide additional insights into zinc regulation and could be of interest for future investigation, E205 stands out because, unlike E169, it is not conserved across the Slo family, making it unique to mSlo3 and potentially a specific determinant of zinc sensitivity in this channel.”

Figure legend is revised accordingly.

Line 392: "Physiological relevance of zinc inhibition of the mSlo3 channel in mouse sperm."

The authors should mention the effects of zinc on CatSper channels, as CatSper is also crucial for capacitation.

Slo3 inhibition may represent only one component of zinc's broader regulatory role during capacitation.

We thank the reviewer for raising this important point regarding the physiological relevance of zinc inhibition of the mSlo3 channel in mouse sperm. We agree that we should have also discussed the effect of zinc on CatSper channels, as this channel is crucial for capacitation. To date, there are only few reports on the effect of zinc on CatSper channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, which facilitating sperm to escape into female genital tract (Jeschke et al., 2021). Taking this into consideration, as the reviewer pointed out, zinc inhibition on Slo3 may represent only one component of zinc’s broader regulatory role during capacitation.

We added a sentence to the discussion section in the revised manuscript as follows:

“In addition to that, to date, there are only few reports on the effect of zinc on other sperm ion channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper, a sperm-specific Ca²⁺ channel, in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, although this study does not provide direct evidence for zinc acting directly on CatSper (Jeschke et al., 2021).”

The study presents valuable insights into the role of intracellular zinc in sperm capacitation and Slo3 channel function. However, the physiological impact of these findings remains unclear due to insufficient controls and missing key experimental data. The suggested revisions would strengthen the validity of the claims made by the authors and improve the overall scientific rigor of the manuscript.

Key Areas for Improvement:

Control experiments in non-capacitated conditions.

Increased statistical rigor in figure analyses.

More detailed experiments to confirm specificity of zinc action on Slo3.

Expanded discussion of zinc's role beyond Slo3, including CatSper regulation.

The authors should measure these effects in sperm cells using the patch-clamp technique to directly record Slo3 currents. By normalizing Slo3 currents to cell capacitance at different intracellular zinc concentrations, the authors can quantitatively assess the extent of Slo3 inhibition by zinc and strengthen the physiological relevance of their findings.

By addressing these concerns, the manuscript will provide a more robust foundation for understanding zinc's regulatory role in sperm physiology and capacitation.

Author response:

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

eLife Assessment

The study presents valuable findings of an optimized E. coli cell-free protein synthesis (eCFPS) system that has been simplified by reducing the number of core components from 35 to 7; furthermore, the findings communicate a simplified 'fast lysate' preparation that eliminates the need for traditional runoff and dialysis steps. This study is an advance towards simplifying protein expression workflows, and the evidence provided is solid, starting with nanoluc, a protein that expresses readily in many systems, to applications to more challenging proteins like the functional self-assembling vimentin and the active restriction endonuclease Bsal. Data on the underlying mechanisms and efficiency of the presented system in terms of protein yield relative to other known cell-free systems would greatly enhance the findings' significance and the strength of the evidence. The paper remains of interest to scientists in microbiology, biotechnology and protein synthesis.

We thank the editors for the positive assessment of our optimized E. coli cellfree protein synthesis (eCFPS) system and the "fast lysate" preparation.

As suggested, we have significantly strengthened the evidence by adding:

(1) Mechanism data: We have integrated a detailed analysis of the endogenous metabolic pathways (amino acids and nucleotides) into the Discussion section, supported by literature (Prinz et al. 1997; Yokoyama et al. 2010; Kigawa et al. 1999).

(2) Efficiency comparisons: We have added quantitative comparisons of absolute protein yields between our simplified 7-component system and the conventional 35-component system (now in Figure S3 E-F), demonstrating that our system matches or exceeds traditional titers.

Public Reviews:

Reviewer #1 (Public review):

The authors only provided the data for optimization, leaving the underlying mechanism that explains the phenomena unexplained.

We appreciate this feedback. To address the mechanism of how protein synthesis persists without exogenous additives, we have expanded the Discussion to explain how the "fast lysate" retains active endogenous enzymes. By omitting runoff and dialysis, our system preserves the metabolic capacity to synthesize amino acids (e.g., Cys and Trp from Ser) and nucleotides from residual precursors, as supported by the literature (Prinz et al. 1997; Yokoyama et al. 2010; Kigawa et al. 1999).

Reviewer #2 (Public review):

The production of the lysate requires special instrumentation, limiting accessibility. While the strengths of the study are well-emphasized, the limitations are not mentioned.

We thank the reviewer for this point. While a high-pressure homogenizer is common in many molecular biology labs, we acknowledge it may be a barrier for some. We have now included a dedicated Limitations paragraph in the Discussion addressing accessibility and the inherent challenges of prokaryotic systems in producing complex human proteins requiring post-translational modifications.

Reviewer #3 (Public review):

(1) Clarification on "highly efficient" and the lack of comparison with typical high-yield systems.

We have clarified "highly efficient" as a holistic balance of high yield, robustness, and simplified preparation. Crucially, we added absolute yield data (sfGFP standard curve) to Figure S3E-F demonstrating that our 7-component system performs comparably to or better than traditional high-yield protocols.

(2) How did the authors ensure chemical composition only affected translation and not transcription?

This is a key distinction. We performed new experiments using pretranscribed mRNA templates (Figure S3G) to isolate translational effects. While translation efficiency slightly decreased in the simplified buffer, the overall protein yield increased significantly due to a dramatic boost in transcription efficiency, confirming the system's net performance gain.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

There are specific concerns that need to be addressed:

(1) On page 4, lines 103-109, the authors speculate that protein synthesis persists even in the absence of amino acids like arginine, cysteine, and tryptophan. They suggest that this is likely due to residual amounts of these amino acids present in the cell lysate. Yokoyama et al. demonstrated that these amino acids are generated from other amino acids by endogenous amino acid metabolic enzymes in the cell lysate (J. Biomol. NMR 48, 193, (2010), doi: 10.1007/s10858-010-9455-3.). Cysteine and tryptophan can be derived from serine. In this context, asparagine and glutamine can be disregarded because they are synthesized from aspartate and glutamate, respectively. A more indepth analysis is required to interpret the results accurately.

We thank the reviewer for this insightful comment and for pointing us toward the relevant literature. We agree that the persistence of protein synthesis in the absence of exogenous amino acids like Arg, Cys, and Trp is driven by the robust metabolic capacity of our "fast lysate."

Unlike conventional protocols, our "fast lysate" procedure deliberately omits runoff and dialysis steps, ensuring the maximal retention of active endogenous metabolic enzymes and residual small-molecule pools. As demonstrated by Yokoyama et al. (2010), E. coli cell extracts retain functional enzymes capable of synthesizing acid-sensitive amino acids from precursors or more stable amino acids. We have integrated a detailed mechanistic analysis of these endogenous metabolic pathways into the Discussion section and have cited Yokoyama et al. (2010) to support this interpretation.

(2) On page 4, lines 111-115, the authors demonstrated that protein synthesis could occur even in the absence of CTP or UTP, provided ATP and GTP are present. This phenomenon can also be attributed to the analogous complementary actions of metabolic pathways.

We agree with the reviewer's assessment. The ability of the optimized eCFPS to function without exogenous CTP/UTP relies on the same principle of endogenous metabolic conversion mentioned above. The omission of dialysis ensures that the lysate retains not only residual nucleotide pools but also the full suite of nucleotide metabolic enzymes. Powered by our optimized energy regeneration system, these enzymes maintain sufficient levels of CTP and UTP to support transcription and translation. This explanation has been added to the Discussion section to clarify the robustness of our system.

(3) On Figure 3A, protein synthesis kinetics are presented in a stair plot instead of the commonly used scatterplot. Is there a specific reason for choosing the stair plot?

We chose the stair plot representation to more clearly visualize the cumulative process of protein synthesis and its stabilization over discrete time intervals. Given that sampling occurred every 10 minutes, a stair plot effectively highlights the "plateau" phases and the incremental nature of accumulation, which can sometimes be obscured by dense scatter plots.

(4) On Figure 3C. It is unclear which system is referred to as the "initial" system in Figure 3C. Which data point on Figures 3A and 3B corresponds to this "initial" system?

We apologize for the lack of clarity. In Figure 3C, "initial" refers to the traditional 35-component system prior to our streamlining process. Figures 3A and 3B characterize the performance of the final optimized system alone. To resolve this ambiguity, we have updated the legend for Figure 3 to explicitly define the "initial" system as the pre-optimization control.

(5) In Figure 5D, previously reported eCFPS and the system using "fast lysate" were compared. The only difference between the two systems seems to be the type of lysate used, according to the Supplementary table. Optimal concentrations for the components are the same for both lysates, or is there still room for optimization for "fast lysate"?

The "fast lysate" primarily differs from conventional lysates in its preparation speed and the retention of endogenous cofactors/enzymes. While the optimal salt and energy concentrations remained consistent across both lysates in our tests, the "fast lysate" provides a higher baseline signal due to the endogenous T7 RNA polymerase and metabolic factors. We believe this demonstrates the robustness of the optimized reaction buffer across varying lysate preparation qualities.

(6) The study suggests that the removal of DTT didn't negatively affect protein expression. However, based on my experience, certain proteins, especially those with cysteine residues on their surface, tend to aggregate without DTT. Did the authors attempt to express such proteins, or did they draw this conclusion based on the limited number of proteins tested?

This is a valid concern. We based our conclusion on the functional expression of Bsal and vimentin—two proteins that are inherently prone to aggregation and misfolding. Their successful synthesis suggests that the intrinsic reducing capacity of the lysate (e.g., glutathione and thioredoxin systems) is sufficient for many targets (Prinz et al. 1997). However, we acknowledge that specialized cysteine-rich proteins may still require exogenous DTT. We have addressed this in the Discussion.

Reviewer #2 (Recommendations for the authors):

(1) Line 77-78 "we iteratively evaluated the contribution of individual constituents through luciferase reporter assays" - where is all the data? Please use an appropriate figure citation. Figure 1 cherry picks some components, but I think all data should be included.

We have structured the data presentation to show dispensable components in Figure 1 (where removal does not inhibit reaction) and essential components in Figure 2 (where 0-concentration results in zero activity). This ensures a logical flow of the "streamlining" narrative. All raw data for these screenings have been included in the Source Data files.

(2) Line 127 typo "concentrations".

We thank the reviewer for pointing out this error. The typo "concentrations" has been corrected.

(3) Figure 2: "protein expression levels" measured how?/what is the unit of the vertical bar on the right? I'm assuming that this experiment was conducted for discrete concentrations and thus generated discrete data points. However, the graph makes it seem as if this is continuous data. Kindly change the type of graphing to indicate that this is discrete data, showing each data point.

We appreciate the reviewer's suggestion. Protein expression levels were measured using the Nanoluciferase (NLuc) reporter gene assay. We utilized heatmaps/contour plots because our data are bivariate, representing the simultaneous optimization of two concentrations (e.g., Mg²⁺ and K⁺ in Figure 2A). For such matrix-based screenings, heatmaps are significantly more effective than scatter plots at conveying synergistic trends and identifying optimal reaction landscapes. Notably, this visualization approach for discrete biochemical optimization data was successfully employed by Ban lab in their recent study on translation system optimization (Bothe and Ban 2024). The vertical color bar on the right represents the relative expression ratio, normalized to the maximum yield. Although we have provided a scatter plot of this discrete data for reference (see Author response image 1), we believe it appears visually cluttered due to the high density of data points, making it difficult to discern overarching trends. Heatmaps, by contrast, offer a much clearer representation of the optimal reaction landscape. To maintain transparency, the discrete concentration points tested are clearly reflected by the axis ticks, and all raw discrete data are available in the Source Data files.

Author response image 1.

(4) Also, for all figures: the way the units are presented (DTT/mM) is confusing to me; it could just be something like [DTT] (mM).

We have revised all figures and tables to follow the standard format (e.g., [Component] (unit)) as suggested.

(5) Do the sucrose gradient sedimentation data have replicates? If so, please indicate statistics.

The sucrose gradient data provided (Figure 5C) is intended as qualitative evidence that the "fast lysate" method preserves intact 70S ribosomes across different preparation batches. This experiment has been performed independently multiple times with consistent results, demonstrating the high reproducibility of our preparation method. While we did not perform a quantitative comparative analysis of ribosome concentration, the consistency of the peaks confirms the integrity of the translational machinery.

(6) Line 457: fix the red line.

We thank the reviewer for pointing this out. The formatting issue has been resolved in the revised manuscript.

(7) Please mention the limitations of this study in the discussion.

We thank the reviewer for this suggestion. We have added a paragraph to the Discussion addressing the limitations of prokaryotic systems regarding complex eukaryotic post-translational modifications and chaperone requirements.

(8) Please include all uncropped gels in the source data, alongside the raw data, as you have already done.

As requested, we have provided all original, uncropped gel images in the Source Data files, alongside the raw data, to ensure full transparency and compliance with the journal's data sharing policies.

Reviewer #3 (Recommendations for the authors):

(1) The study lacks a comparison of protein levels with a typical cell-free protein synthesis system.

We have performed new quantitative experiments (now included in Figure S3 E-F) to measure absolute protein yields. Our optimized system achieves yields comparable to, or exceeding, several widely recognized highyield protocols while utilizing significantly fewer components. We have also clarified in the text that "highly efficient" refers to the synergistic balance of high yield, low cost, and simplified preparation time.

(2) What do the authors mean by "highly efficient", often used in the manuscript?

We thank the reviewer for the opportunity to clarify our terminology. We have performed new quantitative experiments (now included in Figure S3) to measure absolute protein yields, demonstrating that our optimized system achieves yields comparable to, or exceeding, several widely recognized highyield protocols while utilizing significantly fewer components.

In the context of this manuscript, we use the term "highly efficient" as a holistic descriptor that encapsulates three key dimensions of the system:

(1) Performance Superiority: Achieving higher expression levels and faster kinetics compared to conventional 35-component systems.

(2) Functional Robustness: The ability to efficiently synthesize challenging targets, such as cytotoxic proteins (BsaI) and aggregation-prone proteins (vimentin), which often fail in simplified systems.

(3) Practical Utility: A drastic reduction in preparation time and cost through the "fast lysate" protocol and the removal of 28 auxiliary components, thereby lowering the barrier to adoption.

This definition aligns with the study's core objective: developing a system where efficiency is measured not only by final yield but by the synergy between high performance and extreme ease of use.

(3) In this article, the term 'optimisation' is used as a synonym for 'simplification'. In biochemistry, optimisation commonly refers to an increase in yield, or the same yield achieved more easily or at a lower cost. In this case, however, we have no idea how this new system compares to a conventional expression system in terms of yield.

We thank the reviewer for this conceptual clarification. We agree that in biochemistry, "optimization" typically implies an improvement in yield or cost-effectiveness. In our study, we use the term to describe the process of achieving a superior balance between system simplicity and protein production. To address the reviewer's concern regarding the lack of a direct yield comparison, we have added new data in Figure S3. This figure provides a sideby-side comparison of protein yields between our simplified 7-component system and the conventional 35-component system. The results demonstrate that our system not only matches the performance of the traditional setup but frequently exceeds it in terms of final protein titer, while significantly reducing the reagent cost and preparation complexity. Thus, the simplification achieved in this work represents a true biochemical optimization of the cell-free synthesis process.

(4) The levels of transcripts of the proteins studied were not determined in any of the experiments performed. Therefore, it is unknown whether the effects of different experimental conditions on NLuc, GFP or other protein expression are due to an effect on transcription, translation, or both.

This is an excellent point. We performed a new set of experiments using mRNA templates instead of DNA to isolate the effects on translation (Figure S3G). Our results indicate that while the system's overall boost in NLuc expression is partially attributable to enhanced transcription efficiency, the translation machinery remains highly robust. We have updated the Results and Discussion to reflect this distinction.

References

Bothe, Adrian, and Nenad Ban. 2024. “A Highly Optimized Human in Vitro Translation System.” Cell Reports Methods 4 (4): 100755.

Kigawa, T., T. Yabuki, Y. Yoshida, M. Tsutsui, Y. Ito, T. Shibata, and S. Yokoyama. 1999. “Cell-Free Production and Stable-Isotope Labeling of Milligram Quantities of Proteins.” FEBS Letters 442 (1): 15–19.

Prinz, W. A., F. Aslund, A. Holmgren, and J. Beckwith. 1997. “The Role of the Thioredoxin and Glutaredoxin Pathways in Reducing Protein Disulfide Bonds in the Escherichia Coli Cytoplasm.” The Journal of Biological Chemistry 272 (25): 15661–67.

Yokoyama, Jun, Takayoshi Matsuda, Seizo Koshiba, and Takanori Kigawa. 2010. “An Economical Method for Producing Stable-Isotope Labeled Proteins by the E. Coli Cell-Free System.” Journal of Biomolecular NMR 48 (4): 193–201.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Bobola et al reports single-nucleus expression analysis with some supporting spatial expression data of human embryonic and fetal cardiac outflow tracts compared to adult aortic valves. The transcription factor GATA6 is identified as a top regulator of one of the mesenchymal subpopulations, and potential interacting factors and downstream target genes are identified bioinformatically. Additional bioinformatic tools are used to describe cell lineage relationships and trajectories for developmental and adult cardiac cell types.

Strengths:

The studies of human tissue and extensive gene expression data will be valuable to the field.

Weaknesses:

(1) The expression data are largely confirmatory of previous studies in humans and mice. Thus, it is not clear what novel biological insights are being reported. While there is some novelty and impact in using human tissue, there are extensive existing publications and data sets in this area.

(2) Major conclusions regarding spatial localization, differential gene expression, or cell lineage relationships based on bioinformatic data are not validated in the context of intact tissues.

(3) The conclusions regarding lineage relationships are based on common gene expression in the current study and may not reflect cellular origins or lineage relationships that have previously been reported in genetic mouse models.

(4) An additional limitation is the exclusive examination of adult aortic valve leaflets that represent only a subset of outflow tract derivatives in the mature heart. The conclusion, as stated in the title regarding adult derivatives of the outflow tract, is not accurate based on the limited adult tissue evaluated, exclusive bioinformatic approach, and lack of experimental lineage analysis of cell origins.

Reviewer #2 (Public review):

Summary:

The manuscript by Leshem et al. presents a transcriptomic analysis of the developing human outflow tract (OFT) at embryonic and fetal stages using snRNAseq and spatial transcriptomics. Additionally, the authors analyze transcriptomic data from the adult aortic valve to compare embryonic and adult cell populations, aiming to identify persistent embryonic transcriptional signatures in adult cells. A total of 15 clusters were identified from the embryonic and fetal OFT samples, including three mesenchymal and four endothelial clusters. Using SCENIC analysis on the embryonic snRNAseq data, the authors identified GATA6 as a key regulator of valve precursor cells. Spatial transcriptomic analysis of four fetal OFT sections further revealed the spatial distribution of mesenchymal nuclei, smooth muscle cells, and valvular interstitial cells. Trajectory analysis identified two distinct developmental origins of fetal mesenchymal cells: the neural crest and the second heart field. Finally, the authors used snRNAseq data from the adult aortic valve to propose that embryonic transcriptional signatures persist in a subset of adult cells.

Strengths:

(1) The study offers a rich and detailed dataset, combining snRNA-seq and spatial transcriptomics in human embryonic and fetal OFT, which are challenging to obtain.

(2) The use of SCENIC and trajectory analysis adds mechanistic insight into cell lineage and regulatory programs during valve development.

(3) This study confirms GATA6 as a key regulator of valve precursor cells.

(4) Comparison between embryonic/fetal and adult datasets represents a novel attempt to trace persistence of developmental transcriptional programs.

Weaknesses:

(1) A major limitation is the lack of experimental validation to support key conclusions, particularly the claim of persistent embryonic transcriptional signatures in adult cells.

(2) The manuscript would benefit from a clearer discussion of how these results advance beyond previous studies in human heart and valve development.

(3) The comparison between embryonic and adult data is interesting, but would be more convincing with additional evidence supporting the proposed persistence of embryonic transcriptional signatures in adult cells.

Reviewer #3 (Public review):

Leshem et al have generated a transcriptional cell atlas of the human outflow tract at two developmental timepoints and its adult valvular derivatives. This carefully performed study provides a useful resource for the study of known genes implicated in outflow tract defects and potentially also for discovering new disease genes. The authors reveal neural crest and mesodermal contributions to different outflow tract components and show that GATA6, known to play a role in arterial valve development, controls a set of genes expressed in endocardium-derived cells during valve development. Interestingly, the results suggest lineage persistence of expression of certain genes through to the adult timepoint, a main new finding of this study.

The following points should be addressed to reinforce the conclusions and emphasize the novel features of this study.

(1) It would be helpful to clarify how these new findings confirm or diverge from what is known from analysis of neural crest and mesodermal lineage contributions to different cell populations in the mouse heart. Did the authors identify any human-specific populations of cells, such as the LGR5 population reported by Sahara et al?

(2) The authors should clarify in the introduction and results that they consider the endocardium to be on the SHF trajectory as indicated in Figure S4C. Please add a reference for this point.

(3) The GATA6 results are interesting and support this experimental approach. The paper would be reinforced if the authors could provide any functional validation (in addition to their GATA6 genomic occupancy data) that the designated target genes are regulated by GATA6. This might involve looking at mutant mouse embryos or cultured cells. Do the authors consider that GATA6 may regulate the endocardial to mesenchymal transition during the early stages of valve development? Or the valve interstitial cell versus fibroblast fate choice?

(4) Do the new findings reveal whether human valves have a direct SHF to VIC trajectory (ie, without transiting through endocardium) as has been recently shown in the murine non-coronary valve leaflet? Relevant to this point, Figure 5E appears to show contributions to a single adult aortic valve leaflet - this should be explained, or corrected.

We sincerely thank the Editor and the Reviewers for their constructive and insightful comments. We have carefully addressed the majority of the points raised and believe the revisions have substantially strengthened the manuscript.

Recommendations for the authors:

Reviewing Editor Comments:

Overall, the reviewers felt that integrating these datasets with prior snRNAseq datasets on human OFT (de Bono et al, 2025) would enhance analyses and provide broader context.

Several human fetal heart single-cell datasets have been published, including De Bono et al, 2025. We carefully considered whether integrative analyses with these datasets would further strengthen our study. However, there are substantial differences in anatomical scope: most published datasets encompass broad cardiac regions, whereas our study specifically targets the OFT, enabling higher-resolution characterization of OFT-specific cell states. Integration across datasets with markedly different regional compositions would likely be driven by largescale anatomical differences rather than yield additional OFT-specific insight. In addition, cross-study integration requires batch correction. When datasets differ in anatomical scope, as well as developmental timing, and experimental protocols, stronger correction may be needed, increasing the risk of overcorrection and potential loss of biologically meaningful OFTspecific signals.

Importantly, our dataset has been deposited in the Human Cell Atlas and is fully available for future comparative analyses. We therefore believe that broader cross-dataset integration is best undertaken within such harmonized frameworks as more closely matched datasets become available.

Overall, cluster annotations should be more rigorous, which may be facilitated by comparisons with earlier studies.

We have clarified all the points raised by the reviewer regarding cluster annotation. Specifically: (1) the “cardiac” cluster has been renamed “cardiac muscle” to more accurately reflect its transcriptional identity; and (2) we now explicitly state that mesenchymal populations not resolved in the initial global analysis (across all samples) were subsequently defined through dedicated sub clustering analyses performed separately for the adult and developmental datasets. These clarifications have been incorporated into the revised manuscript.

Citation of other spatial transcriptomics studies on human OFT would be useful.

We apologise for missing these contributions. They have now been added to the text.

Can the authors identify a human-specific population of cells, such as the LGR5 population reported by Sahara et al?

While our dataset does not reveal a novel single-gene marker comparable to the human specific LGR5 marker described for the LGR5-positive population by Sahara et al., it does identify a distinct GATA6-enriched embryonic mesenchymal population that functions as a human valve progenitor lineage. Using regulatory network analysis, RNA velocity, lineage tracing and spatial transcriptomics, we show that this GATA6-driven program is specifically associated with semilunar valve morphogenesis and that its transcriptional signature persists in fetal and adult VIC populations. Thus, the novelty of our study lies in defining this human GATA6-regulated valve progenitor population and its lineage trajectory, rather than in the identification of previously unreported single marker genes.

“….Although we have not defined a novel single-gene marker (analogous to LRG5 [Sahara et al]), our identification of a GATA6 network highlights…..”

Further investigation of the specific role of GATA6 would strengthen findings.

FISH studies would indicate whether GATA6 is involved in EMT or fibroblast versus valve interstitial cell fate choice.

We have added a panel to Fig. S2 (D), showing that GATA6 expression is not restricted to specific outflow tract populations. In CS16-17 embryos, GATA6-expressing nuclei are detected across all embryonic clusters. Given this broad expression pattern, FISH analysis would not distinguish whether GATA6 functions in EMT or in fibroblast versus valve interstitial cell fate specification. While we cannot exclude the possibility that GATA6 contributes to EMT, we observe that its expression levels are highest in cluster 4 (post-EMT) cells. This suggests that GATA6 activation is more likely a consequence of the transition rather than its initiating cause (shown in Fig. S2D).

Functional validation of some proposed GATA6 targets would strengthen findings.

To our knowledge, there are currently no publicly available datasets defining the GATA6 regulatory network in human OFT cells or valvular fibroblast progenitors. Existing datasets focus primarily on cardiomyocytes, which arise from a distinct developmental lineage. Given the well-established cell-type and context dependence of transcription factor activity, these datasets are unlikely to provide meaningful insight into regulatory relationships within the valvular lineage examined here.

As noted in the original submission, we previously leveraged published mouse GATA6 ChIPseq data from E11.5 OFT (DOI: https://doi.org/10.7554/eLife.31362) as independent support for the GATA6 regulon identified in our human dataset. In this revised version, we have now extended this analysis by formally quantifying the overlap between the cluster 4 GATA6 regulon and genes bound by GATA6 in the mouse OFT dataset. Using a hypergeometric enrichment test, we found that the observed overlap is approximately two-fold greater than expected by chance and highly significant (p = 1.2 × 10^-33). This statistical analysis strengthens our original interpretation and provides quantitative support that the identified regulon is strongly enriched for bona fide GATA6-bound targets in a closely related developmental context.

In addition, we examined the spatial expression pattern of the GATA6 regulon gene set and found that it specifically localizes to the semilunar valves (OFT derivatives), consistent with GATA6 activity in this developmental context. This new analysis has been incorporated into Figure 2F of the revised manuscript.

Collectively, the cross-species binding enrichment and valve-specific expression pattern provide orthogonal support for the biological relevance of the identified GATA6 regulon and strengthen the mechanistic interpretation of GATA6 function in OFT and valve development.

As GATA6 has been previously identified in mouse studies, can the authors identify novel transcription factors potentially involved in OFT development?

To identify additional transcription factors potentially involved in OFT development and to define regulators that may confer specificity to GATA6 activity, we compared the GATA6 regulon with the regulons of other cluster 4 transcription factors identified by SCENIC (SOX4, GLI3, RARG, ETV1, GLIS3, BACH2, ZNF423, FOXO3, ZBTB20).

While all cluster 4 regulators share some downstream targets, GLI3 regulon showed approximately twice the degree of overlap with the GATA6 regulon compared to the other factors. This suggests a potential functional interaction between GATA6 and GLI3 in OFT associated mesenchyme. Consistent with this, cooperation between GATA6 and GLI3 has been reported in mouse limb development. These findings have now been incorporated into the Results section, and co-expression of GATA6 and GLI3 in CS16-17 populations is shown in Figure S2DE.

Although GATA6 has previously been implicated in OFT development, SCENIC analysis provides mechanistic insight by defining the downstream gene programs active in specific human embryonic lineages. Thus, the novelty of our findings lies not in re-identifying GATA6, but in characterizing its regulon in human OFT- and valve-associated mesenchyme and identifying potential cooperating regulators such as GLI3.

Embryonic signatures in adult valve cells are an interesting finding, that should be further explored by pseudotime trajectories, which may also indicate whether SHF cells have a direct trajectory to VIC (without transiting endocardium), as recently shown in mice.

We included all embryonic populations, including cardiac progenitor cells (SHF), in the pseudotime trajectory analysis. However, we did not observe evidence of a direct trajectory from SHF cells toward VIC. In contrast, the same analysis consistently identified a trajectory linking endocardial cells to VIC, supporting an endocardial origin in our dataset.

Reviewer #1 (Recommendations for the authors):

(1) Major conclusions regarding cell lineages and derivatives are based on common gene expression patterns and bioinformatic tools. Thus, these conclusions are not based on empirical data, and assumptions regarding lineages based on gene expression may not be accurate. The language related to lineage analysis, derivative, and longitudinal gene expression is not supported by data. For example, studies in mice have shown that aortic valve interstitial cells from endocardial cushions and neural crest-derived lineages have overlapping patterns of ECM gene expression and cannot be easily distinguished in adults. Thus, it is not possible to determine derivation and cell origins based on gene expression alone.

While we fully acknowledge that gene expression-based analyses provide correlative rather than direct lineage-tracing evidence, the Reviewer’s statement that “it is not possible to determine derivation and cell origins based on gene expression alone,” and the example cited in support, appear to equate global transcriptional similarity with the distinct embryonic transcriptional signatures that underpin our analysis.

As the Reviewer notes, a given differentiated cell type can derive from different embryonic progenitors. Due to functional convergence, differentiated cells often exhibit highly similar expression profiles that reflect their shared function rather than developmental origin. Consequently, discriminating embryonic origins based on global expression profiles, or even for highly distinctive genes of differentiated cells, is very challenging. The example cited by the Reviewer - overlapping ECM gene expression in aortic valve interstitial cells derived from endocardial cushions and neural crest - illustrates precisely this point.

However, our analysis does not rely on global transcriptional similarity or on markers of mature differentiated cells. Instead, we specifically identified gene sets that are highly distinctive of embryonic clusters prior to the onset of differentiation. These signatures are enriched for transcription factors and signaling molecules that define developmental identity, rather than functional effector genes associated with mature cell states. We have shown that these embryonic signatures persist in fetal cells (which already express differentiated markers but are developmentally closer to the embryonic stage relative to adult cells) and remain detectable, albeit attenuated, in adult cells. It is these distinctive embryonic transcriptional signatures, rather than global or shared functional gene expression, that we have used to infer potential lineage relationships.

We fully acknowledge that this constitutes correlative evidence rather than direct lineage tracing, which is not feasible in human studies. However, the persistence of embryonic regulatory signatures into fetal and adult stages provides a biologically plausible link to developmental origin. This persistence most plausibly reflects partial retention of ancestral embryonic transcriptional programs in descendant cells, rather than de novo activation later in life of embryonic genes that were never previously expressed in that cell’s lineage.

(2) Most of the findings related to cell composition, gene expression, and cell lineages seem to be largely confirmatory of previous reports. Novel findings should be emphasized and validated in the tissues.

We agree that several aspects of our dataset reproduce and extend findings from previous human and animal studies, which we regard as an important validation of the atlas. However, our study also provides multiple novel insights that are directly supported by our spatial data. Specifically, we (i) identify a GATA6-enriched embryonic mesenchymal valve progenitor population, (ii) delineate its GATA6 transcriptional regulon and direct targets implicated in OFT and valve disease, and (iii) trace its embryonic transcriptional signature into fetal and adult valve interstitial cell populations. These findings are strengthened by our spatial transcriptomic data, which maps the GATA6 regulon and key targets to the semilunar valves and adjacent arterial root, providing in situ validation of both cell identity and gene expression patterns (see Fig. 3 and the newly added Fig. 2F). We have revised the Discussion to more explicitly highlight these novel aspects and their spatial validation in the final

“In summary, our work goes beyond confirming previously reported cell types by (i) defining a GATA6-regulated human valve progenitor lineage and its descendants, (ii) establishing distinct embryonic origins for smooth muscle and valvular fibroblasts, and (iii) demonstrating persistence of embryonic signatures in adult valve cell populations. These findings are directly supported in tissue by our spatial transcriptomics data, which map these lineages and regulatory programs to defined anatomical domains within the human OFT and semilunar valves.”

(3) The developing outflow tract of the heart contributes to more than just the aortic valve leaflets in adults. Additional conotruncal structures need to be evaluated in order to define adult derivatives of the developing outflow tract as described in the title.

The title has been changed to reflect that only adult aortic valves were examined.

(4) Major conclusions regarding the GATA6 regulatory network and downstream target genes are not validated in the context of the developing outflow tract or adult valves. Is GATA6 expression restricted to specific outflow tract populations? Is GATA6 binding or responsive gene expression detected for the indicated target genes?

We performed additional analyses that further reinforce the relationship between GATA6 and its target genes and support the biological relevance of GATA6 downstream targets in arterial valve development. Below, we address the specific questions raised by the reviewer.

(1) Is GATA6 expression restricted to specific outflow tract populations?

GATA6 expression is not restricted to specific outflow tract populations. In CS16-17 embryos, GATA6-expressing cells are detected across all embryonic clusters; however, expression levels are highest in cluster 4 (valve precursor cells).

Despite this broad expression pattern, SCENIC identifies GATA6 activity (i.e., a GATA6 regulon) specifically in cluster 4. This apparent restriction of GATA6 regulatory activity to cluster 4 may be explained, at least in part, by its elevated expression levels within this cluster. Alternatively, given that transcription factors often act in a combinatorial manner, GATA6 may co-regulate its target genes in cluster 4 together with additional cluster-specific regulators. To explore this possibility, we compared the GATA6 regulon with the regulons of other cluster 4 transcription factors identified by SCENIC (namely SOX4, GLI3, RARG, ETV1, GLIS3, BACH2, ZNF423, FOXO3, ZBTB20) in order to identify potential co-regulatory modules. As expected, since these regulons are sampled from the subset of genes enriched in cluster 4, all regulators share a substantial proportion of downstream targets with GATA6. However, GLI3 stands out, showing approximately twice the degree of overlap compared to the other factors. This suggests a functional interaction between GATA6 and GLI3, consistent with previously reported cooperation in mouse limb development. These results have been incorporated into the Results section, and the expression of GATA6 and GLI3 in CS16-17 cell populations is shown in Fig. S2DE.

(2) Is GATA6 binding or responsive gene expression detected for the indicated target genes?

We were unable to find public data describing the GATA6 regulatory network or its downstream targets in the specific human cell types examined here (OFT cells; valvular fibroblast progenitors). Available datasets focus primarily on cardiomyocytes, which arise from a distinct lineage, and because transcription factor function is highly cell-type and context dependent, these datasets are unlikely to be helpful in inferring regulatory relationships in the valvular lineage.

The strongest validation for the GATA6 regulon identified in this study comes from the mouse GATA6 occupancy data (this was included in the original manuscript). Although derived from a different species, GATA6 binding has been profiled in a highly related developmental context, the OFT. To assess the relevance of these data to our human findings, we performed a hypergeometric test comparing the GATA6 regulon identified in cluster 4 (this study) with genes bound by GATA6 in E11.5 mouse OFT ChIP-seq data (DOI: https://doi.org/10.7554/eLife.31362). The observed overlap is substantially greater than expected by chance: it is approximately twice the expected value, and the enrichment is highly significant (p = 1.2 × 10^-33). Biologically, this strongly supports the interpretation that many genes within GATA6 regulon are likely to be direct GATA6 targets, or at minimum are strongly associated with GATA6 binding, rather than representing a random gene set. This analysis has been added to the revised manuscript.

In this revised version of the manuscript, we also overlapped the expression of GATA6 regulon genes to our fetal spatial transcriptomics data. GATA6 regulon was identified in embryonic cluster 4, whose expected trajectory is fetal valvular fibroblasts (cluster 12). Remarkably, GATA6 regulon genes are expressed in both the aortic and pulmonary valves, and their expression pattern aligns closely with HAPLN1-positive valvular fibroblasts (cluster 12), further supporting the biological relevance of this gene set. This new data has been added to Fig 2(F).

Together, the strong enrichment of GATA6 regulon genes among GATA6-bound targets in the OFT, and the specific expression of this gene set within the arterial valves (cluster 4 descendant cells), support the biological relevance of GATA6 downstream targets in arterial valve development and disease. In addition, we identify GLI3 as a potential GATA6 co-binding partner.

(5) What are "cardiac" cell types in the embryonic single cell clustering? Are these cardiomyocytes? Cardiac is an ambiguous term if the cells being analyzed are all in the heart.

Thank you for highlighting this ambiguity. The “cardiac” population refers specifically to cardiac muscle cells. We have updated the labels in Fig. 1E, 1F, and Fig. S3A to make this explicit.

(6) The methods and analytical tools seem fairly standard for single nuclear gene expression and spatial genomics studies. What are the new tools and resources being reported? The "novel lineage tracing algorithm" mentioned in the methods is not well described. A Cellxgene VIP app is mentioned, but is not described in detail. Also, it seems to be housed on a local server, which is not optimal.

The description of the lineage tracing algorithm has been expanded in the method’s section of the paper.

The data has been submitted to the Human Cell Atlas, a coordinated global effort to systematically map human cell types using standardized, interoperable formats. Public access via cell x gene enables interactive visualization, gene-level queries, and cross-dataset comparisons without requiring advanced computational expertise. This broad accessibility enhances reproducibility, facilitates integration with complementary single-cell and spatial datasets, and maximizes the visibility, transparency, and long-term impact of our work.

(7) Only adult aortic valves from females were included in the study.

The rationale for using female tissues has been explained in the result section:

We collected female samples to mitigate individual variability and maximise the possibility to analyse healthy aortic valves, justified by the lower incidence and severity of aortic disease in females versus males.

(8) In many of the figures, the font size of the text is too small to read.

We have increased the font size in all figures where this was compatible with the layout. For the larger plots, additional enlargement would necessitate scaling the panels beyond the allowable page dimensions, and therefore could not be implemented.

(9) "CAT" is not a commonly used abbreviation for congenital heart anomalies related to persistent truncus arteriosus.

CAT is now the preferred term for PTA as latinised terms are no longer used.

Reviewer #2 (Recommendations for the authors):

Overall, this study is thoughtfully conducted and offers valuable observations that contribute to our understanding of valve morphogenesis. However, my main concern is the lack of experimental validation to support the findings, particularly the conclusion regarding the persistence of transcriptional signatures in adult cells, which is not sufficiently substantiated or clearly argued. It is unclear how this study advances beyond previous research in humans.

Major points:

(1) Several recent studies have applied spatial transcriptomics to human embryonic and fetal hearts, including OFT (Asp et al., 2019; Queen et al., 2023; Farah et al., 2024; De Bono et al., 2025). It is disappointing that the authors did not acknowledge these important contributions.

We apologise for missing these contributions. They have now been added to the text.

(2) The present study used snRNAseq to explore the transcriptional signature of the fetal OFT. A similar approach was used by De Bono et al. (2025) to analyze fetal hearts. Integrating these complementary snRNAseq datasets could enhance the current analysis and provide broader context for the findings.

The reviewers suggested that integrating our datasets with prior snRNA-seq datasets on human OFT (de Bono et al., 2025) could enhance the analyses and provide broader context. While several fetal heart datasets have been published (e.g., Sahara et al.), our study focuses specifically on the OFT. These other studies do not perform cross-dataset comparisons. We therefore do not see a strong rationale for integrating ours, especially given that those datasets cover much larger regions of the heart.

(3) Figure 1 presents 18 distinct clusters identified through unsupervised clustering. The authors classify three of these clusters broadly as mesenchymal cells. However, the term "mesenchymal cells" lacks precision. The authors should clarify why these clusters were not more specifically defined as fibroblasts or myofibroblasts based on marker expression.

Clustering of the full dataset does not provide sufficient resolution to distinguish all mesenchymal cell types. The clusters broadly annotated as mesenchymal comprise heterogeneous populations, including both undifferentiated embryonic mesenchymal cells and more differentiated fetal mesenchymal cells. These mesenchymal clusters were therefore further subclustered, and the resulting cell identities are described in detail in the Results sections corresponding to Fig. 2 and Fig. 3.

(4) The authors used SCENIC on their snRNAseq datasets to infer key cell fate regulators and identified GATA6 as a top regulator of embryonic mesenchymal cluster 4. However, the rationale for focusing on GATA6, which is already known to be associated with CHD in humans, is not fully convincing. Why not investigate a transcription factor whose role in valve development remains unexplored?

There are two key outcomes from a SCENIC analysis: (1) the identification of major transcriptional regulators driving the differentiation of a given cluster, and (2) the identification of their regulons (the downstream gene programs they control). While GATA6 is indeed already known to be associated with CHD in humans, including valve malformations and major OFT defects, its downstream targets in the relevant human developmental lineages have not been defined. Understanding these targets is essential for clarifying the molecular basis of GATA6-mediated CHD. Thus, the significance of our result does not lie in the rediscovery of GATA6 as a CHD-related factor, but in identifying the genes it regulates in embryonic OFT- and valve-associated mesenchyme. These GATA6-controlled genes in the OFT and valves represent biologically plausible candidate genes for human OFT defects, as disruption of GATA6 targets could similarly contribute to CHD.

In this revised version we have performed a hypergeometric test showing that GATA6 regulon genes are significantly enriched among genes bound by GATA6 in the OFT. Biologically, this strongly supports the interpretation that many genes within the GATA6 regulon are likely to be direct GATA6 targets, or at minimum are strongly associated with GATA6 binding in the OFT, rather than representing a random gene set.

We have also mapped the expression of GATA6 regulon to the semilunar valves. Collectively, these analyses demonstrate that the GATA6 regulon captures a biologically coherent and developmentally relevant program, offering new mechanistic insight into how GATA6 influences OFT and valve formation and how its disruption may contribute to CHD.

(5) Several studies have already suggested a role for GATA6 in EMT. Do the authors propose that GATA6 regulates this process during embryonic valve development? Once again, validation using FISH would be important to support these findings.

We do not propose that GATA6 directly regulates EMT during embryonic valve development. We rather make two independent observations: (1) cluster 4 derives from cluster 7 (likely through EMT); (2) GATA6 regulates cluster4-specific genes.

The first observation is supported by RNA velocity, which links cluster 7 to cluster 4. Supporting this interpretation, endothelial cluster 7 is enriched for genes associated with arterial valve development, and mesenchymal cluster 4 cells are identified as progenitors of fetal valve fibroblasts. Because cluster 7 is endothelial and cluster 4 is mesenchymal, this trajectory suggests an endothelial-to-mesenchymal transition.

Second, SCENIC analysis identifies GATA6 as a regulator of cluster 4 genes. Additionally, the GATA6 regulon shows distinct localization to the formed valves in fetal cells (new data added to Fig 2F). Together these findings support the notion that GATA6 regulates a gene program specific to the cell populations that will give rise to the valves and that these genes remain selectively expressed in valve cells once the arterial valves have formed.

While we cannot exclude the possibility that GATA6 contributes to EMT, we observe that GATA6 expression levels are highest in cluster 4 (post-EMT) cells, suggesting that its activation may be a consequence of the transition rather than its initiating cause (now shown in Fig S2D).

For validation using FISH, please see response to point 6 below

(6) I found it curious that the ST section was used to validate MECOM expression (Figure 2I), while ST had not yet been introduced at this point in the manuscript. Validation using FISH would have been a more appropriate approach.

Thank you for drawing attention to this discrepancy. Spatial transcriptomics is now introduced before MECOM analysis, in the Results section pertaining to Figure 2F

“…spatial transcriptomic analysis of a later stage (12pcw) OFT shows that GATA6 regulon is mainly restricted to the aortic and pulmonary valves (Fig 2F)”.

With regard to this and the above comment concerning FISH, while RNA FISH/RNAscope would provide an additional orthogonal approach, the Visium-based spatial transcriptomics platform directly measures MECOM transcripts in tissue sections and, in our view, represents an appropriate and sufficiently sensitive method for validating its spatial distribution in the human OFT. We have therefore relied on the spatial transcriptomics dataset to confirm and validate gene expression patterns, rather than performing additional FISH experiments. We now explicitly state that this approach serves as an independent in situ validation of gene expression, including MECOM.

(7) "Spatial resolution of mesenchymal nuclei in the OFT" section: It is unclear which cluster the authors are referring to in this section.

As mentioned in the text, we “mapped the five fetal mesenchymal clusters to distinct structures in the OFT” and used distinctive markers to confirm spatial assignments.

(8) The authors should justify their choice to use Cell2location instead of a deconvolution method.

We selected cell2location because it provides a probabilistic, hierarchical Bayesian framework that explicitly models technical variability across both single-cell reference data and spatial transcriptomics platforms. Rather than relying on predefined marker genes or simple linear regression, cell2location leverages the full transcriptomic profile of reference single-cell data and incorporates a factor analysis-based framework to model shared transcriptional signatures and latent structure across cell types. This approach improves discrimination between closely related cell states and reduces sensitivity to gene selection bias. Additionally, the probabilistic formulation yields uncertainty estimates for inferred cell abundances, enhancing interpretability and statistical rigor. Together, these features make cell2location particularly well suited for resolving complex cellular composition in our fetal human tissue spatial transcriptomics data.

(9) Figure 3: Cluster 9 is identified as endothelial, yet it includes markers such as MYH11 among its top genes, a gene more commonly associated with cells at the base of the aorta. This raises questions about the accuracy of the cluster annotation.

We could not find the definition of cluster 9 as endothelial to which the reviewer refers to. In Fig 3, both in the result text and in the figure legend, cluster 9 is identified as smooth muscle, which is consistent with MYH11 expression. The endothelial cluster is shown in Fig S3C.

(10) The approach used to trace embryonic signatures in adult cells, based on overlap with the top 100 genes in embryonic clusters, relies largely on gene expression similarity, without incorporating lineage inference tools such as RNA velocity or pseudotime analysis. This limits the ability to distinguish true developmental relationships from shared functional programs. I believe that the use of aggregated adult samples may mask individual variability. Validation in separate samples (AV1 and AV3) lacks statistical rigor. The observed lower expression of embryonic genes in adult cells further complicates interpretation, raising the possibility that these signatures reflect residual expression rather than persistent lineage markers.

We thank the reviewer for the opportunity to clarify our approach.

We fully agree that tools such as RNA velocity and pseudotime are powerful for capturing short-term dynamic transcriptional changes and inferring lineage trajectories within continuous developmental processes. Indeed, we applied RNA velocity and identified a transition between clusters 7 and 4 in embryonic cells (Fig 2). However, as noted in the Results section, “trajectory inference methods failed to establish lineage relationships between embryonic and fetal populations”. These methods assume temporal continuity and comparable transcriptional kinetics between cells. When comparing samples separated by large developmental intervals (e.g., embryonic versus adult tissues), these assumptions do not hold: RNA velocity vectors become unreliable and may even yield biologically meaningless directions. Therefore, rather than forcing a continuous trajectory across temporally distant datasets, we employed an anchoring approach designed to identify conserved transcriptional programs and potential lineage correspondences between embryonic and adult cell types.

To address the concern about individual variability, we performed analyses both on aggregated adult samples and on individual replicates (AV1 and AV3). The results were highly consistent across both levels of analysis, and statistical significance was supported by very low p-values, indicating that the observed patterns are robust and reproducible. We therefore believe our analysis in independent samples is statistically sound.

Finally, we agree that adult cells display lower expression of embryonic genes, and we acknowledge that these signatures may represent residual rather than persistent expression. This observation aligns with our intended interpretation: our goal was not to demonstrate enduring embryonic marker expression, but to highlight that adult cells retain transcriptional traces that connect them to their developmental origins.

Reviewer #3 (Recommendations for the authors):

(1) Please clarify if MEIS1, JAG1, ROR1, PRDM6 have been previously implicated in neural crest cell development. Are these then new potential regulators of neural crest cells? The same applies to SOX6 for the mesodermal population.

The main reason for selecting these genes (MEIS1, JAG1, ROR1, and PRDM6 in cluster 20, and SOX6 in cluster 4) is that they serve as distinctive markers of specific embryonic clusters. Because their expression remains restricted at later developmental stages, they allow reliable tracing of bona fide descendant cells originating from cluster 20 and cluster 4 into fetal and adult tissues. Importantly, MEIS1, JAG1, ROR1, and PRDM6 were not chosen as new potential regulators of neural crest (NC) cells, but rather because their expression is enriched in cluster 20 and remains restricted at later developmental stages, allowing reliable tracing of bona fide descendant cells originating from cluster 20. Since cluster 20 is, based on transcriptional profiles, the embryonic mesenchymal cluster most closely related to the NC lineage, these markers enable lineage tracing of NC-descendent cells. Nonetheless, these genes have all been linked to neural crest biology, either through known functional roles or through specific expression patterns associated with NC development.

Similarly, SOX6 was selected for its restricted expression in cluster 4, a pattern that is preserved in its descendant populations, making it a suitable marker for tracking the mesoderm-derived lineage.

(2) Please comment in the text whether any regional transcriptional differences (rather than cell type differences) were detected between the aortic and pulmonary regions.

We have added the following text to the result section related to Fig 3: “No molecular differences or distinguishing markers were identified between the aortic and pulmonary valves.”

(3) There appear to be no myocardial cells in the adult valve tissue - the authors could discuss what the fate of myocardium is in the embryonic OFT. Are they only looking at a subset of derivatives of the embryonic OFT?

Our adult dataset represents the aortic valve complex and adjacent arterial root tissue (a subset of outflow tract derivatives) rather than the entire outflow tract (this has now been specified in the title). Spatial transcriptomic analysis identified myocardial gene expression within the ventricular and outflow tract walls at CS16-19, but not within the valve leaflet cluster (Queen et al., 2023). This is consistent with previous observations that myocardium contributes to the arterial root and supports early cushion formation, but does not persist in mature valve tissue, which becomes predominantly fibrous and populated by valve interstitial cells. This explanation has been added to the analysis of cell populations in the valves.

(4) Please equate Carnegie stages 13-23 to embryonic days or weeks of gestation in the first paragraph to help the general reader.

We have added the suggested clarification and noted that this period spans four weeks of human development, rather than the three weeks previously indicated. The text has been updated accordingly.

(5) I suggest rewriting the first sentence of the introduction using the plural, as there are many different types of CHD.

The sentence has been changed accordingly.

(6) It would be helpful to add the persistence of embryonic signatures into adult valve cell types in Figure 4E.

We thank the reviewer for this helpful suggestion. To address this point, we have now added an analysis of the persistence of embryonic signatures in adult valve cell types to Figure 4E. Specifically, we selected 10 representative genes from the 100-gene embryonic signature lists of cluster 4 and cluster 20 and projected their expression onto the t-SNE shown in Figure 4E. The combined (module) expression of these 10 genes is now shown in Figure S6E, and the expression of the individual genes is presented in the newly added Figure S7.

We would like to clarify that our statistical framework identifies potential descendant populations based on significant enrichment of an embryonic gene signature. Therefore, individual embryonic genes are not necessarily expected to be expressed exclusively or uniformly within a single adult population.

(7) Please explain how the 2-dimensional plot in 2J relates to the other plots.

The plot originally shown in Fig 2J (now Fig 2K) was generated by applying RNA velocity exclusively to CS16-17 nuclei. Developmental nuclei (excluding adult samples) were subclustered as shown in Fig S2AB, resulting in the 5 clusters of embryonic nuclei analysed in Fig 2J: cardiac muscle (2, 17), endothelial (7), and mesenchymal (4, 20).

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This thoughtful and thorough mechanistic and functional study reports ARHGAP36 as a direct transcriptional target of FOXC1…… Although this study largely represents a robust and near-comprehensive set of focused investigations on a novel target of FOXC1 activity, several significant omissions undercut the generalizability of the findings reported.

(1) It is notable that the volcano plot in Figure 1a does now show evidence of canonical Hedgehog gene regulation, even though the subsequent studies in this paper clearly demonstrate that ARHGAP36 regulates Hedgehog signal transduction. Is this because canonical Hedgehog target genes (GLI1, PTCH1, SUFU) simply weren't labeled? Or is there a technical limitation that needs to be clarified? A note about Hedgehog target genes is made in conjunction with Table S1, but the justification or basis of defining these genes as Hedgehog targets is unclear. More broadly, it would be useful to see ontology analyses from these gene expression data to understand FOXC1 target genes more broadly. Ontology analyses are included in a supplementary table, but network visualizations would be much preferred.

Space constraints precluded labelling the Volcano plot with all 285 significantly differentially expressed genes. So rather than just Hedgehog pathway members, the most dysregulated were labelled (those with a 4-fold change: -2 <log\_2\> +2) and the full list of DEGs provided in the supplemental excel file. We have added the suggested network analysis, and for additional rigor also included protein interaction partners of Gli1 and Arhgap36 (Fig. S12).

(2) Likewise, the ChIP-seq data in Figure 2 are under-analyzed, focusing only on the ARHGAP36 locus and not more broadly on the FOXC1 gene expression program. This is a missed opportunity that should be remedied with unbiased analyses intersecting differentially expressed FOXC1 peaks with differentially expressed genes from RNA-sequencing data displayed in Figure 1.

We agree that genome-wide analysis of ChIP-seq data from Foxc1 over-expression is worthwhile, not least for diverse malignancies where FOXC1 is over-expressed. We chose to restrict the focus of this paper in order to define, as comprehensively as we could, the FOXC1 - ARHGAP36 relationship. Our ChIP and RNA-seq datasets are freely available to other researchers via GEO (GSE297865/GSE297719). Our future manuscript is integrating ChIP-seq and RNA-seq with ATAC-seq: replicate ATAC-seq experiments permit rigorous characterization of genes transcriptionally regulated by Foxc1 as well as Foxc1’s pioneering abilities. However, these additional assays, and particularly validation of findings, take significant time and so lie beyond the scope of the current manuscript.

(3) RNA-seq and ChIP-seq data strongly suggest that FOXC1 regulates ARHGAP36 expression, and the authors convincingly identify genomic segments at the ARHGAP36 locus where FOXC1 binds, but they do not test if FOXC1 specifically activates this locus through the creation of a luciferase or similar promoter reporter. Such a reagent and associated experiments would not only strengthen the primary argument of this investigation but could serve as a valuable resource for the community of scientists investigating FOXC1, ARHGAP36, the Hedgehog pathway, and related biological processes. CRISPRi targeting of the identified regions of the ARHGAP locus is a useful step in the right direction, but these experiments are not done in a way to demonstrate FOXC1 dependency.

We agree and undertook the suggested luciferase reporter assays. The results demonstrate that transcriptional activity is dependent on Foxc1 and abrogated by mutation of the predicted Foxc1binding motifs (Fig. S8).

(4) It would be useful to see individual fluorescence channels in association with images in Figure 3b.

The figure has been revised to provide individual fluorescence channel data, as suggested.

(5) Perhaps the most significant limitation of this study is the omission of in vivo data, a shortcoming the authors partly mitigate through the incorporation of clinical outcome data from pediatric neuroblastoma patients in the context of ARHGAP36 expression. The authors also mention that high levels of ARHGAP36 expression were also detected in "specific CNS, breast, lung, and neuroendocrine tumors," but do not provide clinical outcome data for these cohorts. Such analyses would be useful to understand the generalizability of their findings across different cancer types. More broadly, how were high, medium, and low levels of ARHGAP36 expression identified? "Terciles" are mentioned, but such an approach is not experimentally rigorous, and RPA or related approaches (nested rank statistics, etc) are recommended to find optimal cutpoints for ARHGAP36 expression in the context of neuroblastoma, "specific CNS, breast, lung, and neuroendocrine" tumor outcomes.

The issue of analyzing in vivo data for neuroblastoma is addressed in more detail below, as it is also raised by the other reviewers. The neuroblastoma data represent the initial findings after the Foxc1Arhgap36 link was defined. There is vastly more that could and should be undertaken to determine mechanism(s) for ARHGAP36’s beneficial association with this tumor’ survival. This is the ongoing focus for the lab.

The original text omitted details of the cancer expression datasets surveyed that revealed high levels of ARHGAP36 expression were also detected in "specific CNS, breast, lung, and neuroendocrine tumors". This oversight has been corrected – when submitting, we omitted to upload a supplemental file (Table S4) that provided these data, which were derived from the following four sites (TCGA, TARGET, PCAWG and CCLE). However, these excellent online resources infrequently provide clinical outcome data.

The three independent neuroblastoma cohorts were analyzed identically. Each was stratified into an ordered dataset for ARHGAP36 expression, and then divided into three equal-sized groups [terciles]. Stratification into smaller subgroups [quartiles/quintiles] would have been equally feasible. The same methodology is used by the UCSC Xena browser for Kaplan-Meier survival analysis, and offers the advantage of avoiding a priori assumptions; it is thus agnostic regarding the data. We agree that there is scope for additional approaches, including recursive partitioning analyses, but suggest it may be better to reserve these for the future, not least in analyses that test the reported ARHGAP36-survival association in additional neuroblastoma datasets.

Reviewer #2 (Public review):

FOXC1 is a transcription factor essential for the development of neural crest-derived tissues and has been identified as a key biomarker in various cancers. … Together, these findings uncover a novel FOXC1-ARHGAP36 regulatory axis that modulates Hh and PKA signaling, offering new insights into both normal development and cancer progression.

The main strengths of the study are:

(1) Identification of a novel signaling pathway involving FOXC1 and ARHGAP36, which may play a critical role in both normal development and cancer biology.

(2) Mechanistic investigation using RNA-seq, ChIP-seq, and functional assays to elucidate how FOXC1 regulates ARHGAP36 and how this axis modulates Hh signaling.

(3) Clinical relevance demonstrated through analysis of neuroblastoma patient datasets, linking ARHGAP36 expression to improved 5-year overall survival.

The main weaknesses of the study are:

(1) Lack of validation in neuroblastoma models - the study does not directly test its findings in neuroblastoma cell models, limiting translational relevance.

We agree that the mechanisms by which increased ARHGAP36 levels are protective, are important to define. Despite experiments over many months manipulating ARHGAP36 expression, that induce quite rapid death of neuroblastoma cells in vitro, the precise mechanism(s) remain unresolved. Currently, we are endogenously labelling multiple neuroblastoma lines with Histone 2B-mCherry to facilitate live cell imaging and differentiate effects on proliferation and apoptosis. In the interim, we believe publication of the current dataset allows other researchers to independently test our findings for this pediatric malignancy. We are also establishing collaborations to access patient tissue samples, that will facilitate investigation of non cell autonomous mechanisms mediated via the tumor microenvironment.

(2) Incomplete mechanistic insight into PKA regulation - the study does not fully elucidate how FOXC1-ARHGAP36 regulates PKAC activity at the molecular level.

Other laboratories elegantly demonstrated that ARHGAP36’s effect on Hedgehog output is mediated by one motif blocking PKAC activity and the targeting of PKAC for degradation [PMIDs 25024229, 27713425, 30598432]. With these effects well-established, we limited experiments to confirming that Foxc1induced Arhgap36 reduced PKAC, and pT197 PKAC levels, to those of ectopic Arhgap36 expression.

(3) Insufficient discussion of clinical outcome data - while ARHGAP36 expression correlates with improved survival in neuroblastoma, the manuscript lacks a clear interpretation of this unexpected finding, especially given the known oncogenic roles of FOXC1, ARHGAP36, and Hh signaling.

ARHGAP36 expression may influence neuroblastoma survival via multiple mechanisms. Considering just canonical Hedgehog, possibilities include: cell cycle modulation, symmetric vs asymmetric cell division, maintenance of cancer stem cells, EMT, metastasis… Others include Hedgehog’s anti-apoptotic roles and the diverse mechanisms by which PKA influences cell function and survival. Faced with such diversity, we focused the discussion on what the presented data demonstrate.

Reviewer #3 (Public review):

Summary:

The focus of the research is to understand how transcription factors with high expression in neural crest cell-derived cancers (e.g., neuroblastoma) and roles in neural crest cell development function to promote malignancy. The focus is on the transcription factor FOXC1 and using murine cell culture, gain- and loss-of-function approaches, and ChIP profiling, among other techniques, to place PKC inhibitor ARHGAP36 mechanistically between FOXC1 and another pathway associated with malignancy, Sonic Hedgehog (SHH).

Strengths:

Major strengths are the mechanistic approaches to identify FOXC1 direct targets, definitively showing that FOXC1 transcriptional regulation of ARHGAP36 leads to dysregulation of SHH signaling downstream of ARHGAP36 inhibition of PKC. Starting from a screen of Foxc1 OE to get to ARHGAP36 and then using genetic and pharmacological manipulation to work through the mechanism is very well done. There is data that will be of use to others studying FOXC1 in mesenchymal cell types, in particular, the FOXC1 ChIP-seq.

Weaknesses:

Work is almost all performed in NIH3T3 or similar cells (mouse cells, not patient or mouse-derived cancer cells), so the link to neuroblastoma that forms the major motivation of the work is not clear. The authors look at ARHGAP36 levels in association with the neuroblastoma patient survival; however, the finding, though interesting and quite compelling, is misaligned with what the literature shows about FOXC1 and SHH, their high expression is associated with increased malignancy (also maybe worse outcomes?). Therefore, ARHGAP36 expression may be more complicated in a tumor cell or may be unrelated to FOXC1 or SHH, leaving one to wonder what the work in NIH3T3 cells, though well done, is telling us about the mechanisms of FOXC1 as an oncogene in neuroblastoma cells or in any type of cancer cell. Does it really function as an SHH activator to drive tumor growth? The 'oncogenic relevance' and 'contribution to malignancy' claimed in the last paragraph of the introduction are currently weakly supported by the data as presented. This could be improved by studying some of these mechanisms in patient-derived neuroblastoma cells with high FOXC1 expression. Does inhibiting FOXC1 change SHH and ARHGAP36 and have any effect on cell proliferation or migration? Alternatively, does OE of FOXC1 in NIH3T3 cells increase their migration or stimulate proliferation in some way, and is this dependent on ARHGAP36 or SHH? Application of their mechanistic approaches in cancer cells or looking for hallmarks of cancer phenotypes with FOXC1 OE (and dependent on SHH or ARHGAP36) could help to make a link with cellular phenotypes of malignant cells.

The manuscript stems from the lab’s findings that Foxc1 influences cilia-mediated signaling (Hedgehog and PDGFRalpha), offering an explanation for FOXC1’s pleiotropic phenotypes. Due to FOXC1’s largely unexplained roles in malignancy, the effects on Hedgehog prompted investigation of differential gene expression in NIH3T3 cells when Foxc1 was over-expressed. This identified Arhgap36 as a prime candidate for the Hedgehog pathway alterations, and most of the paper reports the characterization of this relationship. The final, small component of the paper, tests the relevance in neural crest derived cells, where Foxc1 has key roles. Neuroblastoma’s frequent lethality has created a network of highly supportive researchers with shared datasets, and these survival data were assayed. This in turn revealed that high levels of ARHGAP36 expression were associated with a favorable survival outcome.

Defining the underlying molecular mechanisms for this novel association is clearly important. As outlined above, one challenge reflects the diversity of potential mechanisms, coupled with the requirement to validate those identified from 2-D culture in patient-derived tumor explants as well as immuno-deficient model organisms. Such experiments take significant time, and our present focus is on manipulating ARHGAP36 expression directly, rather than by altering FOXC1 expression, which inevitably has even more diverse effects.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The study would be strengthened by validating key findings, such as the resistance to Hh inhibition, in neuroblastoma cell lines to enhance disease relevance.

Planned future experiments include in vitro evaluation of PKA antagonists and agonists on neuroblastoma survival.

The authors show that FOXC1/ARHGAP36 reduces PKAC protein levels; however, it is unclear whether this regulation occurs at the transcriptional level. Assessing PKAC mRNA expression would help explain the mechanism. Additionally, if PKAC is transcriptionally downregulated, overexpression of PKAC can be used to test whether it reverses the FOXC1/ARHGAP36induced activation of Hh signaling.

The RNA-sequencing data exclude this possibility at the transcriptional level, since PKA is not significantly differentially expressed (Table S1). Instead, Figures 1&3 support Foxc1 inducing Arhgap36 expression, with elevated Arhgap36 protein levels reducing those of PKAC and catalytically active pT197 PKAC, in both the cytoplasm and adjacent to the basal body.

The Discussion should address the potential effects of ARHGAP36 overexpression on other signaling pathways-particularly Hh and PKA signaling and PKA in neuroblastoma. These effects may help interpret the observed association between ARHGAP36 expression and clinical outcomes in patients. Of note, it has been reported that Hh may correlate with better survival in neuroblastoma (Cancers, 2021 Apr 15;13(8):1908; J Pediatr Surg. 2010 Dec;45(12):2299).

Both Hedgehog signaling and protein kinase A have broad effects on normal cell biology, that are likely more extensive in malignant cells. Consequently, although tempting to propose why ARHAGP36 overexpression is associated with enhanced survival, it may be better to wait until the causative mechanisms have been defined.

If treatment information for the patient cohorts is available, it should be included as it may enhance the interpretability of the survival analyses.

This is an excellent suggestion, although at present this information is not available to us. As the manuscript moves forward to publication, we will be liaising with the corresponding authors of the three datasets [GSE49711, E-MTAB-178191 and TARGET] to explore such additional clinical possibilities.

The 'A' label in Figures S9 and S10 should be removed, as neither figure contains sub-panels.

This has been corrected, as suggested.

Reviewer #3 (Recommendations for the authors):

Other comments:

(1) Figure 5A, B: Unclear how meaningful the inhibitor experiments are in the absence of SHH (presumable none in the media or made by NIH3T3 cells?), other than as a control for the FOXC1 OE treated with Smo antagonists. A potentially better experiment could be to take malignant cells with high FOXC1 and high SHH signaling and put on Smo inhibitors.

Figure 5A demonstrates Foxc1’s induction of GLI1 expression is not dependent on Hedgehog ligand. While certainly feasible to repeat in malignant cells strongly expressing FOXC1, doing this comprehensively would require testing lines from many or all of the ~15 malignancies where FOXC1 has a defined contribution.

(2) Figure 6: the Gli2-mGFP seem to have higher levels of ciliary Sufu, they also have higher levels of Gli1 (see Figure 1C), does the Gli2-mGFP expression change SHH signaling? What controls have the authors done to test if this is a serious confound in their studies? They use it for most experiments, this is important to address.

Although Gli2-mGFP expression affects Hedgehog signaling, in the absence of Gli2 (e.g. untransformed NIH3T3) Foxc1 induces Arhgap36 expression. The scope for interaction between Foxc1 and Gli2 represents an additional motivation for the ATAC-seq experiments described above to better determine if these two transcription factors have synergistic effects.

(3) Figure 3B: (1) Please use color-blind friendly LUTs for the signals (same comment for other figures), (2) The Gli2-mGFP line with the current color scheme is confusing; it looks like only 647 and 555 secondaries were used, did they not image with the mGFP? Why not? (3) What is the evidence that these are basal bodies? (4) Why did the authors use cycloheximide in these IF experiments? Was this also done in other methods? The reasoning behind this is missing.

For now, we have included separate channels for Figure 3. In future manuscripts we will adopt the suggestion of moving to either magenta and green, or cyan and magenta combinations for depicting immunofluorescence.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors' goal was to advance the understanding of metabolic flux in the bradyzoite cyst form of the parasite T. gondii, since this is a major form of transmission of this ubiquitous parasite, but very little is understood about cyst metabolism and growth.

Nonetheless, this is an important advance in understanding and targeting bradyzoite growth.

Strengths:

The study used a newly developed technique for growing T. gondii cystic parasites in a human muscle-cell myotube format, which enables culturing and analysis of cysts. This enabled screening of a set of anti-parasitic compounds to identify those that inhibit growth in both vegetative (tachyzoite) forms and bradyzoites (cysts). Three of these compounds were used for comparative Metabolomic profiling to demonstrate differences in metabolism between the two cellular forms.

One of the compounds yielded a pattern consistent with targeting the mitochondrial bc1 complex, and suggest a role for this complex in metabolism in the bradyzoite form, an important advance in understanding this life stage.

Weaknesses:

Studies such as these provide important insights into the overall metabolic differences between different life stages, and they also underscore the challenge with interpreting individual patterns caused by metabolic inhibitors due to the systemic level of some of some targets, so that some observed effects are indirect consequences of the inhibitor action. While the authors make a compelling argument for focusing on the role of the bc1 complex, there are some inconsistencies in the some patterns that underscore the complexity of metabolic systems.

Thank you for reviewing the revised manuscript.

Reviewer #2 (Public review):

Summary:

A particular challenge in treating infections caused by the parasite Toxoplasma gondii is to target (and ultimately clear) the tissue cysts that persist for the lifetime of an infected individual. The study by Maus and colleagues leverages the development of a powerful in vitro culture system for the cyst-forming bradyzoite stage of Toxoplasma parasites to screen a compound library for candidate inhibitors of parasite proliferation and survival. They identify numerous inhibitors capable of inhibiting both the disease-causing tachyzoite and the cyst-forming bradyzoite stages of the parasite. To characterize the potential targets of some of these inhibitors, they undertake metabolomic analyses. The metabolic signatures from these analyses lead them to identify one compound (MMV1028806) that interferes with aspects of parasite mitochondrial metabolism. In the revised version of the manuscript, the authors present convincing evidence that MMV1028806 targets the mitochondrial electron transport (ETC) chain of the parasite (although they don't identify the actual target in the ETC). The revised manuscript also nicely addresses my other criticisms of the original version. Overall, the study presents an exciting approach for identifying and characterizing much-needed inhibitors for targeting tissue cysts in these parasites.

Strengths:

The study presents convincing proof-of-principle evidence that the myotube-based in vitro culture system for T. gondii bradyzoites can be used to screen compound libraries, enabling the identification of compounds that target the proliferation and/or survival of this stage of the parasite. The study also utilizes metabolomic approaches to characterize metabolic 'signatures' that provide clues to the potential targets of candidate inhibitors. In addition to insights into candidate bradyzoite inhibitors, the study also provides new insights into the physiological role of the mitochondrial electron transport chain of bradyzoites, and raises a host of interesting questions around the functional roles of mitochondria in this stage of the parasite.

Weaknesses:

In the revised manuscript, the authors have included additional oxygen consumption rate data that indicate that MMV1028806 targets the mitochondrial electron transport chain (ETC). These data are convincing. On line 481, the authors state that "treatments with ATQ, BPQ, MMV1028806, and antimycin A resulted in substantially reduced oxygen consumption levels relative to the DMSO control and suggest indeed a blockage of the mETC consistent with the inhibition of the bc1-complex." The OCR assay the authors use is still only an indirect measure of bc1 activity. Given that most OCR-inhibiting compounds in T. gondii are bc1 inhibitors, it is possible (and perhaps likely) that MMV1028806 is targeting this complex. However, the data cannot rule out that it is targeting another component of the ETC (or potentially even a TCA cycle enzyme). Without a direct test that MMV1028806 inhibits bc1 complex activity, the authors should be more cautious in their interpretation (e.g. by acknowledging the limitations of their conclusion, or acknowledging other possible targets). Similarly, the conclusion on line Line 622 that "... we confirmed the bc1-complex as a target" is overstating the findings. The phrasing on lines 683-695 is more appropriate: "... suggesting that it also targets complex III or a functionally linked site within the mitochondrial electron transport chain."

We are grateful for he thorough review of the updated manuscript and the identification the minor issues. We addressed all of them as detailed below. We also tempered our conclusions regarding the identification of the bc1-complex as a target in line 616:

“In addition to abundance data, Additionally, we confirmed the bc1-complex as a target by monitoring the incorporation of ¹³C and ¹⁵N stable isotopes from glucose and glutamine, respectively, into TCA cycle and pyrimidine biosynthesis intermediates suggest the bc1-complex as a target”

Reviewer #3 (Public review):

Summary:

The authors described an exciting 400-drug screening using a MMV pathogen box to select compounds that effectively affect the medically important Toxoplasma parasite bradyzoite stage. This work utilises a bradyzoites culture technique that was published recently by the same group. They focused on compounds that affected directly the mitochondria electron transport chain (mETC) bc1-complex and compared with other bc1 inhibitors described in the literature such as atovaquone and HDQs. They further provide metabolomics analysis of inhibited parasites which serves to provide support for the target and to characterise the outcome of the different inhibitors.

Strengths:

This work is important as, until now, there are no effective drugs that clear cysts during T. gondii infection. So, the discovery of new inhibitors that are effective against this parasite-stage in culture and thus have the potential to battle chronic infection is needed. The further metabolic characterization provides indirect target validation and highlight different metabolic outcome for different inhibitors. The latter forms the basis for new studies in the field to understand the mode of inhibition and mechanism of bc1-complex function in detail.

The authors focused in the function of one compound, MMV1028806, that is demonstrated to have a similar metabolic outcome to burvaquone. Furthermore, the authors evaluated the importance of ATP production in tachyzoite and bradyzoites stages and under atovaquone/HDQs drugs.

Thank you for reviewing the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Thanks for making appropriate updates. I believe it makes the report stronger. Just please double-check proof-reading in newly added text: for example "integration" is misspelled in Figure 4 legend (C, E).

Typos have been corrected throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

I congratulate the authors on an excellent study. I have several minor comments for the authors to consider before publication.

Line 99. Schistosoma –

Corrected

Line 123. What was the pH of the bicarb-free RPMI medium?

Added “at pH 7.2”

Line 218 (and again on line 687). "RHku80" - are these just standard RH strain parasites? Or do the authors mean to imply that the ku80 gene has been knocked out in this line? If the latter, RH∆ku80 may be a better way to describe this line.

We harmonized all mentions of this strain to RH∆ku80.

Line 225. "Parasites were incubated in medium with one of the following treatments ..." How long were the parasites incubated in the different treatments before the plate was read? Was there any preincubation? I think not, but it would help to state this so the reader can appreciate that the effects of the compounds on OCR is likely an immediate (rather than a secondary) effect.

This is indeed a good suggestion. There was no pre-incubation and we added changed the text to: “Parasites were incubated in medium with one of the following treatments immediately before measurement: … “

Figure S2A. Check the spelling of Toxoplasmosis.

Done, we corrected this sentence.

Figure S2B. do you mean 'tachyzoidal' or 'tachyzocidal'? 'bradyzoidal' or 'bradyzocidal'?

We clarified the formulation of the legends for Fig S2.

Figure S2D. The "Tachyzoite lowest cytotoxicity" and "Bradyzoite lowest cytotoxicity" columns are, I think, depicting compound toxicity in host cells. Would it be clearer to rename these columns relative to the host cells being tested? e.g. "HFF/KD3 myotube lowest cytotoxicity"

Good suggestion and we changed the designation accordingly.

Line 369. "We found that tachyzocidal, bradyzocidal and dually active compounds possess a statistically significantly higher lipophilicity and this trend appeared more accentuated for bradyzocidal and dually active compounds." Significantly higher than what? Need to be clearer about the comparison being made: i.e. to non-active compounds.

You are correct and we corrected this sentence accordingly.

Line 500. "we attribute these changes to inhibition of host mitochondria (Fig. 5A)." The reason for referencing Figure 5A here isn't clear. Do the authors mean to point out that host mitochondrial membrane potential is affected by compound treatment? This could be stated more clearly.

We deleted the reference to Fig 5A. We did not systematically measure the effect of the inhibitors on the membrane potential of the host mitochondria. We also changed the sentence to emphasize the speculative nature of this assertion: “we attribute these changes to potential inhibitory effects on host mitochondria”.

Line 840. 'hurdling mechanisms'. The authors don't explain what they mean by this expression.

We truncated the figure title to: “Untargeted metabolomic analysis of bradyzoites treated with bc1-complex inhibitors shows an energy imbalance.”

Author response:

Public Reviews:

Reviewer #1 (Public Review):

By mapping H3K4me2 in mouse oocytes and pre-implantation embryos, the authors aim to elucidate how this histone modification is erased and re-established during the parental-to-zygotic transition, as well as how the reprogramming of H3K4me2 regulates gene expression and facilitates zygotic genome activation.

Employing an improved CUT&RUN approach, the authors successfully generated H3K4me2 profiling data from a limited number of embryos. While the profiling experiments are very well executed, several weaknesses, particularly in data analysis, are apparent:

(1) The study emphasizes H3K4me2, which often serves as a precursor to H3K4me3, a well-studied modification during early development. Analyzing the new H3K4me2 dataset alongside published H3K4me3 data is crucial for comprehensively understanding epigenetic reprogramming post-fertilization and the interplay between histone modifications. However, the current analysis is preliminary and lacks depth.

Thank you very much for your valuable suggestions. The data of histone H3K4me3 in humans and mice has been published，and our previous data revealed the unique pattern of H3K4me3 during early human embryos and oocytes (Science. 2019 Jul 26;365(6451):353-360.) . So, this study mainly focuses on the localization of H3K4me2 in mouse oocytes and preimplantation embryos, how it is erased and re-established during mammalian parental-to-zygote transition, and its function. The combined analysis of H3K4me2 and H3K4me3 is not our main work, but it is not ruled out that there may be new discoveries between these two histones. Previously, our data tended to show that the H3K4me2 not only acts as a precursor of H3K4me3, but also plays its role independently.

(2) Tranylcypromine (TCP) is known as an irreversible inhibitor of monoamine oxidase and LSD1. While the authors suggest TCP inhibits the expression of LSD2, this assertion is questionable. Given TCP's potential non-specific effects in cells, conclusions related to the experiments using TCP should be made with caution.

Thank you for pointing this out, and we thank the reviewer again for the important suggestion. We found that the previous study (.Binda C, Valente S, Romanenghi M, Pilotto S, Cirilli R, Karytinos A, Ciossani G, Botrugno OA, Forneris F, Tardugno M, Edmondson DE, Minucci S, Mattevi A, Mai A. Biochemical, structural, and biological evaluation of tranylcypromine derivatives as inhibitors of histone demethylases LSD1 and LSD2. J Am Chem Soc. 2010 May 19;132(19):6827-33.) indicated that TCP was a non-reversible inhibitor of LSD1 and LSD2 (Human LSD2/KDM1b/AOF1 Regulates Gene Transcription by Modulating Intragenic H3K4me2 Methylation, Mol Cell. 2010 Jul 30; 39(2): 222–233.), but according to our data, the content of LSD1 was very low in the early stages of mouse embryos, which mainly inhibited the function of LSD2.

(3) Some batches of H3K4me2 antibody are known to cross-react with H3K4me3. Has the H3K4me2 antibody used in CUT&RUN been tested for such cross-reactivity? Heatmaps in the figures indeed show similar distribution for H3K4me2 and H3K4me3, further raising concerns about antibody specificity.

We thank the reviewer for the insightful comments. The H3K4me2 antibody was purchased from Millipore (cat. 07030). Figure 2A shows the specific enrichment area of H3K4me2 in promoter and distal region. Some batches of H3K4me2 antibody are known to cross-react with H3K4me3, but the H3K4me2 antibody we used in our CUT&RUN seems to have Low cross-reactivity.

(4) Certain statements lack supporting references or figures (examples on page 9 can be found on line 245, line 254, and line 258).

Thank you for pointing this out, and we will add references to support the statement in the paper as suggested.

(5) Extensive language editing is recommended to clarify ambiguous sentences. Additionally, caution should be taken to avoid overstatement - most analyses in this study only suggest correlation rather than causality.

Thank you for your kind comments. We will revise the expression in the manuscript later.

Reviewer #2 (Public Review):

Chong Wang et al. investigated the role of H3K4me2 during the reprogramming processes in mouse preimplantation embryos. The authors show that H3K4me2 is erased from GV to MII oocytes and re-established in the late 2-cell stage by performing Cut & Run H3K4me2 and immunofluorescence staining. Erasure and re-establishment of H3K4me2 have not been studied well, and profiling of H3K4me2 in germ cells and preimplantation embryos is valuable to understanding the reprogramming process and epigenetic inheritance.

(1) The authors claim that the Cut & Run worked for MII oocytes, zygotes, and the 2-cell embryos. However, it is unclear if H3K4me2 is erased during the stage or if the Cut & Run did not work for these samples. To support the hypothesis of the erasure of H3K4me2, the authors conducted immunofluorescence staining, and H3k4me2 was undetected in the MII oocyte, PN5, and 2-cell stage. However, the published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage ((Ancelin et al., 2016; Shao et al., 2014)). The authors need to cite these papers and discuss the contradictory findings.

The authors used 165 MII oocytes and 190 GV oocytes for the Cut & Run. The amount of DNA in MII oocytes is halved because of the emission of the first polar body. Would it be a reason that H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes?

First of all, thank you for your valuable advice. The published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage (Ancelin et al., 2016), which is interesting. I think we may have used different parameters in the confocal laser shooting process. We used the same parameter to continuously shoot the blastocyst stage from the GV stage. If we only shot the fertilized egg and the 2-cell stage, I think we may also see weak fluorescence at the 2-cell stage under different parameters. We will refer to this reference and discuss it in the resubmitted version.

Moreover, you mentioned the H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes, because the MII expelled the polar body. There is no problem with this logic. However, the first polar body expelled from the MII stage is still in the zona pellucida, and we also collected the polar body in the CUT&RUN experiment; Therefore, compared to GV, the DNA content of MII samples is not halved. After further discussion, we believe that the reduction of H3K4me2 peaks in MII stage compared with GV stage may be closely related to oocyte maturation. It is the specific modification of histones in different forms at different times that affects the chromatin structure change appropriately with the different stages of meiosis. At present, it has been confirmed that H3K4me3 gradually decreases from GV to MII stage during the maturation of human oocytes. H3K27me3 did not change from GV to MII stage.

In Figure 3C, 98% (13,183/13,428) of H3K4me2 marked genes in GV oocytes overlap with those in the 4-cell stage. Furthermore, 92% (14,049/15,112) of H3K4me2 marked genes in sperm overlap with those in the 4-cell stage. Therefore, most regions maintain germ line-derived H3K4me2 in the 4-cell stage. The authors need to clarify which regions of germ line-derived H3K4me2 are maintained or erased in preimplantation embryos. Additionally, it would be interesting to investigate which regions show the parental allele-specific H3K4me2 in preimplantation embryos since the authors used hybrid preimplantation embryos (B6 x DBA).

Thank you very much for your suggestion. Further analysis of which regions show the parental allele-specific H3K4me2 in preimplantation embryos will make the study more interesting. We will discuss this in depth in resubmitted vision.

(2) The authors claim that Kdm1a is rarely expressed during mouse embryonic development (Figure 4A). However, the published paper showed that KDM1a is present in the zygote and 2-cell stage using immunostaining and western blotting (Ancelin et al., 2016). Additionally, this paper showed that depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage, and therefore, KDM1a is functionally important in early development.

The authors should have cited the paper and described the role of KDM1a in early embryos.

In the analysis of this experiment, we believe that in the early embryonic development of mice, the expression of KDM1A is lower than that of KDM1B, which is relative. Similarly, the transcriptome data we cite also show that KDM1A is expressed at elevated levels during oocyte maturation and fertilization compared to immature oocytes. In addition, the effects of loss of maternal KDM1a on embryonic development were not discussed. We believe that the absence of maternal KDM1b blocks embryonic development, and we will cite and discus the references later.

(3) The authors used the published RNA data set and interpreted that KDM1B (LSD2) was highly expressed at the MII stage (Figure S3A). However, the heat map shows that KDM1B expression is high in growing oocytes but not at 8w_oocytes and MII oocytes. The authors need to interpret the data accurately.

After re-checking the data, we found that there was a problem with the normalization method of our heat map, and we will re-make the heatmap and submit it in the modified version. With reference to Figure 4A, the content of Kdm1b is indeed higher than that of Kdm1a.

(4) All embryos in the TCP group were arrested at the four-cell stage. Embryos generated from KDM1b KO females can survive until E10.5 (Ciccone et al., 2009); therefore, TCP-treated embryos show a more severe phenotype than oocyte-derived KDM1b deleted embryos. Depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage ((Ancelin et al., 2016)). The authors need to examine whether TCP treatment affects KDM1a expression. Western blotting would be recommended to quantify the expression of KDM1A and KDM1B in the TCP-treated embryos.

We will further dig the transcriptome data to confirm the specificity of TCP to KDM1b. In addition, the intervention of TCP on the whole fertilized egg in this study increased the H3K4me2 content, and the embryo development retarding effect was more significant than that obtained by crossing with normal paternal lines after knocking down KDM1B from the mother.

(5) H3K4me2 is increased dramatically in the TCP-treated embryos in Figure 4 (the intensity is 1,000 times more than the control). However, the Cut & Run H3K4me2 shows that the H3K4me2 signal is increased in 251 genes and decreased in 194 genes in the TCP-treated embryos (Fold changes > 2, P < 0.01). The authors need to explain why the gain of H3K4me2 is less evident in the Cut & Run data set than in the immunofluorescence result.

Thanks a lot for your question. In the experimental group, the fluorescence value of H3K4me2 in IF was increased by 1000 times (Figure 4E), and the expression of H3K4Me2-related genes in CR was up-regulated and down-regulated for a total of 445 changes (Figure 6A). In our opinion, as a semi-quantitative analysis, immunofluorescence cannot be compared with the quantitative analysis method of CR because of the different analysis models and threshold Settings.

References

Ancelin, K., ne Syx, L., Borensztein, M., mie Ranisavljevic, N., Vassilev, I., Briseñ o-Roa, L., Liu, T., Metzger, E., Servant, N., Barillot, E., Chen, C.-J., Schü le, R., & Heard, E. (2016). Maternal LSD1/KDM1A is an essential regulator of chromatin and transcription landscapes during zygotic genome activation. https://doi.org/10.7554/eLife.08851.001

Ciccone, D. N., Su, H., Hevi, S., Gay, F., Lei, H., Bajko, J., Xu, G., Li, E., & Chen, T. (2009). KDM1B is a histone H3K4 demethylase required to establish maternal genomic imprints. Nature, 461(7262), 415-418. https://doi.org/10.1038/nature08315

Shao, G. B., Chen, J. C., Zhang, L. P., Huang, P., Lu, H. Y., Jin, J., Gong, A. H., & Sang, J. R. (2014). Dynamic patterns of histone H3 lysine 4 methyltransferases and demethylases during mouse preimplantation development. In Vitro Cellular and Developmental Biology - Animal, 50(7), 603-613. https://doi.org/10.1007/s11626-014-9741-6

Reviewer #3 (Public Review):

Summary:

This study explores the dynamic reprogramming of histone modification H3K4me2 during the early stages of mammalian embryogenesis. Utilizing the advanced CUT&RUN technique coupled with high-throughput sequencing, the authors investigate the erasure and re-establishment of H3K4me2 in mouse germinal vesicle (GV) oocytes, metaphase II (MII) oocytes, and early embryos.

Strengths:

The findings provide valuable insights into the temporal and spatial dynamics of H3K4me2 and its potential role in zygotic genome activation (ZGA).

Weaknesses:

The study primarily remains descriptive at this point. It would be advantageous to conduct further comprehensive functional validation and mechanistic exploration.

Key areas for improvement include enhancing the innovation and novelty of the study, providing robust functional validation, establishing a clear model for H3K4me2's role, and addressing technical and presentation issues. The text would benefit from the introduction of a novel conceptual framework or model that provides a clear explanation of the functional consequences and molecular mechanisms underlying H3K4me2 reprogramming in the transition from parental to early embryonic development.

While the findings are significant, the current manuscript falls short in several critical areas. Addressing major and minor issues will significantly strengthen the study's contribution to the field of epigenetic reprogramming and embryonic development.

Author response:

Public Reviews:

Reviewer #1 (Public review):

In the manuscript by Li et al., the authors perform a comprehensive study on the template and cofactor determinants of the SARS-CoV-2 nsp13 protein. They find that, alongside the classical processive unwinding ability of helicases driven by ATP consumption, other chaperone-like and ATP-independent functions exist for this enzyme. By testing DNA and RNA oligos in several conformations, the authors show that these functions are highly dependent on template identity, but also on the ratio of ATP to divalent cations. Ultimately, it is suggested that these distinct mechanisms of action are employed by nsp13 to orchestrate viral replication.

Overall, this study provides some novel insights into the functionality of a central and conserved enzyme of a relevant human pathogenic virus. While the approach is important and adds to the field, particularly by characterizing the chaperoning activities and adding G-quadruplexes as templates, previous studies have already identified several determinants of nsp13 template binding and processing in vitro (Sommers et al., 2023, JBC; Park et al., 2025, JBC). In addition, some issues regarding experimental design need to be addressed to increase the cogency and biological relevance of the study.

We thank the reviewer for recognizing the novelty of our work, particularly the ATP-independent chaperone-like activities and G-quadruplex remodeling. We also appreciate the opportunity to clarify the conceptual distinction between our study and the prior work by Sommers et al. (2023) and Park et al. (2025). We fully agree that those studies systematically defined the canonical ATP-driven motor mechanism of Nsp13. Our results on 5′→3′ polarity, DNA preference, and tail/ATP/Mg²⁺ dependence align with these benchmarks, confirming the reliability of our platform.

However, the core novelty of our work lies in revealing that Nsp13 functions as a multifaceted nucleic acid remodeler, integrating motor and non-motor activities within a single protein-a functional regime absent from the JBC papers. Specifically, we uncover three novel layers: 1. Mg²⁺-activated, ATP-independent remodeling of short duplexes and G-quadruplexes. 2. Bidirectional remodeling on duplexes in the Mg²⁺-primed state. 3. Intrinsic chaperone functions including strand annealing and stem-loop restructuring.

Thus, our work fundamentally expands the biochemical model of Nsp13 from a simple ATP-driven motor to a multifunctional, mode-switchable remodeler. We will highlight these distinctions in the revised Discussion. Below, we respond point-by-point to the specific experimental design issues.

(1) Generally, low concentrations of monovalent cations (20 mM), as used throughout this study, may influence helicase activity and artificially enhance protein binding/oligomerization, which could favor the observed chaperoning activity (Venus et al., 2022, Methods). In contrast, some helicases, such as HCV NS3, are inhibited by higher K+ concentrations (Gwack et al., 2004, FEBS). Thus, the influence of higher concentrations of monovalent cations should be tested in relevant assays, as intracellular K+ levels are usually >100 mM. Additionally, this could significantly affect template stability. For instance, in some G4 assays, the addition of the trap already leads to observable duplex formation (Figure 5), which may be due to low K+ conditions.

We thank the reviewer for this critical comment regarding the ionic environment. We agree that monovalent cation concentrations are pivotal for both helicase activity and the structural stability of templates like G4s.

First, we wish to clarify that the final NaCl concentration in our reaction is not 20 mM, as this refers only to the unwinding buffer. Our protein dilution buffer contains 200 mM NaCl, and each 10 μL reaction includes 2 μL of protein, contributing ~40 mM NaCl. With 20 mM from the reaction buffer, the final concentration reaches~60 mM. We will clarify this in the Methods.

Second, our choice of ionic strength is guided by established literature. A survey of 27 published nsp13 studies (Author response table 1) shows that the majority use 20–50 mM monovalent cations, with 20 mM being most common. Mickolajczyk et al. (2021) showed that nsp13 activity is highest at low salt and declines at higher concentrations. Thus, low salt conditions are routinely used to capture nsp13’s intrinsic catalytic activity. The intracellular environment is far more complex, with crowding and interacting proteins that likely modulate helicase behavior. The low-salt conditions are therefore a deliberate simplification to isolate and define enzyme function.

Planned experiments: We fully agree that higher salt concentrations should be tested. In the revision, we will perform key assays such as ATP-independent duplex unwinding and G4 unfolding at ≥100 mM NaCl or KCl to verify that the observed activities persist under more physiological ionic conditions

(2) As in most publications that focus strictly on helicase (or other enzymatic) functions, the activity of the isolated protein is examined. However, particularly in the case of nsp13, core functions rely on other factors, such as nsp7/8 and other components of the replication-transcription complex (RTC). The overall structure and oligomerization state of nsp13 are altered within the complex (Chen et al., 2022, NSMB). The inclusion of such factors in key experiments would greatly improve the biological relevance of the findings.

We agree that examining Nsp13 within the context of the RTC is essential for establishing the biological relevance of our findings. The structural reorganization of Nsp13 upon binding to Nsp12 and Nsp7/8 (Chen et al., 2022) suggests that its enzymatic "mode" may be regulated by its protein partners.

Planned experiments: To address this, we will include the following biochemical characterizations:

(1) Nsp13/12 and Nsp13/7/8 sub-complexes will be examined to dissect the individual contributions of the polymerase and the primase-like factors to Nsp13’s multifaceted activities.

(2) The core RTC (Nsp13/12/7/8) will be used to evaluate how the full assembly modulates the functions of Nsp13 particularly on complex templates like G4 and pseudoknots.

(3) In Figure 4, the authors claim that Mg2+ concentration inhibits RNA unwinding. While this is likely considering previous findings, it must be validated that duplex stabilization is not the primary cause for the observed lower dissociation rates. As the template is only 12 bp long with extensive overhangs, higher ion concentrations may significantly stabilize base pairing by reducing fraying effects. Similarly, in Figure 6, template-dependent effects of Mg2+/ATP should be ruled out.

We thank the reviewer for this insightful suggestion. We agree that it is critical to distinguish whether the observed inhibition of RNA unwinding at higher Mg²⁺ concentrations is due to the physical stabilization of the RNA duplex.

Planned experiments: To address this, we will perform the following characterizations:

(1) We will measure the Tm of the RNA duplex used in Figure 4 across a range of Mg²⁺ concentrations (0, 0.5, and 1.0 mM). This will allow us to quantify the extent to which divalent cations stabilize the duplex RNA. These data will provide a more rigorous interpretation of the Mg²⁺-dependent unwinding in Figure 4.

(2) Similarly, we will perform thermal melting analyses for the various DNA and RNA templates used in Figure 6 under different Mg²⁺/ATP conditions to rule out the template-dependent effects of Mg²⁺/ATP.

(4) It is not entirely clear to me by which principle the templates were chosen. In my opinion, it would improve the overall comparability of the experimental results if, for instance, the blunt-ended duplex had the same sequence as the oligos with overhangs, since factors such as length, G/C content, Tm, etc., may play a significant role in binding and unwinding. Similarly, the oligos for binding and unwinding should be kept somewhat comparable, e.g., the G4 for the binding assay has 3 stacks, whereas RG1 has only 2. This discrepancy could make a significant difference. Thus, key experiments should be repeated using comparable sequence pairs.

We fully agree with the reviewer that maintaining sequence consistency across different assays is essential for a rigorous comparison of nsp13 activities. We apologize for the ambiguity in the initial presentation of our sequences in Table S1.

Planned revisions and experiments:

(1) We wish to clarify that several key substrates were sequence-matched. For unwinding assays, the 12-bp 3′-overhang DNA and blunt-ended DNA share the identical duplex sequence, and the 16-bp 5′-overhang and 3′-overhang DNA substrates are also sequence-matched. For annealing assays, the duplex regions for all DNA substrates (3′, 5′, blunt, and fork) are identical, and the same internal consistency was maintained for all RNA annealing substrates. To make this clear, we will reorganize Table S1 to explicitly group these sequence-paired substrates.

(2) The reviewer also notes discrepancies between binding and unwinding substrates (e.g., the difference in G4 stacks). To ensure direct comparability, we will perform additional experiments: complete binding assays for RG-1 (the 2-stack G4 used in unwinding) to match the functional data, and systematically measure binding affinities for all key unwinding substrates, including 3′-overhang, 5′-overhang, blunt-ended DNA, and the RNA fork.

(5) Moreover, in the initial characterization of the binding abilities (Figure 1), the authors should include blunt-ended controls (duplex/hairpin) and, importantly, a pseudoknot (PK), as these structures are crucial for multiple steps in the viral life cycle (frameshifting, replication). Specifically, the PK in the 3'UTR (Sola et al., 2011, RNA Biology) may be an interesting target structure for unwinding assays, as it recruits the RTC, and, to my knowledge, no studies are available regarding nsp13 function at a PK. This would be particularly interesting in combination with nsp7/8 (Ohyama et al., 2024, JACS Au).

We thank the reviewer for this insightful and inspiring suggestion. Incorporating pseudoknot (PK) structures into our analysis—particularly the well-characterized PK in the 3'UTR (Sola et al., 2011)—represents a significant opportunity to bridge our biochemical findings with the viral life cycle. To address this, we have designed a 3'UTR PK substrate based on recently reported scaffolds (Ohyama et al., 2024).

Planned experiments:

(1) We will expand our initial binding assays (Figure 1) to include blunt-ended duplexes, hairpins, and the 3'UTR PK. This will establish a baseline for how Nsp13 recognizes these structurally distinct and physiologically critical templates.

(2) We will perform unwinding assays to determine whether Nsp13, in its isolated state, possesses the mechanical capability to resolve the complex tertiary interactions within a pseudoknot.

(3) Following the reviewer's insight, we will examine whether the addition of nsp7/8 is required to facilitate the unfolding of the 3'UTR PK.

Together, these experiments will allow us to assess whether Nsp13 is capable of managing one of the most challenging structural obstacles in the SARS-CoV-2 genome.

Reviewer #2 (Public review):

Summary:

The authors are trying to broaden the understanding of SARS-CoV2 Nsp13 activity to show that a single viral protein can accomplish multiple functions. Additionally, they try to show that helicase function is not limited to ATP-driven, unidirectional unwinding.

Strengths: The consistent application of statistics to triplicate experiments is a strength of the manuscript. The ToPif1 control in Figure S12 is a good control.

We thank the reviewer for the insightful assessment and for highlighting the rigor of our experimental design, particularly our reliance on triplicate data with robust statistical validation and the inclusion of the ToPif1 control.

We are especially grateful for the detailed comments provided by the reviewer. We fully recognize that addressing these specific points is essential for strengthening the cogency of our conclusions and improving the overall rigor of the manuscript. These suggestions have provided us with a clear roadmap for further refining our experimental evidence and clarifying our mechanistic interpretations. Below, we respond point-by-point to the specific issues.

Weaknesses:

(1) All the experiments except the one in Figure S2 use N-terminally His-tagged Nsp13. Because the N-terminal tag is known to have large effects on Nsp13 activity, this calls into question virtually all of the results in this manuscript.

We thank the reviewer for raising this important concern regarding the potential influence of the N-terminal His tag on nsp13 activity. We have carefully considered this issue and provide the following lines of evidence to address it.

(1) We have generated a tag-free nsp13 variant and our preliminary characterization (Author response image 1) shows that it retains all key activities: ATP hydrolysis (comparable to His-tagged nsp13), both ATP-independent (Mg²⁺-activated) and ATP-dependent unwinding, as well as chaperone activity to remodel stem-loops. These results demonstrate that while the His tag may modulate enzymatic efficiency, it does not create or abolish any specific biochemical function.

(2) We conducted a systematic survey of 27 published studies on SARS-CoV/SARS-CoV-2 nsp13 (Author response table 1). The results show that 17 out of 27 studies (63%) used affinity-tagged nsp13 without tag removal, including His, MBP, GST, and Strep tags.

(3) The only study that systematically compared different affinity tags (Adedeji et al., 2012) reported that GST-tagged nsp13 exhibited ~520-fold higher ATPase activity than His-tagged nsp13, demonstrating that the choice of affinity tag can affect enzymatic efficiency. However, both tagged versions retained all core enzymatic activities, including ATP hydrolysis and duplex unwinding. Importantly, no study has compared the full functional spectrum between His-tagged and tag-free nsp13. Our preliminary data suggest that the His tag may affect efficiency but does not alter the presence or absence of any specific activity.

Planned experiments:

We fully agree with the reviewer that a more systematic comparison would strengthen the conclusions. In the revision, we will include additional characterization of tag-free nsp13: (i) quantitative nucleic acid binding affinity, (ii) G4 unfolding efficiency, (iii) strand annealing activity. These experiments are currently underway.

In summary, while we acknowledge that the His tag may influence enzymatic efficiency, our key conclusions are supported by experiments with tag-free nsp13. We will add a discussion of these points and include additional tag-free nsp13 data in the revised manuscript.

(2) The ATP-independent, bidirectional duplex unwinding shown for short duplex substrates is reminiscent of the trapping of thermal fraying intermediates that have been reported for other helicases. Because they are only observed on short duplexes, do not require ATP, and are bidirectional, this does not suggest strand displacement as suggested in the manuscript. Instead, it suggests trapping of partially melted intermediates.

We thank the reviewer for this insightful perspective. While the passive trapping of thermal fraying intermediates is a well-established model for non-catalytic protein-nucleic acid interactions, several lines of evidence suggest that nsp13 employs a more active, allosteric mechanism for ATP-independent remodeling.

(1) If nsp13 were merely a passive trap, increasing duplex stability should decrease unwinding. However, as shown in Figure S3, raising Mg²⁺ from 0 to 5 mM increases the DNA duplex Tm by ~10°C, yet nsp13’s remodeling activity is markedly enhanced under the same conditions (Figure 2). This positive correlation between cation-induced substrate stabilization and protein activation supports an active, protein-centered mechanism that overcomes the increased energetic barrier.

(2) The observed bidirectionality in ATP-independent remodeling does not simply imply a lack of polarity; rather, it can reflect nsp13’s intrinsic chaperone function. In the absence of ATP, nsp13 binds the ss/ds junction (Figure 2F) and, in a Mg²⁺-dependent manner, may use its binding energy to actively intercalate into the duplex. This mechanism is inherently symmetric for 3′ and 5′ overhangs, explaining bidirectional remodeling, while the absence of activity on blunt-ended substrates confirms the requirement for a pre-existing junction.

(3) The lack of activity on 24-bp substrates does not negate this remodeling mode but defines its energetic boundary. The binding energy released upon nsp13-nucleic acid interaction is sufficient to overcome the lower unwinding barrier of 12-16 bp duplexes, but insufficient to counteract the high stability and rapid re-annealing of a 24-bp duplex without the continuous mechanical power of ATP hydrolysis.

Planned Revision:

We thank the reviewer for prompting us to refine our mechanistic model. In the revision, we will add a dedicated discussion explicitly comparing the model of allosterically activated, binding-driven strand intrusion with the passive trapping model, incorporating the Tm data to strengthen our conclusions.

(3) Results that may be artifacts of unusual in vitro conditions are interpreted as if similar results will occur in the cell, where ATP is likely always present. Along those same lines, SARS-CoV-2 replicates in compartments of the endoplasmic reticulum, which would limit the ability of Nsp13 to access DNA substrates.

We thank the reviewer for raising this important concern regarding the physiological relevance. We fully agree that in vitro conditions do not entirely recapitulate the complex intracellular environment, and we have been careful not to over-interpret our findings. Below we address the two specific issues raised:

(1) Regarding the ATP-independent activity, we acknowledge that ATP is abundant in healthy, actively replicating cells. However, during rapid viral replication, local ATP concentrations can fluctuate due to the high energy demand of the RTC as the template contains extensive secondary structures, which may lead to transient ATP depletion. Under such energy-limited conditions, Yu et al. (2025) demonstrated that ADP-bound nsp13 exhibits chaperone activity that destabilizes nucleic acid structures without ATP hydrolysis, and Dumm et al. (2025) reported that SARS-CoV-2 nsp13 resolves RNA stem-loops in an ATP-independent manner.

Even when ATP is abundant, the ATP-independent mode may enable rapid, local structural adjustments that bypass the kinetic delay of ATP binding and hydrolysis. As shown in Figure 1D, nsp13 exhibits high binding affinity for structured nucleic acids. In this scenario, nsp13 functions not as a processive motor but through a binding-driven mechanism, using the free energy of protein-nucleic acid interaction to transiently destabilize short duplexes or resolve local secondary structures such as G4s and stem-loops in an energy-efficient manner.

(2) Regarding DNA substrates, we fully agree that RNA is the physiological substrate for nsp13. However, DNA is a validated and widely accepted surrogate for mechanistic studies because DNA is more stable and easier to manipulate than RNA to yield the mechanistic insights. A systematic survey of 27 published nsp13 studies (Author response table 1) shows that 20 out of 27 (74%) used DNA substrates for at least some of their experiments. In our study, we used DNA primarily as a mechanistic probe and a stable control, and we validated all key conclusions on physiological RNA substrates, as shown in Figures 4, 5, 6, S7, S8, S10, S11 and S12.

Planned revisions: To address the reviewer’s concerns more directly, we will revise the manuscript to include a discussion paragraph explicitly stating that the ATP-independent activity was observed under optimized in vitro conditions and may represent a latent remodeling capability that could be relevant under energy-limited conditions such as local ATP depletion during rapid replication. We will also clarify that DNA substrates were used as mechanistic probes and controls, and that all key findings were validated on physiological RNA substrates. We thank the reviewer for prompting us to strengthen the discussion of these important points.

(4) There is no evidence to support the conclusion that "Duplex DNA supports bidirectional remodeling via both ATP-dependent and ATP-independent mechanisms." 3'-5' duplex melting is limited to short duplexes and is ATP-independent, suggesting it may be due to trapping of thermal fraying intermediates by the ssDNA binding Nsp13. The ATP-dependent and ATP-independent melting on the substrates with the 3'-overhang are the same, suggesting that ATP-dependent melting does not occur on this substrate, which would indicate that bidirectional ATP-dependent translocation does not occur.

We are grateful to the reviewer for this critical evaluation of our mechanistic claims. We agree that our initial statement regarding bidirectional ATP-dependent remodeling was imprecise and not fully supported by the data. As the reviewer correctly notes, the similar unwinding efficiency on 3′-overhang substrates regardless of ATP presence indicates that ATP hydrolysis does not drive 3′→5′ translocation, which is consistent with nsp13’s known 5′→3′ motor polarity. The observed 3′→5′ activity is therefore more accurately described as an ATP-independent remodeling event, not ATP-dependent unwinding.

We will revise the Discussion and relevant Results sections to clarify the nature of this bidirectional activity. Specifically, the sentence:

"Duplex DNA supports bidirectional remodeling via both ATP-dependent and ATP-independent mechanisms..."will be corrected to: "Duplex DNA supports bidirectional remodeling via ATP-independent mechanisms."

We will also explicitly state that while nsp13 requires ATP for long-range, processive 5'→3' helicase activity, its remodeling/chaperone function is inherently bidirectional and powered by the free energy of binding to the ss/ds junction, rather than by ATP-driven mechanical work.

(5)-The description of ATP-independent unwinding as having "limited processivity," is likely not accurate. These experiments were multiturnover reactions with very high Nsp13 concentrations and no protein trap to ensure single turnover conditions. Because the reactions were multi-turnover, no information about the processivity of Nsp13 can be obtained. On the contrary, it seems likely that the product formed over the 30-minute reaction with a vast excess of Nsp13 is due to binding and dissociation of multiple Nsp13 molecules instead of processive translocation by a single enzyme.

We thank the reviewer for this important correction. We fully agree that our use of the term "processivity" was technically imprecise. Processivity strictly defines the distance a single enzyme translocates during one binding event, which our multi-turnover assays (with high nsp13 concentrations and no protein trap) were not designed to measure. Our results specifically demonstrate that the ATP-independent remodeling mode is highly sensitive to duplex length, with efficiency declining sharply as the duplex lengthens. To reflect the experimental data more faithfully, we have replaced "processivity" with more accurate descriptors throughout the manuscript.

Planned revisions:

(1) Original: "The ATP-independent unwinding mode, however, has limited processivity." Revised: "The ATP-independent unwinding mode, however, exhibits a steep decline in efficiency as the duplex length increases."

(2) Original: "...an ATP-independent, cation-activated mode with limited processivity." Revised: "...an ATP-independent, cation-activated mode specialized for localized structural remodeling"

(3) Original: "...primes Nsp13 for basal strand remodeling but supports only limited processivity." Revised: "...primes Nsp13 for basal strand remodeling but is insufficient for the sustained unwinding of extended duplexes."

(4) Original: "...primes Nsp13 for low-processivity strand displacement." Revised: "...primes Nsp13 for short-range strand displacement rather than long-range processive unwinding."

We believe these changes clarify that the ATP-independent mode acts as a molecular chaperone for local obstacles (like G4 or short stems) rather than a motor for long-range translocation. We thank the reviewer for helping us improve the precision of our description.

(6) G4s are much more stable at cellular K+ concentrations than they are at 20 mM K+. As such, Nsp13's ability to unfold a G4 in the absence of ATP may be diminished or eliminated at a physiological K+ concentration.

We thank the reviewer for this critical point regarding physiological ion concentrations. We agree that K⁺ significantly stabilizes G4 structures, which may raise the energy barrier for ATP-independent remodeling.

Planned experiments:

To address this, we will perform salt titration assays (up to 150 mM KCl) to evaluate the robustness of nsp13’s G4 unfolding activity under more physiological ionic conditions. We will also measure the melting temperature of our G4 substrates across this K⁺ range to correlate structural stability with enzymatic efficiency.

Author response image 1.

Preliminary characterization of tag-free Nsp13 enzymatic activities. (A) Comparison of ATPase activity between His-tagged and tag-free Nsp13 in the presence of ssRNA or RNA G4. (B) Raw fluorescence data from stopped-flow FRET analysis of ATP-dependent unwinding (16-bp fork DNA, 2 mM Mg²⁺, 2 mM ATP). F/F₀ represents FAM fluorescence normalized to initial DNA intensity. (C) ATP-independent DNA duplex remodeling (data reproduced from Figure S2). (D) Chaperone activity of tag-free Nsp13 on DNA and RNA stem-loops.

Author response table 1.

Summary of affinity tags, monovalent salt concentrations, and substrate types used in 27 published SARS-CoV/SARS-CoV-2 nsp13 studies

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(10) Lu L, Peng Y, Yao H, Wang Y, Li J, Yang Y, Lin Z. Punicalagin as an allosteric NSP13 helicase inhibitor potently suppresses SARS-CoV-2 replication in vitro. Antiviral Res. 2022 Oct;206:105389.

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Author response:

eLife Assessment

This useful study presents an improved protocol for long-term in vitro culture of Schistosoma mansoni that enables progression toward sexually dimorphic stages, representing a meaningful advance for studying parasite development and reducing reliance on animal models. The findings show that host-specific culture conditions support essential developmental and metabolic functions required for parasite maturation, although development remains delayed compared to in vivo conditions. The evidence is solid overall, but limited pairing efficiency and the absence of egg production indicate that the system does not yet fully recapitulate complete reproductive development.

On behalf of the co-authors, we thank the three reviewers and the editors for their complimentary remarks as well as the major and minor comments/ concerns. Addressing these concerns have led to revisions that improved the manuscript. In particular, further analyses have generated an updated Figures 3 and 4, and Supplementary Tables S1, and S4-S6.

Public Reviews:

Reviewer #1 (Public review):

Pichon, Rémi et al. describe an in vitro method for transforming Schistosoma cercariae into mature adult worms. The authors show that human serum (HS) supports parasite growth and differentiation more effectively than fetal bovine serum (FBS). They also observed differences in parasite growth and activity, with worms cultured in HS efficiently digesting human red blood cells (hRBC). Cultured worms were able to pair with ex vivo adult worms and produce eggs, indicating functional maturation suitable for downstream applications such as drug screening. While the experimental approach is comprehensive and supports the advantage of HS culture conditions, the pairing efficiency was low (≈7%) and required long culture periods (70-80 days), highlighting limitations that may affect reproducibility.

We acknowledge the reviewer for the positive highlights. Regarding the low in vitro pairing efficiency, we have now edited the manuscript to clarify a misleading statement related to 7%. We decided to remove the value of 7% — which corresponds to the percentage of experiments in which couples were observed, as it does not accurately represent the actual number of observed worm pairs and it is probably misleading. We have updated the text as follows:

Results, lines 230 ff.:

“While the establishment of sexual dimorphism was robust and reproducible across more than 15 independent experiments, pairing between male and female parasites was rare. Pairing was observed only in experiments lasting more than 80 days in which we were only able to observe a few couples. In addition, these pairings were temporary (Figures 6A, B; Supplementary Video S4).”

We also agree with the reviewer that the extended culture periods required to obtain fully sexually dimorphic parasites remain a limitation. As elaborated in Discussion (see below), key factors, probably derived from the host, are missing in the in vitro system explaining both the slow in vitro development and low rate of spontaneous pairing between in vitro developed, sexually dimorphic male and female worms. This was discussed as follows (lines 340-343): “That said, while our system was highly efficient in producing sexually dimorphic worms, spontaneous pairing between male and female parasites was extremely rare, mainly in aged in vitro cultures (from 80 to 100 days in culture) indicating that other factors, e.g., cholesterol, may be missing[35].”

A major strength of the study, in particular, is that the authors clearly differentiate the effects of FBS versus HS on developmental progression. The conversion rate observed in HS cultures is significant and consistent with previously published data.

While the study has several strengths, some aspects of the work are not fully explored. In particular, the role of hRBC supplementation requires further clarification. Although HS-cultured worms were shown to digest hRBC more readily, the implications of this observation remain unclear. Specifically, it would be useful to understand whether hRBC supplementation influences (1) long-term culture stability, (2) molecular pathways associated with development and differentiation, or (3) the pairing capacity of the worms. While addressing these questions may not be the main objective of the study, further discussion of these points would strengthen the manuscript.

We agree that deciphering the role of the human Red Blood Cells (hRBCs) supplementation is critical. Regarding the influence of hRBCs on the long-term culture stability in parasite development it has been well established for more than four decades that schistosomes do need red blood cells to grow in culture [Basch, P. F. Cultivation of Schistosoma mansoni in vitro. II. production of infertile eggs by worm pairs cultured from cercariae. J Parasitol 67, 186-190 (1981); Basch, P. F. Cultivation of Schistosoma mansoni in vitro. I. Establishment of cultures from cercariae and development until pairing. J. Parasitol. 67, 179-185 (1981)]. The molecular pathways underlying development, sexual differentiation and pairing and modulated by hRBCs in culture is currently being investigated by our team. We decided not to include these data and analyses in the current manuscript, as they fall outside its scope.

The manuscript is clearly written and represents a valuable contribution to the field. Overall, the experimental approach is sound, and the results support a useful methodological framework for the in vitro culture of Schistosoma worms and the attainment of sexual maturity, particularly for adult male worms.

We thank the reviewer for highlighting the manuscript’s strengths.

Reviewer #2 (Public review):

Summary:

The authors perform confirmation studies of Paul Basch's seminal schistosome work from 1981, demonstrating the development of transformed schistosomules into sexually dimorphic adult parasites, albeit without successful egg production. In addition to the findings from Basch's earlier work, the authors add some new molecular data in the form of an analysis of proliferative cells in in-vitro-derived animals.

Strengths:

The authors successfully confirm experimental results from earlier schistosome researchers, providing a potential new tool for studying schistosome biology without the need for vertebrate hosts.

We thank the reviewer for highlighting the manuscript’s strengths.

Weaknesses:

The display of data from the authors is sometimes difficult to follow/understand where it comes from. For example:

(1) Line 136: The authors claim that parasites in HS and FBS conditions have substantially different mortality rates (11.3 +/- 2.7 vs 5 +/- 2.3) but a quite high p-value (0.8). Analyzing the raw data myself, I obtained a mean of 8.2 +/- 1.7% vs 4.8% +/- 4.3% with a p-value of 0.15. Either the data are not clearly presented, and I did not follow them, or the data presented in the text do not match the raw data in the supplemental files.

We thank the reviewer for pointing this out; we have now edited Supplementary Tables S1 and S6 by turning them into a long format for the sake of clarity. Accordingly, Results, Methods sections, and indicated supplementary tables were edited as follows:

Results, lines 142 ff.:

“No morphological differences were observed between parasites cultured either in FBS or HS within the first week in culture; in both conditions most parasites were classified as early schistosomula [category 1: 76% ± 30 (average ± SD) in FBS and 73% ± 29 (average ± SD) in HS] with few lung (category 2) and early liver schistosomula (category 3) (Figure 1B, week 1; Supplementary Figure S1). The mean mortality (category 0) at week 1 was slightly higher, but not statistically significant (P= 0.42), in worms cultured in HS [9.75% ± 2.76 (average ± SD)] compared to the mortality registered in FBS-cultured parasites [5.52% ± 5.18 (average ± SD), Supplementary Table S6], consistent with previous findings[39].”

Methods, lines 463-465:

“To evaluate differences in mortality between HS- and FBS-cultured parasites, data from 5 experiments were combined and analysed using a Shapiro-Wilk normality test to test normality of the data and a non-parametric Wilcoxon rank sum exact test (Supplementary Tables S1 and S6).”

Supplementary Tables:

Supplementary Table S1. “Raw counts of parasites within each developmental stage category. Each row corresponds to a picture of parasites in culture medium containing FBS or HS. Each column corresponds to the raw parasite counts at indicated stage development (categories 0 to 5), time in culture (Time in days - D), and experimental condition.”

Supplementary Table S6. “Summary of all statistical tests employed in this study. 1. Statistical tests of parasite mortality and the raw data table used for this test. 2. Statistical tests for worm size comparisons (correspond to Figure 2). 3. Statistical tests for worm black gut comparisons (correspond to Figure 3). BG: Black gut. 4. Statistical tests for EdU positive cells comparisons (correspond to Figure 4). Replicate code: E, M and L correspond to day 2, 8 and 15 respectively; R and W correspond to the presence (R) or absence (W) of RBCs added 13 days after transformation.”

For clarity, in Author response image 1 we provide the R script used to perform the statistical tests on the data shown in Supplementary Table S6 (column Raw count of parasite developmental category per image and experiment)

Author response image 1.

(2) Line 187/Figure 4: Though it is not clearly stated, it appears that the authors treat their EdU counts as an ordinal data set of 61 steps (from 0 to >60) rather than a continuous measure of EdU+ cells per animal. In this author's opinion, the graph strongly suggests a continuous data set, and the fact that this reviewer had to dig through poorly-labeled raw data to discover the nature of the data is problematic. The authors should either switch to a continuous data set or make it explicit that the data shown are ordinal. If counting EdU+ cells is too arduous, the authors could consider comparing the amount of EdU+ area to the amount of DAPI+ area in maximum intensity projections of their confocal images, as this would roughly approximate the amount of proliferative cells in the animals.

As the reviewer correctly pointed out, the data were treated as ordinal because counting worms with more than 60 Edu+ cells became extremely difficult and highly inaccurate. Therefore, we decided to group in a single category, “60 EdU+ cells”, all worms showing more than 60 EdU+ cells. We have now updated Figure 4 where medians are shown instead of media values, Supplementary Table S5 to provide more comprehensive access to the raw counts, and Supplementary Table S6 to indicate the data for EdU+ cells per worm were considered ordinal. Accordingly, we have revised the corresponding sections as follows:

Results, lines 211 ff.:

“HS-cultured schistosomula showed higher numbers of proliferating stem cells, with a median of >48 and >60 EdU+ cells per worm at days 8 and 15, respectively (Figure 4). On the other hand, most FBS-cultured parasites displayed no more than an average of 20 EdU+ cells per worm (Figure 4).”

Methods, lines 520 ff.:

“EdU+ cells per parasite were counted for an average of 100 parasites across three independent experiments (Supplementary Table S5). Worms were grouped based on the number of cells per individual, but all those showing ⪰ 60 EdU+ cells were counted in the same group named ‘60 EdU+ cells'. Therefore, the data were considered ordinal data. Statistical analysis was performed by Kruskal-Wallis test with Dunn multiple comparison post-hoc test, with P≤0.05 considered significant (Supplementary Table S6).”

Figure 4 legend, lines 830 ff.:

“A. Violin plots showing the number of Edu+ cells per worm at indicated time points (2, 8, and 15 days post cercarial transformation) in parasites cultured either in Foetal Bovine Serum (FBS, blue) or Human Serum (HS, light brown). Human Red Blood Cells (hRBCs) were added in the culture at day 13 post cercarial transformation. The small black dots indicate individual worms, and the big black point indicates the median of EdU+ cells per worm. All worms showing ⪰ 60 EdU+ cells were counted and clustered together in the group named ‘60 EdU+ cells’. Hence, the data were treated as ordinal and statistical analysis performed by Kruskal-Wallis test with Dunn multiple comparison post-hoc test, with P≤0.05 (*) considered significant (Supplementary Tables S5 and S6).”

We thank the reviewer for the very interesting suggestion to quantify cell proliferation by calculating the ratio between EdU+ area to DAPI+ area in maximum intensity projections images. Measuring the fluorescence area for each worm in maximum projection is an excellent idea; however, due to the number of EdU+ cells present in some samples, we think this technique would not provide additional information or produce more detailed data compared with our analysis when the number of Edu+ cells exceeds 60 per worm. We will certainly consider this approximation for future studies.

There are some minor issues as well:

(1) Line 122: It is perhaps incorrect to refer to humans as "the" definitive host of schistosomes, as S. japonicum is primarily considered a zoonotic infection with water buffalo/cows being the primary definitive host.

We thank the reviewer for pointing this out; we have now replaced “schistosomes” with “Schistosoma mansoni” (current line 131)

(2) Line 185/298: The authors refer to EdU pulse-chase experiments, but the experiments described here are EdU pulse experiments.

This is a very good point, we thank the reviewer for bringing this up and have accordingly edited by replacing “EdU pulse-chase” with “EdU pulse” experiments in lines 37, 204, and 321.

Reviewer #3 (Public review):

Summary:

This study is significant as it established a protocol for the long-term culture of Schistosoma mansoni newly transformed cercariae, which developed in vitro into sexually dimorphic forms. The impact of two different sera, Fetal Bovine Serum (FBS) and Human Serum (HS), added to the culture medium supplemented with human red blood cells was evaluated. The authors demonstrated that HS-cultured parasites were able to digest red blood cells, a critical step for long-term parasite development. Furthermore, while most FBS-cultured parasites did not progress beyond an early liver stage, sexual dimorphism was clearly evident in the HS-cultured worms, albeit delayed compared to in vivo development.

Strengths:

This study could contribute to further in vitro studies for a better understanding of the unique sexual biology of Schistosoma mansoni and for screening novel schistosomicidal compounds. By increasing parasite development in in vitro studies, this protocol could have a positive impact on the principles of the 3Rs (Replacement, Reduction and Refinement) for animal research.

We thank the reviewer for highlighting the manuscript’s strengths.

Weaknesses:

As the authors mentioned, "pairing between male and female parasites was rare. Pairing was observed in approximately ~7% of the experiments, usually after day ~ 80 in culture. Egg production was also not achieved with this protocol.

Following the reviewer’s point and to clarify a misleading point, we have now decided to remove the value of 7% — which corresponds to the percentage of experiments in which couples were observed. However, this value does not accurately reflect the actual number of observed worm pairs, and it is probably misleading. We have updated the text as follows:

Results, lines 230 ff.:

“While the establishment of sexual dimorphism was robust and reproducible across more than 15 independent experiments, pairing between male and female parasites was rare. Pairing was observed only in experiments lasting more than 80 days in which we were only able to observe a few couples. In addition, these pairings were temporary (Figures 6A, B; Supplementary Video S4).”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Lin et al. presents a timely, technically strong study that builds patient-specific midbrain-like organoids (MLOs) from hiPSCs carrying clinically relevant GBA1 mutations (L444P/P415R and L444P/RecNcil). The authors comprehensively characterize nGD phenotypes (GCase deficiency, GluCer/GluSph accumulation, altered transcriptome, impaired dopaminergic differentiation), perform CRISPR correction to produce an isogenic line, and test three therapeutic modalities (SapC-DOPS-fGCase nanoparticles, AAV9GBA1, and SRT with GZ452). The model and multi-arm therapeutic evaluation are important advances with clear translational value.

My overall recommendation is that the work undergo a major revision to address the experimental and interpretive gaps listed below.

Strengths:

(1) Human, patient-specific midbrain model: Use of clinically relevant compound heterozygous GBA1 alleles (L444P/P415R and L444P/RecNcil) makes the model highly relevant to human nGD and captures patient genetic context that mouse models often miss.

(2) Robust multi-level phenotyping: Biochemical (GCase activity), lipidomic (GluCer/GluSph by UHPLC-MS/MS), molecular (bulk RNA-seq), and histological (TH/FOXA2, LAMP1, LC3) characterization are thorough and complementary.

(3) Use of isogenic CRISPR correction: Generating an isogenic line (WT/P415R) and demonstrating partial rescue strengthens causal inference that the GBA1 mutation drives many observed phenotypes.

(4) Parallel therapeutic testing in the same human platform: Comparing enzyme delivery (SapC-DOPS-fGCase), gene therapy (AAV9-GBA1), and substrate reduction (GZ452) within the same MLO system is an elegant demonstration of the platform's utility for preclinical evaluation.

(5) Good methodological transparency: Detailed protocols for MLO generation, editing, lipidomics, and assays allow reproducibility

Weaknesses:

(1) Limited genetic and biological replication

(a) Single primary disease line for core mechanistic claims. Most mechanistic data derive from GD2-1260 (L444P/P415R); GD2-10-257 (L444P/RecNcil) appears mainly in therapeutic experiments. Relying primarily on one patient line risks conflating patient-specific variation with general nGD mechanisms.

We thank the reviewer for highlighting the importance of genetic and biological replication. An additional patient-derived iPSC line was included in the manuscript, therefore, our study includes two independent nGD patient-derived iPSC lines, GD2-1260 (GBA1^L444P/P415R) and GD2-10-257 (GBA1^{L444P/RecNcil}), both of which carry the severe mutations associated with nGD. These two lines represent distinct genetic backgrounds and were used to demonstrate the consistency of key disease phenotypes (reduced GCase activity, elevated substrate, impaired dopaminergic neuron differentiation etc.) across different patient’s MLOs. Major experiments (e.g., GCase activity assays, substrate, immunoblotting for DA marker TH, and therapeutic testing with SapC-DOPS-fGCase, AAV9-GBA1) were performed using both patient lines, with results showing consistent phenotypes and therapeutic responses (see Figs. 2-6, and Supplementary Figs. 4-5). To ensure clarity and transparency, a new Supplementary Table 2 summarizes the characterization of both, the GD2-1260 and GD2-10-257 lines.

(b) Unclear biological replicate strategy. It is not always explicit how many independent differentiations and organoid batches were used (biological replicates vs. technical fields of view).

Biological replication was ensured in our study by conducting experiments in at least 3 independent differentiations per line, and technical replicates (multiple organoids/fields per batch) were averaged accordingly. We have clarified biological replicates and differentiation in the figure legends.

(c) A significant disadvantage of employing brain organoids is the heterogeneity during induction and potential low reproducibility. In this study, it is unclear how many independent differentiation batches were evaluated and, for each test (for example, immunofluorescent stain and bulk RNA-seq), how many organoids from each group were used. Please add a statement accordingly and show replicates to verify consistency in the supplementary data.

In the revision, we have clarified biological replicates and differentiation in the figure legend in Fig.1E; Fig.2B,2G; Fig.3F, 3G; Fig.4B-C,E,H-J, M-N; Fig.6D; and Fig.7A-C, I.

(d) Isogenic correction is partial. The corrected line is WT/P415R (single-allele correction); residual P415R complicates the interpretation of "full" rescue and leaves open whether the remaining pathology is due to incomplete correction or clonal/epigenetic effects.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was not feasible because GBA1 overlaps with a highly homologous pseudogene (PGBA), which makes precise editing technically challenging. Consequently, only the L444P mutation was successfully corrected, and the resulting isogenic line retains the P415R mutation in a heterozygous state. Because Gaucher disease is an autosomal recessive disorder, individuals carrying a single GBA1 mutation (heterozygous carriers) do not develop clinical symptoms. Therefore, the partially corrected isogenic line, which retains only the P415R allele, represents a clinically relevant carrier model. Consistent with this, our results show that GCase activity was restored to approximately 50% of wild-type levels (Fig.4B-C), supporting the expected heterozygous state. These findings also make it unlikely that the remaining differences observed are due to clonal variation or epigenetic effects.

(e) The authors tested week 3, 4, 8, 15, and 28 old organoids in different settings. However, systematic markers of maturation should be analyzed, and different maturation stages should be compared, for example, comparing week 8 organoids to week 28 organoids, with immunofluorescent marker staining and bulk RNAseq.

We agree that a systematic analysis of maturation stages is essential for validating the MLO model. Our data integrated a longitudinal comparison across multiple developmental windows (Weeks 3 to 28) to characterize the transition from progenitors to mature/functional states for nGD phenotyping and evaluation of therapeutic modalities: 1) DA differentiation (Wks 3 and 8 in Fig. 3): qPCR analysis demonstrated the progression of DA-specific programs. We observed a steady increase in the mature DA neuron marker TH and ASCL1. This was accompanied by a gradual decrease in early floor plate/progenitor markers FOXA2 and PLZF, indicating a successful differentiation path from progenitors to differentiated/mature DA neurons. 2) Glycosphingolipid substrates accumulation (Wks 15 and 28 in Fig 2): To assess late-stage nGD phenotyping, we compared GluCer and GluSph at Week 15 and Week 28. This comparison highlights the progressive accumulation of substrates in nGD MLOs, reflecting the metabolic consequences of the disease at different mature stage. 3) Organoid growth dynamics (Wks 4, 8, and 15 in new Fig. 4): The new Fig. 4 tracks physical maturation through organoid size and growth rates across three key time points, providing a macro-scale verification of consistent development between WT and nGD groups. By comparing these early (Wk 3-8) and late (Wk 15-28) stages, we confirmed that our MLOs transition from a proliferative state to a post-mitotic, specialized neuronal state, satisfied the requirement for comparing distinct maturation stages.

(f) The manuscript frequently refers to Wnt signaling dysregulation as a major finding. However, experimental validation is limited to transcriptomic data. Functional tests, such as the use of Wnt agonist/inhibitor, are needed to support this claim (see below).

We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work.

(g) Suggested fixes / experiments

Add at least one more independent disease hiPSC line (or show expanded analysis from GD2-10-257) for key mechanistic endpoints (lipid accumulation, transcriptomics, DA markers).

Additional line iPSC GD2-10-257 derived MLO was included in the manuscript. This was addressed above [see response to Weaknesses (1)-a].

Generate and analyze a fully corrected isogenic WT/WT clone (or a P415R-only line) if feasible; at minimum, acknowledge this limitation more explicitly and soften claims.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was unsuccessful because the GBA1 gene overlaps with a pseudogene (PGBA) located16kd downstream of GBA1, which shares 9698% sequence similarity with GBA1) (Ref#1, #2), which complicates precise editing. GBA1 is shorter (~5.7 kb) than PGBA (~7.6 kb). The primary exonic difference between GBA1 and PGBA is a 55-bp deletion in exon 9 of the pseudogene. As a result, the isogenic line we obtained carries only the P415R mutation, and L444P was corrected to normal sequence. We have included this limitation in the Methods as “This gene editing strategy is expected to also target the GBA1 pseudogene due to the identical target sequence, which limits the gene correction on certain mutations (e.g., P415R)”.

References:

(1) Horowitz M., Wilder S., Horowitz Z., Reiner O., Gelbart T., Beutler E. The human glucocerebrosidase gene and pseudogene: structure and evolution. Genomics (1989). 4, 87–96. doi:10.1016/0888-7543(89)90319-4

(2) Woo EG, Tayebi N, Sidransky E. Next-Generation Sequencing Analysis of GBA1: The Challenge of Detecting Complex Recombinant Alleles. Front Genet. (2021). 12:684067. doi: 10.3389/fgene.2021.684067. PMCID: PMC8255797.

Report and increase independent differentiations (N = biological replicates) and present per-differentiation summary statistics.

This was addressed above [see response to Weaknesses (1)-b, (1)-c].

(2) Mechanistic validation is insufficient

(a) RNA-seq pathways (Wnt, mTOR, lysosome) are not functionally probed. The manuscript shows pathway enrichment and some protein markers (p-4E-BP1) but lacks perturbation/rescue experiments to link these pathways causally to the DA phenotype.

(b) Autophagy analysis lacks flux assays. LC3-II and LAMP1 are informative, but without flux assays (e.g., bafilomycin A1 or chloroquine), one cannot distinguish increased autophagosome formation from decreased clearance.

(c) Dopaminergic dysfunction is superficially assessed. Dopamine in the medium and TH protein are shown, but no neuronal electrophysiology, synaptic marker co-localization, or viability measures are provided to demonstrate functional recovery after therapy.

(d) Suggested fixes / experiments - Perform targeted functional assays:

(i) Wnt reporter assays (TOP/FOP flash) and/or treat organoids with Wnt agonists/antagonists to test whether Wnt modulation rescues DA differentiation.

(ii) Test mTOR pathway causality using mTOR inhibitors (e.g., rapamycin) or 4E-BP1 perturbation and assay effects on DA markers and autophagy.

Include autophagy flux assessment (LC3 turnover with bafilomycin), and measure cathepsin activity where relevant.

Add at least one functional neuronal readout: calcium imaging, MEA recordings, or synaptic marker quantification (e.g., SYN1, PSD95) together with TH colocalization.

We thank the reviewer for these valuable suggestions. We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work. Importantly, the primary conclusions of our manuscript, that GBA1 mutations in nGD MLOs resulted in nGD pathologies such as diminished enzymatic function, accumulation of lipid substrates, widespread transcriptomic changes, and impaired dopaminergic neuron differentiation, which can be corrected by several therapeutic strategies in this study, are supported by the evidence presented. The suggested experiments represent an important direction for future research using brain organoids.

(3) Therapeutic evaluation needs greater depth and standardization

(a) Short windows and limited durability data. SapC-DOPS and AAV9 experiments range from 48 hours to 3 weeks; longer follow-up is needed to assess durability and whether biochemical rescue translates into restored neuronal function.

We agree with the reviewer. Because this is a proof-of-principle study, the treatment was designed within a short time window. Long-term studies with more comprehensive outcome assessments will be conducted in future work.

(b) Dose-response and biodistribution are under-characterized. AAV injection sites/volumes are described, but transduction efficiency, vg copies per organoid, cell-type tropism quantification, and SapC-DOPS penetration/distribution are not rigorously quantified.

We appreciate the reviewer’s concerns. This study was intended to demonstrate the feasibility and initial response of MLOs to AAV therapy. A comprehensive evaluation of AAV biodistribution will be considered in future studies.

The penetration and distribution of SapC-DOPS have been extensively characterized in prior studies. In vivo biodistribution of SapC–DOPS coupled CellVue Maroon, a fluorescent cargo, was examined in mice bearing human tumor xenografts using real-time fluorescence imaging, where CellVue Maroon fluorescence in tumor remained for 48 hours (Ref. #3: Fig. 4B, mouse 1), 100 hours (Ref. #4: Fig. 5), up to 216 hours (Ref. #5: Fig. 3). Uptake kinetics were also demonstrated in cells, with flow cytometry quantification showing that fluorescent cargo coupled SapC-DOPS nanovesicles, were incorporated into human brain tumor cell membranes within minutes and remained stably incorporated into the cells for up to one hour (Ref. # 6: Fig. 1a and Fig. 1b). Building on these findings, the present study focuses on evaluating the restoration of GCase function rather than reexamining biodistribution and uptake kinetics.

References:

(3) X. Qi, Z. Chu, Y.Y. Mahller, K.F. Stringer, D.P. Witte, T.P. Cripe. Cancer-selective targeting and cytotoxicity by liposomal-coupled lysosomal saposin C protein. Clin. Cancer Res. (2009) 15, 5840-5851. PMID: 19737950.

(4) Z. Chu, S. Abu-Baker, M.B. Palascak, S.A. Ahmad, R.S. Franco, and X. Qi. Targeting and cytotoxicity of SapC-DOPS nanovesicles in pancreatic cancer. PLOS ONE (2013) 8, e75507. PMID: 24124494.

(5) Z. Chu, K. LaSance, V.M. Blanco, C-H. Kwon, B. Kaur, M. Frederick, S. Thornton, L. Lemen, and X. Qi. Multi-angle rotational optical imaging of brain tumors and arthritis using fluorescent SapC-DOPS nanovesicles. J. Vis. Exp. (2014) 87, e51187, 1-7. PMID: 24837630.

(6) J. Wojton, Z. Chu, C-H. Kwon, L.M.L. Chow, M. Palascak, R. Franco, T. Bourdeau, S. Thornton, B. Kaur, and X. Qi. Systemic delivery of SapC-DOPS has antiangiogenic and antitumor effects against glioblastoma. Mol. Ther. (2013) 21, 1517-1525. PMID: 23732993.

(c) Specificity controls are missing. For SapC-DOPS, inclusion of a non-functional enzyme control (or heat-inactivated fGCase) would rule out non-specific nanoparticle effects. For AAV, assessment of off-target expression and potential cytotoxicity is needed.

Including inactive fGCase would confound the assessment of fGCase in MLOs by immunoblot and immunofluorescence; therefore, saposin C–DOPS was used as the control instead.

We agree that assessment of off-target expression and potential cytotoxicity for AAV is important, this will be included in future studies.

(d) Comparative efficacy lacking. It remains unclear which modality is most effective in the long term and in which cellular compartments.

To address this comment, we have added a new table (Supplementary Table 2) comparing the four therapeutic modalities and summarizing their respective outcomes. While this study focused on short-term responses as a proof-of-principle, future work will explore long-term therapeutic effects.

(e) Suggested fixes/experiments

Extend follow-up (e.g., 6+ weeks) after AAV/SapC dosing and evaluate DA markers, electrophysiology, and lipid levels over time.

We appreciate the reviewer’s suggestions. The therapeutic testing in patient-derived MLOs was designed as a proof-of-principle study to demonstrate feasibility and the primary response (rescue of GCase function) to the treatment. A comprehensive, long-term therapeutic evaluation of AAV and SapC-DOPS-fGCase is indeed important for a complete assessment; however, this represents a separate therapeutic study and is beyond the scope of the current work.

Quantify AAV transduction by qPCR for vector genomes and by cell-type quantification of GFP+ cells (neurons vs astrocytes vs progenitors).

For the AAV-treated experiments, we agree that measuring AAV copy number and GFP expression would provide additional information. However, the primary goal of this study was to demonstrate the key therapeutic outcome, rescue of GCase function by AAV-delivered normal GCase, which is directly relevant to the treatment objective.

Include SapC-DOPS control nanoparticles loaded with an inert protein and/or fluorescent cargo quantitation to show distribution and uptake kinetics.

As noted above [see response to Weakness (3)-c], using inert GCase would confound the assessment of fGCase uptake in MLOs; therefore, it was not suitable for this study. See response above for the distribution and uptake kinetics of SapC-DOPS [see response to Weaknesses (3)-b].

Provide head-to-head comparative graphs (activity, lipid clearance, DA restoration, and durability) with statistical tests.

We have added a new table (Supplementary Table 2) providing a head-to-head comparison of the treatment effects.

(4) Model limitations not fully accounted for in interpretation

(a) Absence of microglia and vasculature limits recapitulation of neuroinflammatory responses and drug penetration, both of which are important in nGD. These absences could explain incomplete phenotypic rescues and must be emphasized when drawing conclusions about therapeutic translation.

We agree that the absence of microglia and vasculature in midbrain-like organoids represents a limitation, as we have discussed in the manuscript. In this revision, we highlighted this limitation in the Discussion section and clarified that it may contribute to incomplete phenotyping and phenotypic rescue observed in our therapeutic experiments. Additionally, we have outlined future directions to incorporate microglia and vascularization into the organoid system to better recapitulate the in vivo environment and improve translational relevance (see 7th paragraph in the Discussion).

(b) Developmental vs degenerative phenotype conflation. Many phenotypes appear during differentiation (patterning defects). The manuscript sometimes interprets these as degenerative mechanisms; the distinction must be clarified.

We appreciate the reviewer’s comments. In the revised manuscript, we have clarified that certain abnormalities, such as patterning defects observed during early differentiation, likely reflect developmental consequences of GBA1 mutations rather than degenerative processes. Conversely, phenotypes such as substrate accumulation, lysosomal dysfunction, and impaired dopaminergic maturation at later stages are interpreted as degenerative features. We have updated the Results and Discussion sections to avoid conflating developmental defects with neurodegenerative mechanisms.

(c) Suggested fixes

Tone down the language throughout (Abstract/Results/Discussion) to avoid overstatement that MLOs fully recapitulate nGD neuropathology.

The manuscript has been revised to avoid overstatements.

Add plans or pilot data (if available) for microglia incorporation or vascularization to indicate how future work will address these gaps.

The manuscript now includes further plans to address the incorporation of microglia and vascularization, described in the last two paragraphs in the Discussion. Pilot study of microglia incorporation will be reported when it is completed.

(5) Statistical and presentation issues

(a) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

We have clarified biological replicates and differentiation in the figure legend [see response to Weaknesses (1)-b, (1)-c].

(b) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated Statistical analysis in methods as described below:

For comparisons between two groups, data were analyzed using unpaired two-tailed Student’s t-tests when the sample size was ≥6 per group and normality was confirmed by the Shapiro-Wilk test. When the normality assumption was not met or when sample sizes were small (n < 6), the non-parametric Mann-Whitney U test was used instead. For comparisons involving three or more groups, one-way ANOVA followed by Tukey’s multiple comparison test was applied when data were normally distributed; otherwise, the nonparametric Dunn’s multiple comparison test was used. Exclusion of outliers was made based on cutoffs of the mean ±2 standard deviations. All statistical analyses were performed using GraphPad Prism 10 software. Exact p-values are reported throughout the manuscript and figures where feasible. A p-value < 0.05 was considered statistically significant.

(c) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

In this work, quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM. This multilevel averaging approach minimizes bias from regional heterogeneity within organoids and accounts for variability across differentiations. Representative confocal images shown in the figures were selected to accurately reflect the quantified data. We believe this standardized quantification strategy ensures robust and reproducible results while appropriately representing the 3D architecture of the organoids.

In the revision, we have clarified the method used for image analysis of sectioned MLOs as below:

Quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed using ImageJ (NIH) on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM.

(d) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

RNA-seq data are from same batch. The mapping rate is >90%. GEO accession will be active upon publication. These were included in the Methods.

(e) Suggested fixes

Add a table summarizing biological replicates, technical replicates, and statistical tests used for each figure panel.

We have revised the figure legends to include replicates for each figure and statistical tests [see response in weaknesses (1)-b, (1)-c].

Recompute statistics where appropriate (non-parametric if N is small) and report effect sizes and confidence intervals.

Statistical analysis method is provided in the revision [see response in Weaknesses (5)-b].

(6) Minor comments and clarifications

(a) The authors should validate midbrain identity further with additional regional markers (EN1, OTX2) and show absence/low expression of forebrain markers (FOXG1) across replicates.

We validated the MLO identity by 1) FOXG1 and 2) EN1. FOXG1 was barely detectable in Wk8 75.1_MLO but highly present in ‘age-matched’ cerebral organoid (CO), suggesting our culturing method is midbrain region-oriented. In nGD MLO, FOXG1 expression is significantly higher than 75.1_MLO, indicating that there was aberrant anterior-posterior brain specification, consistent with the transcriptomic dysregulation observed in our RNA-seq data.

To further confirm midbrain identity, we examined the expression of EN1, an established midbrain-specific marker. Quantitative RT-PCR analysis demonstrated that EN1 expression increased progressively during differentiation in both WT-75.1 and nGD2-1260 MLOs at weeks 3 and 8 (Author response image 1). EN1 reached 34-fold and 373-fold higher levels than in WT-75.1 iPSCs at weeks 3 and 8, respectively, in WT-75.1 MLOs. In nGD MLOs, although EN1 expression showed a modest reduction at week 8, the levels were not significantly different from those observed in age-matched WT-75.1 MLOs (p > 0.05, ns).

Author response image 1.

qRT-PCR quantification of midbrain progenitor marker EN1 expression in WT-75.1 and GD2-1260 MLOs at Wk3 and Wk8. Data was normalized to WT-75.1 hiPSC cells and presented as mean ± SEM (n = 3-4 MLOs per group). ns, not significant.

(b) Extracellular dopamine ELISA should be complemented with intracellular dopamine or TH+ neuron counts normalized per organoid or per total neurons.

We quantified TH expression at both the mRNA level (Fig. 3F) and the protein level (Fig. 3G/H) from whole-organoid lysates, which provides a more consistent and integrative measure across samples. These TH expression levels correlated well with the corresponding extracellular (medium) dopamine concentrations for each genotype. In contrast, TH⁺ neuron counts may not reliably reflect total cellular dopamine levels because the number of cells captured on each organoid section varies substantially, making normalization difficult. Measuring intracellular dopamine is an alternative approach that will be considered in future studies.

(c) For CRISPR editing: the authors should report off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus. (off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus).

The off-target effect was analyzed during gene editing and the chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis. The related method was also updated as stated below:

“The chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis (Hsu, P., Scott, D., Weinstein, J. et al. DNA targeting specificity of RNA-guided Cas9 nucleases. Nat Biotechnol 31, 827–832 (2013). https://doi.org/10.1038/nbt.2647).”

(d) It should be clarified as to whether lipidomics normalization is to total protein per organoid or per cell, and include representative LC-MS chromatograms or method QC.

The normalization was to the protein of organoid lysate. This was clarified in the Methods section in the revision as stated below:

“The GluCer and GluSph levels in MLO were normalized to total MLO protein (mg) that were used for glycosphingolipids analyses. Protein mass was determined by BCA assay and glycosphingolipid was expressed as pmol/mg protein. Additionally, GluSph levels in the culture medium were quantified and normalized to the medium volume (pmol/mL).”

Representative LC-MS chromatograms for both normal and GD MLOs have been included in a new figure, Supplementary Figure 2.

(e) Figure legends should be improved in order to state the number of organoids, the number of differentiations, and the exact statistical tests used (including multiplecomparison corrections).

This was addressed above [see response to Weaknesses (1)-b and (5)-b].

(f) In the title, the authors state "reveal disease mechanisms", but the studies mainly exhibit functional changes. They should consider toning down the statement.

The title was revised to: Patient-Specific Midbrain Organoids with CRISPR Correction Recapitulate Neuronopathic Gaucher Disease Phenotypes and Enable Evaluation of Novel Therapies

(7) Recommendations

This reviewer recommends a major revision. The manuscript presents substantial novelty and strong potential impact but requires additional experimental validation and clearer, more conservative interpretation. Key items to address are:

(a) Strengthening genetic and biological replication (additional lines or replicate differentiations).

This was addressed above [see response to Weaknesses (1)-a, (1)-b, (1)-c].

(b) Adding functional mechanistic validation for major pathways (Wnt/mTOR/autophagy) and providing autophagy flux data.

(c) Including at least one neuronal functional readout (calcium imaging/MEA/patch) to demonstrate functional rescue.

As addressed above [see response to Weaknesses (2)], the suggested experiments in b) and c) would provide additional insights into this study and we will consider them in future work.

(d) Deepening therapeutic characterization (dose, biodistribution, durability) and including specificity controls.

This was addressed above [see response to Weaknesses (3)-a to e].

(e) Improving statistical reporting and explicitly stating biological replicate structure.

This was addressed above [see response to Weaknesses (1)-b, (5)-b].

Reviewer #2 (Public review):

Sun et al. have developed a midbrain-like organoid (MLO) model for neuronopathic Gaucher disease (nGD). The MLOs recapitulate several features of nGD molecular pathology, including reduced GCase activity, sphingolipid accumulation, and impaired dopaminergic neuron development. They also characterize the transcriptome in the MLO nGD model. CRISPR correction of one of the GBA1 mutant alleles rescues most of the nGD molecular phenotypes. The MLO model was further deployed in proof-of-principle studies of investigational nGD therapies, including SapC-DOPS nanovesicles, AAV9-mediated GBA1 gene delivery, and substrate-reduction therapy (GZ452). This patient-specific 3D model provides a new platform for studying nGD mechanisms and accelerating therapy development. Overall, only modest weaknesses are noted.

We thank the reviewer for the supportive remarks.

Reviewer #3 (Public review):

Summary:

In this study, the authors describe modeling of neuronopathic Gaucher disease (nGD) using midbrain-like organoids (MLOs) derived from hiPSCs carrying GBA1 L444P/P415R or L444P/RecNciI variants. These MLOs recapitulate several disease features, including GCase deficiency, reduced enzymatic activity, lipid substrate accumulation, and impaired dopaminergic neuron differentiation. Correction of the GBA1 L444P variant restored GCase activity, normalized lipid metabolism, and rescued dopaminergic neuronal defects, confirming its pathogenic role in the MLO model. The authors further leveraged this system to evaluate therapeutic strategies, including: (i) SapC-DOPS nanovesicles for GCase delivery, (ii) AAV9-mediated GBA1 gene therapy, and (iii) GZ452, a glucosylceramide synthase inhibitor. These treatments reduced lipid accumulation and ameliorated autophagic, lysosomal, and neurodevelopmental abnormalities.

Strengths:

This manuscript demonstrates that nGD patient-derived MLOs can serve as an additional platform for investigating nGD mechanisms and advancing therapeutic development.

Comments:

(1) It is interesting that GBA1 L444P/P415R MLOs show defects in midbrain patterning and dopaminergic neuron differentiation (Figure 3). One might wonder whether these abnormalities are specific to the combination of L444P and P415R variants or represent a general consequence of GBA1 loss. Do GBA1 L444P/RecNciI (GD2-10-257) MLOs also exhibit similar defects?

We observed reduced dopaminergic neuron marker TH expression in GBA1 L444P/RecNciI (GD2-10-257) MLOs, suggesting that this line also exhibits defects in dopaminergic neuron differentiation. These data are provided in a new Supplementary Fig. 4E, and are summarized in new Supplementary Table 2 in the revision.

(2) In Supplementary Figure 3, the authors examined GCase localization in SapC-DOPSfGCase-treated nGD MLOs. These data indicate that GCase is delivered to TH⁺ neurons, GFAP⁺ glia, and various other unidentified cell types. In fruit flies, the GBA1 ortholog, Gba1b, is only expressed in glia (PMID: 35857503; 35961319). Neuronally produced GluCer is transferred to glia for GBA1-mediated degradation. These findings raise an important question: in wild-type MLOs, which cell type(s) normally express GBA1? Are they dopaminergic neurons, astrocytes, or other cell types?

All cell types in wild-type MLOs are expected to express GBA1, as it is a housekeeping gene broadly expressed across neurons, astrocytes, and other brain cell types. Its lysosomal function is essential for cellular homeostasis and is therefore not restricted to any specific lineage. (https://www.proteinatlas.org/ENSG00000177628GBA1/brain/midbrain).

(3) The authors may consider switching Figures 2 and 3 so that the differentiation defects observed in nGD MLOs (Figure 3) are presented before the analysis of other phenotypic abnormalities, including the various transcriptional changes (Figure 2).

We appreciate the reviewer’s suggestion; however, we respectfully prefer to retain the current order of Figures 2 and 3, as we believe this structure provides the clearest narrative flow. Figure 2 establishes the core biochemical hallmarks: reduced GCase activity, substrate accumulation, and global transcriptomic dysregulation (1,429 DEGs enriched in neural development, WNT signaling, and lysosomal pathways), which together provide essential molecular context for studying the specific cellular differentiation defects presented in Figure 3. Presenting the broader disease landscape first creates a coherent mechanistic link to the subsequent analyses of midbrain patterning and dopaminergic neuron impairment.

To enhance readability, we have added a brief transitional sentence at the start of the Figure 3 paragraph: “Building on the molecular and transcriptomic hallmarks of GCase deficiency observed in nGD MLOs (Figure 2), we next investigated the impact on midbrain patterning and dopaminergic neuron differentiation (Figure 3).”

Recommendations for the authors:

Reviewing Editor Comments:

Your paper has been reviewed by three expert reviewers in the GBA field. Although they appreciate the work and its novelty, they raise several concerns. We suggest that you to address these concerns in the next version.

Reviewer #1 (Recommendations for the authors):

Statistical and presentation issues

(1) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

This was addressed above [see response to Reviewer 1 Weaknesses (1)- b].

(2) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated methods to describe the Statistical analysis details [see response to Reviewer 1 Weaknesses (5)-b].

(3) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

This was addressed above [see response to Reviewer 1 Weaknesses (5)- c].

(4) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

Our RNA-seq data were generated from a single batch of MLOs, with mapping rates exceeding 90%. The GEO accession will be made publicly available upon publication.

Reviewer #2 (Recommendations for the authors):

Please consider the following suggestions for revisions:

(1) Line 86: A bit more explanation/justification for the focus on midbrain-like organoids would be helpful, including introducing the nature of the midbrain pathology to better put some of the MLO findings in context. Is the nGD pathology for the midbrain significantly different / out of proportion to other affected brain regions?

nGD Patients often display impaired vertical gaze and movement disorders. These symptoms correlate with midbrain involvement due to the sensitivity of this region to neuroinflammatory and degenerative processes (Ref #7, #8). Both human and mouse studies indicate that the midbrain exhibits prominent substrate accumulation compared to other brain regions, suggesting a predisposition for greater pathological involvement in GD midbrain (Ref #8, #9, #10, #11). This rationale was added to Line 86 in the revision.

References:

(7) Goker-Alpan O, Ivanova MM. Neuronopathic Gaucher disease: Rare in the West, common in the East. J Inherit Metab Dis.(2024) 47(5):917-934. PMID: 38768609.

(8) Burrow TA, Sun Y, Prada CE, Bailey L, Zhang W, Brewer A, Wu SW, Setchell KDR, Witte D, Cohen MB, Grabowski GA. CNS, lung, and lymph node involvement in Gaucher disease type 3 after 11 years of therapy: clinical, histopathologic, and biochemical findings. Mol Genet Metab. (2015) 114(2):233-241. PMID: 25219293.

(9) Tamar Farfel-Becker, Einat B. Vitner, Samuel L. Kelly, Jessica R. Bame, Jingjing Duan, Vera Shinder, Alfred H. Merrill, Kostantin Dobrenis, Anthony H. Futerman. Neuronal accumulation of glucosylceramide in a mouse model of neuronopathic Gaucher disease leads to neurodegeneration, Human Molecular Genetics, (2014). Volume 23, Issue 4, Pages 843–854.

(10) E. Ellen Jones, Wujuan Zhang, Xueheng Zhao, Cristine Quiason , Stephanie Dale, Sheerin Shahidi-Latham, Gregory A. Grabowski, Kenneth D. R. Setchell, Richard R. Drake, and Ying Sun. High-Resolution MALDI Imaging Mass Spectrometry. SLAS Discovery (2017). Vol. 22(10) 1218–1228

(11) Xu YH, Xu K, Sun Y, Liou B, Quinn B, Li RH, Xue L, Zhang W, Setchell KD, Witte D, Grabowski GA. Multiple pathogenic proteins implicated in neuronopathic Gaucher disease mice. Hum Mol Genet. (2014) 23(15):3943-57. PMID: 24599400.

(2) Lines 359-360: Please specify the carbon-chain length of the sphingoid base of the GluCer species analyzed. Also, is there a citation for the statement that 18:0 and 16:0 are "brain-enriched species"?

The carbon-chain length analyzed ranges from 14:0 to 24:0. The sphingoid base for all GluCer species analyzed is d18:1. For example, the species referred to as GluCer 18:0 corresponds to GluCer(d18:1/18:0). Although both, 16:0 and 18:0 are enriched in the brain, 18:0 is the most abundant species in the brain (Ref #12, #13). We revised "brain-enriched species” to “brain-predominant species (18:0)”.

References:

(12) Nilsson, O., and Svennerholm, L. Accumulation of Glucosylceramide and Glucosylsphingosine (Psychosine) in Cerebrum and Cerebellum in Infantile and Juvenile Gaucher Disease. Journal of Neurochemistry (1982) 39, 709–718.

(13) Sun, Y., Zhang, W., Xu, Y.H., Quinn, B., Dasgupta, N., Liou, B., Setchell, K.D., and Grabowski, G.A. Substrate compositional variation with tissue/region and Gba1 mutations in mouse models--implications for Gaucher disease. PLoS One (2013). 8, e57560.10.1371/journal.pone.0057560.

(3) Figure 2: It would be interesting to compare the MLO findings to prior gene expression data. Are there previously published transcriptome analyses from nGD brain tissue (or other tissues) that the transcriptome data obtained from MLOs may be compared with? What about transcriptome analyses of mouse GD models?

We thank the reviewer for this valuable suggestion. To strengthen the biological context of our transcriptomic findings, we have added a new comparative table (new Supplementary Table 3) in the revised manuscript that summarizes key dysregulated pathways in our human nGD MLOs alongside previously published data from nGD mouse midbrain (Ref#14). The table highlights substantial overlap, including axon guidance, neuron differentiation, dopaminergic/glutamatergic/GABAergic synaptic signaling, lipid metabolism, apoptosis/cell death, and nervous system development, emphasizing the translational relevance of our model. We also note that our dataset uniquely reveals pronounced dysregulation of WNT signaling and anterior-posterior patterning (Fig. 2L and 2M), potentially reflecting human-specific early midbrain defects.

We added the following sentence to Discussion: “Comparative analysis with prior transcriptomic data from nGD mouse midbrain showed consistent dysregulation in axon guidance, synaptic signaling, lipid metabolism, and nervous system development (new Supplementary Table 3), supporting the fidelity of our human MLO model.”

Reference:

(14) Dasgupta N, Xu YH, Li R, Peng Y, Pandey MK, Tinch SL, Liou B, Inskeep V, Zhang W, Setchell KD, Keddache M, Grabowski GA, Sun Y. Neuronopathic Gaucher disease: dysregulated mRNAs and miRNAs in brain pathogenesis and effects of pharmacologic chaperone treatment in a mouse model. Hum Mol Genet. (2015) 24(24):7031-48. PMID: 26420838.

(4) Lines 402-405 & Figure 3D: Is it possible to include a merged image to better visualize the TH and FOXA2 co-staining / potential colocalization?

The merged images of TH (red) and FOXA2 (green) are shown in Fig. 3E. Yellow arrows indicate TH and FOXA2 co-stained cells, which appear yellow in the merged images. The results demonstrate that the number of co-stained cells is reduced in GD2-1260 MLOs compared with WT-75.1 MLOs at both, week 6 and week 8.

(5) Lines 447-448 & Figure 4F, G, J: It would be helpful to provide a direct analysis/visualization of MLO size between the WT-75.1, GD2-1260, and iso-GD2-1260 genotypes (allowing direct comparison of WT and iso). Similarly, the same 3-way analysis would be valuable for assessing dopamine levels.

We have included WT-75.1 in Fig. 4 F/G/J in the revision. All three genotypes, WT-75.1, GD2-1260, and iso-GD2-1260, are presented for analysis compared to WT-75.1. In new Figure 4F, MLO growth is presented by representative MLO images taken under wide field microscopy at day 2, Wk4 and Wk8 of differentiation. In new Fig. 4G, MLOs size was analyzed by NIS elements and presented as the area (µm²) of MLO in image (mean ± SEM). N≥10 MLOs were analyzed for each genotype. In new Fig. 4J. Dopamine levels in MLO culture medium from WT-75.1, GD2-1260 and iso- GD2-1260 MLOs at Wk12 cultured in 3 mL BGM medium for 72 hours were analyzed. Data are presented as mean ± SEM (n = 5 per group). Statistical analysis applied was described in the legend.

(6) Figure 4: What is the explanation/interpretation of the residual autophagy pathway dysfunction in CRISPR-corrected MLOs? nGD requires near-complete loss of GCase activity, so it is a bit curious that autophagic dysfunction would be observed with only ~50% GCase reduction? There is some discussion, but it doesn't fully capture the unexpected nature and implications of this result.

This phenomenon may be explained by a threshold effect in lysosomal function. Gaucher disease is an autosomal recessive disorder. The carriers with heterozygous GBA1 mutation, who retain approximately 50% of normal GCase activity, do not develop disease. This suggests that even partial restoration of GCase activity can reduce glucosylceramide accumulation below a pathological threshold, thereby restoring lysosomal integrity and autophagic flux. In addition, improved GCase activity may help normalize the lipid composition of lysosomal membranes, facilitating the fusion events required for effective autophagy.

(7) Lines 512-516 & Figure 5J: The data shown are inconclusive. Can these Western blot data be quantified, noting the number of replicates for each measurement? Without quantification and statistics, it is difficult to assess the claim that levels of LAMP1, LC3-I, LC3-II, 4E-BP1, and p-4E-BP1 in GD2-1260 treated with SapC-DOPS-fGCase are more similar to GD2-1260 treated following SapC-DOPS than to WT-75.1.

We performed quantitative analysis by comparing WT-75.1 and included the data in new Fig. 5J. The result was revised as:

Analysis of protein levels showed that decreased LAMP1 expression in GD2 1260 MLOs was not altered following SapC DOPS fGCase treatment (Figure 5J). The elevated LC3-II levels, an indicator of impaired autophagic flux, were reduced upon treatment, suggesting enhanced autophagic activity (Figure 5J). Moreover, phosphorylated 4E-BP1 (Thr37/46), but not total 4E-BP1, was improved in SapC-DOPS-fGCase–treated MLOs, reflecting a decrease in mTOR hyperactivation (Figure 5J). We anticipate that a longer duration of SapC-DOPS-fGCase exposure in nGD MLOs may produce a more robust therapeutic effect in rescuing nGD-associated phenotypes, which will be evaluated in future studies.

(8) Lines 518-520: The presented data support "effective restoration of GCase activity," but clarification is needed regarding "correction of GD-related disease phenotypes." Perhaps "selected molecular and biochemical phenotypes" would be more accurate. Data are not shown for several other phenotypes, including TH, FOXA2, and dopamine levels.

This was revised to “selected molecular and biochemical phenotypes “.

(9) Figure 5D-J: Please clarify whether all experiments were conducted 48 hours after treatment, as indicated for Figure 5C. If so, does this suggest that SapC-DOPS treatment exhibits only short-term effects? Were any data collected to evaluate the persistence of the treatment effect?

The treatment duration is specified in the Fig. 5 legend. Fig. 5D–J represent experiments conducted after two weeks of treatment, whereas Fig. 5C reflects a 48-hour treatment. In both Gaucher disease lines, two-week treatment restored GCase activity to wild-type levels and reduced GluSph substrate accumulation. These findings were intended as proof-of-principle to demonstrate therapeutic feasibility; evaluation of treatment persistence beyond two weeks was beyond the scope of this study.

Minor suggestions

(1) Line 80: "A brain organoid derived from hiPSCs of a healthy individual with GBA1 knockout and α-synuclein overexpression exhibited some PD features23." I would suggest enumerating what "PD features" are to distinguish from "clinical features", which I don't think is the intended meaning.

This was revised as “exhibited characteristic PD markers”.

(2) Figure 2I: The reported number of downregulated DEGs is incorrect. It should be 765, not 1429.

This was corrected in Figure 2I.

(3) Line 359: change "enrich" to "enriched".

This word was corrected.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This foundational study builds on prior work from this group to reveal the complexities underlying ligand-dependent RXRγ-Nur77 heterodimer formation, offering a compelling re-evaluation of their earlier conclusions. The authors examine how a library of RXR ligands influences the biophysical, structural, and functional properties of Nur77. They find that although the Nur77-RXRγ heterodimer shares notable functional similarities with the Nurr1-RXRα complex, it also exhibits unique features, notably, both dimer dissociation and classical agonist-driven activities. This work advances our understanding of the nuanced behaviors of nuclear receptor heterodimers, which have important implications for health and disease.

Strengths:

(1) Builds on previous work by providing a comprehensive analysis that examines whether Nur77-RXRγ heterodimer formation parallels that of the Nurr1-RXRα complex.

(2) Systematic evaluation of a library of RXR ligands provides a broad survey of functional outputs.

(3) Careful reanalysis of previous work sheds new light on how NR4A heterodimers function.

We thank the reviewer for recognizing our work as foundational. In the nuclear receptor field, current understanding of ligand-regulated nuclear receptor activity is based largely on ligand-dependent coregulator recruitment preferences; for example, agonists enhance coactivator recruitment to activate transcription. Building on our recent study of Nurr1-RXRα, the present work suggests that activation of the evolutionarily related NR4A-RXR heterodimer Nur77-RXRγ by RXR ligands is also consistent with a non-classical activation mechanism involving heterodimer dissociation.

Weaknesses:

(1) Some conclusions appear overstated or are not well substantiated by the work presented. It's unclear how the data support a non-classical mode of agonism, for example, based on the data shown.

We thank the reviewer for this important point. We did not intend to claim that Nur77-RXRγ activation is explained exclusively by a non-classical mode of agonism. Rather, our interpretation was that the data are consistent with two possible, non-mutually exclusive mechanisms: (1) a classical pharmacological mechanism involving ligand-dependent coregulator recruitment; and (2) a non-classical mechanism involving ligand-binding domain (LBD) heterodimer dissociation, as we previously described for Nurr1-RXRα. This differs from our prior eLife study of Nurr1-RXRα, in which the data supported the LBD heterodimer dissociation model but not the classical pharmacological model.

In our revised manuscript, we clarify two points that are important for interpreting the Nur77-RXRγ data. First, several experimental limitations of the Nur77-RXRγ studies reduced the extent to which the mechanism could be resolved as rigorously as in our earlier Nurr1-RXRα study. Second, and more importantly, the currently available ligand set lacks Nur77-RXRγ-selective agonists. This limits our ability to determine whether LBD heterodimer dissociation is the sole or principal mechanism of activation, or instead one of several contributing mechanisms.

Taken together, these results support LBD heterodimer dissociation as a plausible and experimentally observable component of Nur77-RXRγ activation and, therefore, as a candidate shared activation mechanism for NR4A-RXR heterodimers. At the same time, because the quantitative evidence is less definitive than in the Nurr1-RXRα system, we agree that conclusions regarding Nur77-RXRγ should be stated more cautiously. This caution is reflected in both the title of our manuscript (“Towards a unified mechanism…”) and the language used throughout the text.

(2) Some assays have relatively few replicates, with only two in some cases.

We thank the reviewer for their attention to experimental rigor. For some assays, the findings were reproduced in two independent experiments, which we considered sufficient to confirm the presence and reproducibility of the effects observed in those particular assay formats. In the original manuscript, we used a general statement in the figure legends (“representative of two or more independent experiments”) across all assay data. In the revised manuscript, we now specify the number of independent experimental replicates for each assay in the corresponding figure legends to improve transparency.

Reviewer #2 (Public review):

Summary:

This study explores the mechanisms by which binding of the nuclear receptor RXRg regulates its heterodimeric partner Nur77. Previously, this group made the interesting discovery that ligand-dependent activation of RXRg bound to a related partner, Nurr1, does not occur through a classical pharmacological mechanism but through agonist-dependent dissociation of the complex through disruption of their ligand binding domain (LBD) interactions. Here, they revisit this paradigm with Nur77. In contrast to Nurr1, the authors do not have the reagents to clearly support a role for LBD dissociation. Following the model of partial ligand-dependent dissociation of the LBD heterodimer, the experimental data (NMR, ITC, SEC) are interesting and quite complex.

Strengths:

The authors do a rigorous job of describing the data and providing possible interpretations and caveats. Revisiting the analysis of Nurr1, they identify the crucial role that selective Nurr1-RXRg agonists played in supporting the LBD dissociation model; without analogous compounds for the Nur77-RXRg complex, it is difficult to invoke this mechanism. Interestingly, treatment with the Nurr1-RXRg selective agonist HX600 suggests it can induce some LBD dissociation. Therefore, there may be some similarities between the regulation of Nurr1 and Nur77 by RXRg.

We thank the reviewer for this thoughtful and balanced summary of our work. We appreciate the reviewer’s recognition of both our prior findings in the Nurr1-RXRα system and the interesting, but more complex, experimental behavior observed here for Nur77-RXRγ. We agree that the absence of Nur77-RXRγ-selective agonists currently limits how definitively the contribution of LBD dissociation can be resolved, and we have revised the manuscript to make this point more explicit and to further temper our conclusions accordingly.

Weaknesses:

Despite evidence supporting a partial role for RXRg LBD dissociation as a mechanism to activate Nur77, other data demonstrate that a fundamentally different regulatory mechanism likely exists in the Nur77-RXRg complex that involves the RXRg disordered NTD. The decision to describe further study of this as outside the scope of this work is unfortunate, as it closed off an avenue that could have provided fruitful data informing the apparently distinct regulatory mechanisms of the Nur77-RXRg complex. Given the uncertainty in the importance of the partial roles of the pharmacological mechanism, LBD dissociation, and the RXRg NTD, this study may have limited impact on the field.

We thank the reviewer for this thoughtful point. We agree that the RXRγ NTD likely contributes to regulation of Nur77-RXRγ transcription, and that our truncation data suggest that regions outside the LBD can influence transcriptional output. At present, however, the effect of RXRγ NTD truncation is not sufficiently mechanistically resolved to distinguish among several plausible explanations.

For example, the RXRγ NTD has been implicated in phase separation and biomolecular condensate formation in cells (PubMed ID 40392852, 40420113, 33971237, 31881311), and perturbing these properties (via RXRγ NTD truncation) could indirectly affect Nur77-RXRγ transcriptional activity. In addition, NTDs of nuclear receptors can participate in coactivator or corepressor interactions (PubMed ID 24284822), raising the possibility that removal of the RXRγ NTD alters transcription by changing recruitment of regulatory factors rather than by directly informing the LBD-centered mechanism examined here. We will clarify in the revised manuscript that these possibilities remain unresolved and represent important directions for future study.

We also agree that defining how multiple RXRγ domains contribute to Nur77-RXRγ regulation would be valuable for the field. However, the focus of the present study is narrower: to test whether, as in our previous eLife study of Nurr1-RXRα, RXR ligands can influence heterodimer function through effects on LBD-LBD interactions. Because the available data do not yet allow a mechanistic dissection of the RXRγ NTD contribution, we believe that a definitive analysis of this question would require a separate set of experiments beyond the scope of the present work. We have revised the manuscript to better acknowledge this limitation and to frame the conclusions accordingly.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Overall, this is a compelling body of work. Additional summary statements and clearer transitions would be helpful throughout.

Here are some points that should be addressed or at least discussed by the authors:

(1) It is unclear in the luciferase assays whether the truncated proteins are functional or not. Were there Western blots or other assays run to confirm protein concentrations?

We thank the reviewer for this point. We did not perform Western blotting or other assays to confirm equivalent expression levels of the truncated RXRγ constructs, and we agree that this is a limitation of the luciferase assay data. As a result, the transcriptional effects observed with the truncation constructs should be interpreted cautiously.

With that said, the increased transcriptional activity observed upon deletion of the RXRγ NTD/AF-1 region suggests that this region may exert a repressive effect on Nur77-RXRγ transcription. This effect could reflect multiple, non-mutually exclusive mechanisms, including altered phase separation or condensate-related properties of RXRγ, or altered recruitment of transcriptional coregulators through the NTD. Because our truncation strategy does not distinguish among these possibilities, we do not believe these data allow a definitive mechanistic interpretation of the NTD contribution.

We have revised the manuscript to clarify this limitation. We also note that the primary focus of the present study is the role of ligands in modulating Nur77-RXRγ function through LBD-mediated interactions, in direct comparison with our previous Nurr1-RXRα study. A more complete mechanistic dissection of how RXRγ domain architecture influences Nur77-RXRγ transcription will require future work.

(2) Why does the Nur77 construct lacking the NTD show increased luciferase activity?

Please see our response above to Reviewer 2’s Public Review, which also addresses this point.

(3) A case is made for the Nur77 LBD driving the activity, but it also could be inferred that the DBD is driving based on the data shown in Figure 1.

We thank the reviewer for this point. We agree that the Nur77 DBD is required for binding to NBRE response elements, and we did not intend to suggest otherwise. The experimental approach in Figure 1 was not designed to dissect the relative contributions of Nur77 domains, since Nur77 was tested only in its full-length form. Instead, the purpose of this experiment was to examine how truncation of RXRγ domains affects Nur77-RXRγ transcriptional activity, in direct comparison with our prior eLife study of Nurr1-RXRα, where RXRα domain truncations helped define the importance of RXR-LBD-mediated regulation. We will revise the text to clarify that Figure 1 does not distinguish whether Nur77 DBD-dependent DNA binding is necessary, but instead addresses whether the pattern of RXRγ domain dependence is consistent with an LBD-centered mechanism of ligand-regulated heterodimer function.

(4) It is stated that the HX600 coactivator recruitment requires further study. Why wasn't it studied here?

We thank the reviewer for this point. The primary focus of this study was to determine how RXR ligands influence Nur77-RXRγ heterodimer activity, particularly in relation to ligand-dependent effects on heterodimer function. A more detailed analysis of HX600-dependent coactivator recruitment would require a broader mechanistic investigation of RXRα and RXRγ homodimer pharmacology and RXR-specific coregulator interactions, which extends beyond the central scope of the present manuscript. We agree that this is an important question and view it as a valuable direction for future work.

(5) Figure 3B, the shifts in monomer populations, error bars aren't shown, the biggest shift is from 0.2 to 0.6, is that statistically meaningful?

We thank the reviewer for this point. The reviewer is correct that error bars were not shown for Figure 3B. These NMR measurements were performed once (n=1), and therefore the shifts in monomer populations shown in Figure 3B cannot be assessed statistically. Because these studies required substantial NMR instrument time and isotopically labeled protein at high concentration, we were not able to perform experimental replicates for this dataset. We have revised the figure legend to explicitly state that these data were collected from a single experiment and have tempered the corresponding language in the manuscript accordingly.

(6) Some ligands are shown in the figures but don't appear to be discussed in the text (at least that I can find), such as SR11237.

We thank the reviewer for pointing this out. We used a panel of 14 commercially available RXR ligands with different pharmacological properties to probe Nur77-RXRγ function, as in our previous Nurr1-RXRα study. In the text, we emphasized ligands that were most informative for the mechanistic conclusions, rather than discussing every compound individually. SR11237, for example, behaved similarly to the broader group of RXR agonists and was therefore shown as part of the full ligand panel but not specifically highlighted in the text. We will clarify this in the revised manuscript.

(7) There is a sentence in the discussion that says "these observations implicate that although RXRg LBD provides the protein-protein interaction interface to bind Nur77...." the authors did not show enough data to support this claim. It should be bolstered.

We thank the reviewer for this point. We agree that this statement was stronger than was warranted by the data presented. Our intent was not to claim that the present study definitively establishes the RXRγ LBD as the sole or fully defined protein-protein interaction interface for Nur77 binding. Rather, based on the domain truncation data together with our prior Nurr1-RXRα study, we intended this statement as a working interpretation consistent with an LBD-centered mechanism. In our revised manuscript, we have softened this language to avoid overstating the conclusion and clarified that the current data support, but do not definitively prove, a role for the RXRγ LBD in mediating functionally relevant interaction with Nur77.

Reviewer #2 (Recommendations for the authors):

Even though this study is not able to make definitive claims about the mechanism(s) of activation of Nur77 in the Nur77-RXRg complex, the work presented here is rigorous and solidly interpreted. Identifying differences between Nurr1 and Nur77 regulation is important, and the work here shows that selective agonists are essential for supporting the non-canonical mechanism they identified before. Although they address potential implications of NTD regulation in the discussion, it feels like a lot of insight into Nur77 regulation is being missed. However, it is clear that addressing this experimentally would require substantially more work. I don't have any specific recommendations. Given current limitations on funding, I think it's fine to focus on the work completed with the acceptance that it likely limits the impact of the work on the field.

We thank the reviewer for this thoughtful and balanced assessment of our work. The goal of this manuscript was to test whether the LBD heterodimer dissociation mechanism that we previously reported for Nurr1-RXRα may represent a conserved feature of NR4A-RXR heterodimers by extending these studies to Nur77-RXRγ. We agree that understanding the role of the RXRγ NTD in Nur77-RXRγ regulation is important and potentially highly informative. At the same time, resolving that question experimentally would require a distinct and more extensive set of studies beyond the scope of the present work. We have therefore chosen to focus this manuscript on the completed LBD-centered studies, while acknowledging that this narrower scope may limit the broader impact of the work.

Minor points:

(1) Without page and line numbers, it is not easy to point out specific text. On the bottom of page 6 of the document, there are two references to Figure 3a, and the arrows that help illustrate RXRg LBD-dependent CSPs; the second figure callout should describe the blue arrow, I believe.

Thank you, we made this change.

(2) Bottom of page 8, "...revealed two compounds [that] standout..."

Thank you, we made this change.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

We truly appreciate all the effort that the reviewer put into reading and understanding our work. With a total of 37 excellent questions, this is one of the most thorough reviews that we have received in a long time.

R1.0: Summary:

In this study, the authors propose a "unifying method to evaluate inter-areal interactions in different types of neuronal recordings, timescales, and species". The method consists of computing the variance explained by a linear decoder that attempts to predict individual neural responses (firing rates) in one area based on neural responses in another area.

The authors apply the method to previously published calcium imaging data from layer 4 and layers 2/3 of 4 mice over 7 days, and simultaneously recorded Utah array spiking data from areas V1 and V4 of 1 monkey over 5 days of recording. They report distributions over "variance explained" numbers for several combinations: from mouse V1 L4 to mouse V1 L2/3, from L2/3 to L4, from monkey V1 to monkey V4, and from V4 to V1. For their monkey data, they also report the corresponding results for different temporal shifts. Overall, they find the expected results: responses in each of the two neural populations are predictive of responses in the other, more so when the stimulus is not controlled than when it is, and with sometimes different results for different stimulus classes (e.g., gratings vs. natural images).

Strengths:

(1) Use of existing data.

(2) Addresses an interesting question.

R1.1: Unfortunately, the method falls short of the state of the art: both generalized linear models (GLMs), which have been used in similar contexts for at least 20 years (see the many papers, both theoretical and applied to neural population data, by e.g. Simoncelli, Paninsky, Pillow, Schwartz, and many colleagues dating back to 2004), and the extension of Granger causality to point processes (e.g. Kim et al. PLoS CB 2011). Both approaches are substantially superior to what is proposed in the manuscript, since they enforce non-negativity for spike rates (the importance of which can be seen in Figure 2AB), and do not require unnecessary coarse-graining of the data by binning spikes (the 200 ms time bins are very long compared to the time scale on which communication between closely connected neuronal populations within an area, or between related areas, takes place).

First, a few points of clarification.

(i) We worked with two-photon calcium imaging data (mice), and with the envelope of multi-unit activity (monkeys). While both of these types of signals are strongly correlated with spikes, neither of them can be truly considered to be a point process.

(ii)The reviewer points to Figure 2AB. The signals that we worked with can be negative. The black traces are the actual signals and show clear negative bouts, especially noticeable in the middle panel in Figure 2B. Of course, this does not mean that there are negative spike rates. This has to do with the way the data are normalized and not with the specific prediction method. However, the reviewer is correct in stating that the method that we used could also yield negative values even for non-negative spike rates.

(iii) We did not bin the macaque data into 200-ms time bins, but rather 25-ms time bins (line 548, Figure 1B legend). Additionally, we have now performed additional analyses with different window sizes, showing that the conclusions still hold (see Supplemental Figure 4 and lines 139-143).

To further address the reviewer’s question, we implemented a Poisson GLM enforcing non-negativity on macaque MUAe data (without spontaneous activity subtraction, ensuring strictly positive values; lines 135-139, Supplemental Figure 1M). The model did not improve predictions over ridge regression, confirming our methodological choice. This method is not directly applicable to mouse calcium data, since the activity after baseline subtraction can be negative.

We did not use Granger or any other causality methods. The question of causality is certainly important, and there are multiple methods developed to assess causality in neural signals. We do not make any claims about causality in our study. A rigorous evaluation of causality is an interesting line of research for future work.

R1.2: In terms of analysis results, the work in the manuscript presents some expected and some less expected results. However, because the monkey data are based on only one monkey (misleadingly, the manuscript consistently uses the plural ‘monkeys’), none of the results specific to that monkey, nor the comparison of that one monkey to mice, are supported by robust data.

We have now added data from 2 additional monkeys, including:

(i) A second monkey (monkey “A”) from the same dataset (Chen et al., 2020), which includes all activity types except the lights off condition (lines 90-96, 120-132, 159, 161, 171, 183-185, 188-194, 200-203, 228-237, 254-258, 292-296, 334-342, 351-353, 358-364, 374-378, 387-393, 400-408, 414, 417-421, 539-540, 544-545, 680-681, 696-698; Supplemental figures 1-6, 8, 11, 12, and 13; Table 2).

(i) We collected new neural activity from one additional monkey (monkey “D”) in collaboration with the Ponce lab (lines 90-96, 120-130, 132-134, 163-164, 228-235, 237-243, 292-296, 351-353, 374-378, 387-389, 539-540, 553-560, 696-698; Supplemental figures 1-2, 4, 6, 9, 11, and 12; Table 2). The new data include responses to the same checkerboard and gray screen images as the original dataset, along with responses during lights-off conditions.

R1.3: One of the main results for mice (bimodality of explained variance values, mentioned in the abstract) does not appear to be quantified or supported by a statistical test.

We have now formally quantified the bimodality of the relationship between one-vs-rest correlation and inter-laminar explained variance (EV) in mice using Hartigan’s dip test, applied to neurons with EV>0.4. The test confirmed significant bimodality in two of the three mice (MP031 and MP032: p<0.001; MP033: p=0.687). These results are now included in the Results section (lines 307-311) and shown in Supplemental Figure 7A,D. In datasets that did not show bimodality by visual inspection (macaque recordings), the same test yielded non-significant results (e.g., p=0.994), confirming that the statistical analysis distinguishes between bimodal and unimodal cases.

R1.4: Moreover, the two data sets differ in too many aspects to allow for any conclusions about whether the comparisons reflect differences in species (mouse vs. monkey), anatomy (L2/3-L4 vs. V1-V4), or recording technique (calcium imaging vs. extracellular spiking).

We also agree with this comment. Our goal is not to provide any direct quantitative comparison between the two species. We emphasize (lines 494-497) that the experiments in the two species differ along multiple dimensions, including: (i) differences in recording modalities (calcium vs. electrophysiology), (ii) associated differences in temporal resolution, neuronal types, and SNR, (iii) cortical targets (layers vs. areas), (iii) sample size, (iv) stimuli, (v) task conditions. In the revised manuscript, we also emphasized that the aim of this work is to investigate inter-areal interactions within each species rather than to draw quantitative comparisons between species (lines 497-499).

Reviewer #1 (Recommendations for the authors):

R1.5 In the analysis of directionality, you stated that subsampling was done randomly. Presumably, there could be multiple subsamples that fulfill the control of split-trial r. Are you only showing results from one subsample or multiple subsamples?

We show the median from 10 subsample permutations. This is now clarified in line 621.

R1.6 About the measurement 1-vs-rest r2. Understanding the definition is important for interpreting the results, but the definition was not clearly written. In lines 195-196, could you be more clear about whether the correlation is between the predicted neuron and other neurons in the predicted population or between the predicted neuron and the mean activity of the predictor population? Also, in line 212, why do you call this self-consistency? Isn't this a correlation between a neuron and the others?

The 1-vs-rest r² value, or self-consistency, is the correlation calculated for each neuron i and does not involve other neurons. Let indicate the response 𝑟 of neuron i during trial t (t=1,..., T where T is the total number of trials). For a given trial t, we compute the average activity of the neuron excluding this trial:

Throughout, the superscript (rest)means “all repetitions excluding repeat 𝑡”. The one-vs-rest correlation for the held-out repetition 𝑡 is:

We then average these correlations across all held-out repetitions:

We now clarify this in the text (lines 304-306 and lines 642-647).

R1.7 In Figure 6 G and I. The "all" condition contains more neurons than either of the other two. In this case, is this comparison fair or meaningful?

The reviewer is also correct here. The comparisons between the <10% and >80% groups contain the same number of predictor neurons, and those are fair comparisons. The “all” condition contains more predictor neurons, and, therefore, those comparisons are not fair. We clarified this point in lines 360-364.

We included the “all” condition here because we think that it is an instructive sanity check in terms of reporting how EV changes with more neurons, and also in terms of understanding why the EV values in the other two conditions are lower. Expanding on this point with a little bit of philosophy, ultimately, when considering a neuron in area B (e.g., V4) and the contributions from neurons in another area A (e.g., V1), one would like to have access to all the inputs (e.g., all the neurons in V1 that are monosynaptically connected to the target neuron in area V4). We do not have access to this type of information, and we do not make any claims about monosynaptic connectivity, let alone exhaustive sampling of inputs to a given neuron. The “all” condition merely provides a quantitative illustration of the fact that EV increases with the number of predictor neurons. This observation may be considered to be somewhat trivial, but it should be pointed out that the conclusion relies on the input neurons sharing information with the target neurons (e.g., perhaps one may not be able to predict V4 activity very well from the responses of millions of neurons in the cerebellum).

R1.8 I believe the results section can be improved by adding some interpretation after each finding.

We thank the reviewer for the suggestion. We generally like to separate results from interpretation. However, to honor the suggestion, we added brief interpretations throughout the results section (lines 142-143, 171-173, 272-273, 279-281, 331-333, and 361-364) and expanded on the interpretations in the Discussion section.

R1.9 Line 52 - 74: It would be better to be more specific about what kind of neuronal interactions, e.g., noise correlation, synchrony, etc.

We added a clarification on the types of interactions we study in lines 68-73.

R1.10 Line 81. Something seems to be missing after "5500". 5500 trials? Neurons?

We thank the reviewer for pointing this out. The number refers to neurons (fixed in line 87).

R1.11 Line 94. The readers would appreciate more explanation of the method.

We have expanded on the explanation, as suggested (lines 106-107).

R1.12 Line 104. The fraction of visually responsive neurons seems to be small. Is this typically for mouse V1? Would this fraction be higher if you also used the peak, as you did for macaque data in your SNR calculation (line 412)? And what is this number for the recorded L4?

The reviewer correctly points out the small number of visually responsive neurons.

We note that we now refer to the subset of neurons used for prediction analyses as visually reliable (VR) neurons (lines 115-116, 125-126, 178-179, 183-184, 211-212, 214-216, 217-226, 283-286), defined conservatively as neurons with SNR > 2 computed from the mean across all stimuli (not the peak to any one stimulus) and split-half reliability >0.8 (Methods, lines 569–590). This choice emphasizes neurons that are consistently informative over the full stimulus set.

Regarding the question of how typical the number of responsive neurons in mice is, the fraction of “responsive” neurons in mouse V1 varies widely depending on the definition and stimulus set but the fractions are substantially lower than those reported in monkeys (with different methods). For those of us more used to the macaque neurophysiology literature, this has been one of the biggest surprises coming from work in rodents. Many studies report a sizable group of non-responsive neurons in mouse V1 (e.g., as little as 37% percent of V1 neurons being responsive in at least 25% of the trials according to de Vries et al., Nat Neur, 2020). Our fraction of visually responsive neurons is small because it couples a conservative SNR metric with a high trial-reliability threshold.

As the reviewer notes, a peak-based metric based on any stimulus would be a less conservative criterion that would increase the fraction of neurons labeled responsive.

R1.13 Line 113. Why not also give an exact percentage number?

We have given the exact percentage number (lines 125-126).

R1.14 Line 128. Is this just because L2/3 has more neurons? If so, then isn't this trivial?

Our intention was to illustrate the best prediction performance we could get in either direction, which means including all L2/3 neurons. We have reworded our text to clarify (lines 149-151).

R1.15 Line 134. Isn't this expected? Since V1 have more units than V4?

The reviewer is correct. As discussed in R1.7 in mice, we sought to report the best prediction performances in either direction. We have edited our text for clarity (lines 149-151).

R1.16 Line 165-168. What's the logical connection between these two sentences? If the former is true, we should expect to see differences. Also, why the same population? Shouldn't you include non-visual neurons?

The two sentences in question are: “The difference in predictability in the absence of a stimulus could in principle change according to the directionality in inter-laminar interactions.” and, “There was no statistically significant difference in the EV fraction between laminar directions (L4→L2/3 vs. L2/3→L4) using the same control population as in Figure 3B (Figure 5A-C and Figure Supplement 2H).”. The key point here was to control for similar reliability values in order to make fair comparisons. We have added an additional comparison between directionalities focusing on nonvisual neurons (SNR<2 & r<0.8), and have also found no statistically significant difference between direction of predictability (Supplemental Figure 3A, right, lines 221-224).

R1.17 Table 2. The information of which session corresponds to which experiment can be put in the table, which would be easier to read.

We have added which sessions correspond to which experiments in Table 2.

R1.18 Figure 1, Captions for panel c and d. I don't see any colored arrows in the figure.

We removed the color descriptions (Figure 1C-D).

R1.19 Figures 3, 4, and others. The annotations of "n.s." are very hard to see.

We changed the color so that it is easier to see now (Figures 3, 4, 6, and Supplementary Figures 1-4, 6, and 8-10).

R1.20 Figure 5, panel A. The legend is too small.

We increased the legend size (Figure 5A).

R1.21 Figure S5, panel D. Why are some of the data points connected?

The paired connections are illustrated specifically in the highly predictable neurons to highlight the two separate distributions of neurons. One group, the highly predictable and highly reliable group, maintains its inter-laminar predictability after projecting out the “non-visual” activity (lines 327-330), whereas the highly predictable yet unreliable group shows a sharp decrease in inter-areal predictability, which corroborates the idea of non-visual components influencing neurons in mouse V1, as shown by Stringer et al. 2019b and consistent with our results.

R1.22 l.91 "Ope" -> open?

We fixed the typo (line 100).

R1.23 Fig. 3C+D: Why is only one session used for this?

One session was used to illustrate the distribution of split-half reliability values per area. Figure 3D contains information about all 5 stimulus sessions (see legend to Figure 3D).

R1.24 "Even without controlling for the number of predictors or their respective split-half correlation values (627-688 sites in V1, 86-115 sites in V4), we found better predictability in the V1 to V4 direction than the reverse ( 𝑝 < 0.001, Figure Supplement 2I)." -> What does "even" mean here? Isn't this simply the null result if there is no true difference and the real reason the authors controlled for size?

The reviewer’s understanding is correct. We have edited our text for clarity (lines 157-160)

R1.25 "We could predict V1 and V4 activity across all stimulus types ( 𝑝 < 0.001, paired permutation test of prediction vs. shuffled frames prediction)." -> better than chance? For all neurons on average? What does this mean? Isn't it trivial and 100% expected that neural activity in the visual cortex is above chance related to the visual input?

We stated that sites in V1 and V4 could predict each other across all stimulus types before describing the differences between them. We agree that this observation is to be expected and indicated so now in the text (lines 185-186).

R1.26 "The predictability was the highest in both directions for neuronal activity in response to a full field checkerboard images (Figure 4D). In the V1 → V4 direction, the EV fraction was higher when predicting a slow-moving small thin bar compared to a fast-moving large thick bar (Figure 4D, left), whereas the opposite was true for the V4 → V1 direction (Figure 4D, right)." -> What does this mean? Is this expected or not? Under what theories of cortical processing?

The differences between EV prediction directions (V1→V4: slow thin bars > fast thick bars; V4→V1: fast thick bars > slow thin bars) could be because V4 responses are more reliable for the slow thin bars whereas V1 responses are more reliable for the fast thick bars (Supplemental Figure 5H–I). To account for this possibility, we controlled for differences in target-related properties by regressing out covariates like SNR, split-half correlation, and variance. In monkey L, regressing out reliability/drive within direction using these covariates, the V4→V1 bar difference between slow thin bars and fast thick bars was not significant and the difference in the V1→V4 difference direction was reduced (Supplemental Figure 5K, lines 198-203). This suggests that the asymmetry primarily reflects stimulus‑dependent reliability of the target population rather than a strong directional selectivity.

To the best of our knowledge, there are no clear predictions that match these observations from existing theories of visual cortical processing, especially given the paucity of computational models that include stimulus velocity when describing the responses in area V4. There has been extensive work on theories of surround suppression, but it seems unlikely that the thick bars would elicit surround suppression given the size of the V4 receptive fields. Many current computational models that aim to fit the responses of neurons in the visual cortex use neural networks that take an image as visual input and yield activations. Most of these models do not incorporate stimulus movement, and even those that do incorporate stimulus dynamics, only indirectly map onto interlaminar stimulus transformations or even between-area stimulus transformations. We hope that the results in this manuscript will help inspire and constrain better models of visual cortical processing.

R1.27 Shouldn't all the predictability analysis be done conditioned on the stimulus in order to tell us more than the trivial "both V1 and V3, or L2/3 and L4, are driven by visual inputs"? (The spontaneous activity analyses are essentially that, for a small subset of the stimuli.)

The key goal of this study is to quantify inter-areal interactions both under visual input and without visual input. This type of analysis is important because inter-areal interactions may depend both on visual inputs but also on neuronal inputs that are not triggered by visual signals. For example, extensive work in mice has now shown that neuronal responses in V1 depend on an animal’s running speed, independently of any visual input. Even within the visual input conditions, we present analyses where we shuffle trial order (e.g., Figure 7, Supplementary Figure 11) to estimate the contribution of trial-by-trial variations that are independent of visual inputs and other analyses where we project out non-visual activity (e.g., Supplementary Figure 7).

R1.28 "In visually responsive neurons, there was a significant reduction in EV during gray screen compared to visual stimulus presentation" -> perfectly expected. But the report-worthy result here is how much is left, not whether EV is decreased!

We have changed the wording on the results to highlight the sustained predictability (lines 211-212). It is important to note that, although the reduction in EV during gray screen may be expected, this observation does not hold for all neurons. In fact, there are some neurons for which the EV during visual presentation is comparable to that during gray screen (Figure 5B,C,E: neurons that lie on the diagonal line).

R1.29 "Similar to the conclusions drawn from the mouse data, the predictability of neuronal activity was higher in response to stimulus presentation than to gray screen presentations" -> Really? Conditioned on stimulus, or explainable by the well-known fact that both V1 and V4 are visually driven?

As discussed in R1.28, in mice, there are many neurons where the EV during gray screen is comparable to that during stimulus presentation. In monkeys, most sites were visually driven. As the reviewer points out, we expected that EV during stimulus presentation would be higher than during gray screen; this observation is a reasonable sanity check. The difference between unshuffled trials and shuffled trials (Figure 7, Supplementary Figure 11) provides an estimate of the interactions that are not purely explained by visual inputs alone in monkeys.

R1.30 "Unlike the mouse, macaque correlation of visual predictability between stimulus presentation and spontaneous activity was high across all types of spontaneous conditions" -> Why? Is this simply explainable by a lower mean response in the spontaneous condition in the mouse? Are these mouse and monkey experiments truly comparable? Isn't it surprising that spontaneous activity in the monkey visual cortex compared to evoked activity is higher than in the mouse?

With respect to the question of whether spontaneous activity (or stimulus-evoked activity) in monkeys is higher than in the mouse, it is difficult to make these comparisons. We emphasize in the text the multiple differences between the experiments in both species. Our goal is not to perform any quantitative comparison across species (see R1.4). We changed the wording to remove any inference of comparison between species (lines 248-250).

R1.31 Occasionally imprecise presentation. Ex "To further examine the non-stimulus driven component, we reasoned that if the shared information between areas were strictly driven by the visual stimulus, then using the activity of a stimulus presentation repeat to one specific image could be used to predict the responses to any other stimulus repeat of the same image. On the other hand, if the shared activity does not have any stimulus-response information, then the prediction model would not work when considering responses across repeated presentations of identical stimuli in different trials. To test these two opposing ideas, we compared the inter-areal prediction EV fractions using unshuffled versus shuffled trials." -> Sets up two extreme strawmen (100% driven by stimulus vs 0% driven by stimulus). What does "model would not work" mean? EV=0? Hypotheses not ideas.

Our intent was to set up two extreme hypotheses, not to claim that neurons must fall exclusively into one or the other. The two extremes help better interpret the results.

The reviewer indicates that these are straw-man hypotheses. This may well be the case. But note the responses to R1.12, R1.27, R1.28, and R1.29. The reviewer seems to assume that all or most neurons in the visual cortex should be mostly or exclusively driven by visual stimuli.

We also replaced “ideas” with “hypotheses”, as suggested. We have expanded the discussion of these points in the manuscript (lines 480-493). Many neurons occupy intermediate positions between these two extreme hypotheses. We clarified that “model would not work” refers to prediction accuracy approaching chance (EV ≈ 0).

R1.32 "In both species and in both directions, inter-areal prediction EV fraction persisted (𝑝 < 0.001," Doesn't persist mean EV is unchanged? But the test is EV>0 or not in both cases.

We meant that EV values remained significantly above chance, not that they were unchanged. The statistical test was indeed whether EV > 0 as the reviewer indicated. We have revised the text accordingly (lines 375-380).

R1.33 "In mice, neurons showed a bimodal distribution in terms of their response predictability in shuffled and unshuffled trials" -> I don't see any bimodality in the figure, nor is there a statistical test provided for bimodality.

In Figure 7C, a group of neurons lay essentially along the horizontal axis, whereas the other group is dispersed closer to the diagonal line. Specifically, the neurons that lay on the horizontal axis are also the ones whose responses are best predicted during gray screen activity. We have changed the text to clarify this point (lines 380-382).

R1.34 "In the macaque V4 → V1 direction, there was a large proportion of neurons with peak EV when considering 25 ms to 50 ms offsets in the positive direction (i.e., V4 after V1, Figure 7I, right)." -> So what does this mean? Is this compatible with anything we know? This is the anti-causal direction so some kind of explanation would be warranted.

In the V4→V1 panel, a positive offset means we use V4 at t+Δt to predict V1 at t (and conversely in the V1→V4 panel). Therefore, the fact that the peak EV occurs at +10–20 ms indicates that V1 leads V4 by ~10–20 ms: in other words, V1’s earlier response best predicts V4’s slightly later response. This observation is not anti-causal, but rather it is consistent with the canonical largely feed-forward V1→V4 latency (e.g., Schmolesky et al., 1998 among many others). We clarified this in text (lines 400-404).

R1.35 L. 307: "In monkeys," plural!?

While this was not correct in the original version, we have now added data from two more monkeys.

R1.36 L. 313: "we observed an approximately bimodal distribution of neuronal responses, with a large subset of neurons that do not show reliable responses to visual stimuli both in L4 and L2/3" -> where?

The bimodal distribution can be appreciated in Figure 6B (1-vs-rest r2, third panel, note neurons along the y-axis, see also R1.33) and Supplementary Figure 7B (lines 307-312). Additionally, as stated in R1.3, we have now formally quantified the bimodality of the relationship between one-vs-rest correlation and inter-laminar explained variance (EV) in mice using Hartigan’s dip test (lines 310-313); see also Supplementary Figure 7A,D. In datasets that did not show bimodality by visual inspection (macaque recordings) the same test yielded non-significant results, confirming that the statistical analysis distinguishes between bimodal and unimodal cases.

R1.37 Random subsampling to control for population size done with how many subsamples? How are they combined? Variability across subsamples interpreted how?

We performed 10 permutations and used the median distributions across permutations (line 621).

Reviewer #2 (Public Review):

R2.0: “Summary:

In this work, the authors investigated the extent of shared variability in cortical population activity in the visual cortex in mice and macaques under conditions of spontaneous activity and visual stimulation. They argue that by studying the average response to repeated presentations of sensory stimuli, investigators are discounting the contribution of variable population responses that can have a significant impact at the single trial level. They hypothesized that, because these fluctuations are to some degree shared across cortical populations depending on the sources of these fluctuations and the relative connectivity between cortical populations within a network, one should be able to predict the response in one cortical population given the response of another cortical population on a single trial, and the degree of predictability should vary with factors such as retinotopic overlap, visual stimulation, and the directionality of canonical cortical circuits.”

R2.1: To test this, the authors analyzed previously collected and publicly available datasets. These include calcium imaging of the primary visual cortex in mice and electrophysiology recordings in V1 and V4 of macaques under different conditions of visual stimulation. The strength of this data is that it includes simultaneous recordings of hundreds of neurons across cortical layers or areas. However, the weaknesses of calcium dynamics (which has lower temporal resolution and misses some non-linear dynamics in cortical activity) and multi-unit envelope activity (which reflects fluctuations in population activity rather than the variance in individual unit spike trains), underestimate the variability of individual neurons. The authors deploy a regression model that is appropriate for addressing their hypothesis, and their analytic approach appears rigorous and well-controlled.

We agree with these points, and we discuss these specific limitations in capturing the variability of individual neurons in the Discussion section (lines 500-504). We have now also added analyses based on local field potentials (LFP). LFPs do not directly reflect the activity of individual neurons either.

R2.2: From their analysis, they found that there was significant predictability of activity between layer II/III and layer IV responses in mice and V1 and V4 activity in macaques, although the specific degree of predictability varied somewhat with the condition of the comparison with some minor differences between the datasets. The authors deployed a variety of analytic controls and explored a variety of comparisons that are both appropriate and convincing that there is a significant degree of predictability in population responses at the single trial level consistent with their hypothesis. This demonstrates that a significant fraction of cortical responses to stimuli is not due solely to the feedforward response to sensory input, and if we are to understand the computations that take place in the cortex, we must also understand how sensory responses interact with other sources of activity in cortical networks. However, the source of these predictive signals and their impact on function is only explored in a limited fashion, largely due to limitations in the datasets. Overall, this work highlights that, beyond the traditionally studied average evoked responses considered in systems neuroscience, there is a significant contribution of shared variability in cortical populations that may contextualize sensory representations depending on a host of factors that may be independent of the sensory signals being studied.

We agree that these datasets do not lend themselves well to directly separating and quantifying all the different sources of the predictive signals. We expand on this point in the Discussion section (lines 509-511).

R2.3: The different recording modalities and comparisons (within vs. across cortical areas) limit the interpretability of the inter-species comparisons.

We also agree with this comment. We emphasize that our goal is not to attempt a direct quantitative comparison across species (lines 497-499).

R2.4: Strengths:

This work considers a variety of conditions that may influence the relative predictability between cortical populations, including receptive field overlap, latency that may reflect feed-forward or feedback delays, and stimulus type and sensory condition. Their analytic approach is well-designed and statistically rigorous. They acknowledge the limitations of the data and do not over-interpret their findings.

Weaknesses:

The different recording modalities and comparisons (within vs. across cortical areas) limit the interpretability of the inter-species comparisons.The mechanistic contribution of known sources or correlates of shared variability (eye movements, pupil fluctuations, locomotion, whisking behaviors) were not considered, and these could be driving or a reflection of much of the predictability observed and explain differences in spontaneous and visual activity predictions.

We have expanded on the Discussion section to explicitly state the points raised by the reviewer (lines 494-509).

In mice, we have now also analyzed a separate dataset in which behavioral measurements were available, including running speed and facial motion (FaceMap SVDs). We used these to build behavioral-only and combined models to predict neural activity. We found that behavioral variables explained a modest but consistent portion of the variance across both spontaneous and stimulus conditions (Supplementary Figure 10A,C, lines 268-273).

For the macaque data, we analyzed pupil size as the only available behavioral measure in the macaque dataset. We focused specifically on the “resting state, eyes open” condition, where both neural activity and pupil measurements were available. Using ridge regression, we assessed the extent to which pupil size predicted neural activity in V1 and V4. Pupil size alone explained only a small fraction of the variance (Supplementary Figure 10E, lines 274-276).

R2.5: Previous work has explored correlations in activity between areas on various timescales, but this work only considered a narrow scope of timescales.

Without going into specifics about the numbers, it is hard to fully address this question. As the reviewer noted in R2.1, the mouse data analyzed here do not lend themselves to evaluating predictability on scales of tens of milliseconds. In the macaque data, we have now conducted additional analyses where we binned the activity across a range of bin sizes (10 ms to 200 ms). The new analyses are shown in Supplementary Figure 4, and described in lines 140-143, 160-163.

R2.6: The observation that there is some degree of predictability is not surprising, and it is unclear whether changes in observed predictability with analysis conditions are informative of a particular mechanism or just due to differences in the variance of activity under those conditions. Some of these issues could be addressed with further analysis, but some may be due to limitations in the experimental scope of the datasets and would require new experiments to resolve.

First, we note that several of the analyses and comparisons are within conditions and not across conditions, where by “condition” we mean the presence or absence of a stimulus or different stimuli (e.g., Figures 3, 5, 6, 7, Supplementary Figures 3-4, 7–13).

Second, we note that our mouse preprocessing standardized responses by spontaneous mean and SD per neuron, controlling baseline scale across conditions (lines 535-538). Because of this standardization, spontaneous traces have unit scale (mean = 0, SD = 1).

To test whether differences in variance underlie our findings, we calculated the variance for both species. For mice, we computed variance across repeats (visual) and across timepoints (lines 286-291). For the macaque moving-bar sessions, we computed variance across the concatenated held-out samples pooling timepoints, repeats, and bar identities (lines 291-292).

The V4 population showed a higher overall variance distribution compared to the V1 population (Supplementary Figure 2I-J), and L2/3 variance was also overall higher than L4 (Supplementary Figure 2D-E). We also see a modest monotonic relationship between EV fraction and this variance (mouse visual: Spearman ρ = 0.43–0.52, p < 0.001; macaque stimulus responses: ρ = 0.50–0.56, p < 0.001; macaque gray-screen responses: ρ = 0.38, p < 0.001, Figure 6A,D), indicating variance contributes to (but is not the primary driver of) EV prediction fraction. We then adjusted for variance by fitting, within each stimulus condition, a linear regression of EV on variance (excluding shuffled-control rows) and conducted all comparisons on the resulting residual EV values, thereby isolating effects not attributable to variance (see Supplementary Figure 3E-G, lines 165-171).

Reviewer #2 (Recommendations for the authors):

R2.7 Overall I found this manuscript to be very clearly written and the results compelling, although I found myself wanting a little more. I believe these datasets also include information about eye movements, pupil diameter, and maybe locomotion and whisking in the rodent work. I think it could be informative to ask the degree to which the predictability, particularly during the spontaneous activity, is attributable to these other known sources of variance in trial-by-trial measures. My concern is that during visual stimulation, the space of cortical responses is limited to a very narrow scope (observing a visual stimulus during fixation) whereas spontaneous activity includes a broader range of possibilities (different states of arousal, eye movement).

We analyzed the role of behavioral variables that could explain the neural activity in mouse V1 (including the variables suggested by the reviewer, running speed, facemap SVDs). The open dataset authors warned not to use pupil size since in the dark, the measurements were not accurate. In terms of the contribution to the predictability of mouse V1 activity, these behavioral variables showed a weak yet significant contribution (Supplementary Figure 10A,C, lines 260-270).

R2.8 By controlling for eye movements or pupil diameter during spontaneous measurements, would you improve your measure of predictability?

When predicting neural activity in the lights-off eyes open condition, combining neural data of the predictor population with information of pupil size did not result in a statistically significant increase in EV fraction when predicting the target population (Supplementary Figure 10E, lines 276-278).

R2.9 Also, there is work that shows feed-forward correlations between V1 and higher visual areas are observed in higher frequency activity, whereas feedback is associated with lower frequency activity. If you compared your predictability measure over bandpasses with different timescales, would you find the direction of V1-V4 interactions changes consistent with this previous work?

To address this question, we extended our analyses to the local field potential signals (LFPs) in monkeys, using band-limited LFP power (2–12, 12–30, 30–45, 55–95 Hz). We reran the lag sweep analyses (10-ms steps; 200-ms windows slid every 10 ms) in both directions. The Gamma band showed a feed-forward signature in the early evoked period: the V1→V4 predictability peaked at negative offsets (∼10–30ms; V1 leads), and the V4→V1 predictability peaked at positive offsets, consistent with previous findings. The results for low and beta frequency bands are also presented in the text (Supplemental Figure 13, lines 412-423).

Reviewer #3 (Public review):

R3.0: Neural activity in the visual cortex has primarily been studied in terms of responses to external visual stimuli. While the noisiness of inputs to a visual area is known to also influence visual responses, the contribution of this noisy component to overall visual responses has not been well characterized.

In this study, the authors reanalyze two previously published datasets - a Ca++ imaging study from mouse V1 and a large-scale electrophysiological study from monkey V1-V4. Using regression models, they examine how neural activity in one layer (in mice) or one cortical area (in monkeys) predicts activity in another layer or area. Their main finding is that significant predictions are possible even in the absence of visual input, highlighting the influence of non-stimulus-related downstream activity on neural responses. These findings can inform future modeling work of neural responses in the visual cortex to account for such non-visual influences.

R3.1: "A major weakness of the study is that the analysis includes data from only a single monkey. This makes it hard to interpret the data as the results could be due to experimental conditions specific to this monkey, such as the relative placement of electrode arrays in V1 and V4."

We have now added the second monkey (monkey “A”) from the same dataset (Chen et al., 2020), which includes all activity types except the lights-off condition. In addition, we collected new neural activity from one additional monkey (monkey “D”) in collaboration with the Carlos Ponce lab (monkey A: seelines 90-96, 120-132, 159, 161, 171, 183-185, 188-194, 200-203, 228-237, 254-258, 292-296, 334-342, 351-353, 358-364, 374-378, 387-393, 400-408, 414, 417-421, 539-540, 544-545, 680-681, 696-698; Supplemental Figures 1-6, 8, 11, 12, and 13; monkey D: see lines 90-96, 120-130, 132-134, 163-164, 228-235, 237-243, 292-296, 351-353, 374-378, 387-389, 539-540, 553-560, 696-698; Supplemental Figures 1-2, 4, 6, 9, 11, and 12. The conclusions for the new monkeys are qualitatively similar to the ones reported previously. The main quantitative differences are due to the very large difference in the number of predictor sites (Table 2, lines 127-134).

R3.2: The authors perform a thorough analysis comparing regression-based predictions for a wide variety of combinations of stimulus conditions and directions of influence. However, the comparison of stimulus types (Figure 4) raises a potential concern. It is not clear if the differences reported reflect an actual change in predictive influence across the two conditions or if they stem from fundamental differences in the responses of the predictor population, which could in turn affect the ability to measure predictive relationships. The authors do control for some potential confounds such as the number of neurons and self-consistency of the predictor population. However, the predictability seems to closely track the responsiveness of neurons to a particular stimulus. For instance, in the monkey data, the V1 neuronal population will likely be more responsive to checkerboards than to single bars. Moreover, neurons that don't have the bars in their RFs may remain largely silent. Could the difference in predictability be just due to this? Controlling for overall neuronal responsiveness across the two conditions would make this comparison more interpretable.

First, we note that several of the analyses and comparisons are within conditions and not across conditions, where by “condition” we mean the presence or absence of a stimulus or different stimuli (e.g., Figures 3, 5, 6, 7, Supplementary Figures 3-4, 7-13).

In Figure 4, differences in target-population responsiveness could influence predictability across stimulus types, as the reviewer points out. We therefore controlled for this by modeling EV as a function of the following neuron properties: split-half r, SNR, one-vs-rest r^2, and response variance. Regression was performed within each direction, where we then used residuals for inference_._ When comparing residuals, the predictability of checkerboard responses remained statistically higher than the predictability of the responses to moving bars (p<0.001, permutation test, Supplementary Figure 5K, lines 196-203), suggesting that the differences in predictability cannot be exclusively attributed to differences in the target population neuronal properties.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This important study provides the first direct neuroimaging evidence for the integration segregation theory of exogenous attention underlying inhibition of return, using an optimized IOR-Stroop fMRI paradigm to dissociate integration and segregation processes and to demonstrate that attentional orienting modulates semantic- and response-level conflict processing. Although the empirical evidence is compelling, clearer justification of the experimental logic, more cautious framing of behavioral and regional interpretations, and greater transparency in reporting and presentation are needed to strengthen the conclusions. The work will be of broad interest to researchers investigating visual attention, perception, cognitive control, and conflict processing.

We appreciate the positive reception to our manuscript. In the revised manuscript, we have further clarified the logic underlying the task design, adopted a more cautious tone in interpreting the behavioral and neuroimaging results, and enhanced the transparency of reporting and presentation.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study makes a significant and timely contribution to the field of attention research. By providing the first direct neuroimaging evidence for the integration-segregation theory of exogenous attention, it fills a critical gap in our understanding of the neural mechanisms underlying inhibition of return (IOR). The authors employ a carefully optimized cue-target paradigm combined with fMRI to elegantly dissociate the neural substrates of cue-target integration from those of segregation, thereby offering compelling support for the integration-segregation account. Beyond validating a key theoretical hypothesis, the study also uncovers an interaction between spatial orienting and cognitive conflict processing, suggesting that exogenous attention modulates conflict processing at both semantic and response levels. This finding shed new light on the neural mechanisms that connect exogenous attentional orienting with cognitive control.

Strengths:

The experimental design is rigorous, the analyses are thorough, and the interpretation is well grounded in the literature. The manuscript is clearly written, logically structured, and addresses a theoretically important question. Overall, this is an excellent, high-impact study that advances both theoretical and neural models of attention.

Weaknesses:

While this study addresses an important theoretical question and presents compelling neuroimaging findings, a few additional details would help improve clarity and interpretation. Specifically, more information could be provided regarding the experimental conditions (SI and RI), the justification for the criteria used for excluding behavioral trials, and how the null condition was incorporated into the analyses. In addition, given the non-significant interaction effect in the behavioral results, the claim that the behavioral data "clearly isolated" distinct semantic and response conflict effects should be phrased more cautiously.

We thank the reviewer for these helpful comments. In the revised manuscript, we have provided additional clarification regarding the SI and RI conditions (page 29), expanded the justification for the behavioral trial exclusion criteria (page 32), and clarified how the null condition was modeled and incorporated into the analyses (page 29). In addition, we have revised the description of the behavioral results to adopt more cautious wording, particularly given the absence of a significant interaction effect. For detailed responses to these specific points, please refer to the "Recommendations for the Authors" section below.

Reviewer #2 (Public review):

Summary:

This study provides evidence for the integration-segregation theory of an attentional effect, widely cited as inhibition of return (IOR), from a neuroimaging perspective, and explores neural interactions between IOR and cognitive conflict, showing that conflict processing is potentially modulated by attentional orienting.

Strengths:

The integration-segregation theory was examined in a sophisticated experimental task that also accounted for cognitive conflict processing, which is phenomenologically related to IOR but "non-spatial" by nature. This study was carefully designed and executed. The behavioral and neuroimaging data were carefully analyzed and largely well presented.

Weaknesses:

The rationale for the experimental design was not clearly explained in the manuscript; more specifically, why the current ER-fMRI study would disentangle integration and segregation processes was not explained. The introduction of "cognitive conflict" into the present study was not well reasoned for a non-expert reader to follow.

We thank the reviewer for raising these important points. In the revised manuscript, we have further clarified the rationale of the experimental design and the motivation for introducing cognitive conflict.

First, we clarified that previous neuroimaging studies relied primarily on SOA-based contrasts, which capture the temporal dynamics of attentional orienting but do not directly distinguish the functional processes of integration and segregation. We therefore established the direct comparison between cued and uncued targets in the long SOA as the critical test required by the theory, as these conditions are hypothesized to engage integration and segregation processes, respectively (pages 6-7, “The Challenge of Neural Verification”). Crucially, to successfully implement this comparison, we highlighted the specific methodological advantage of our study: the use of a Genetic Algorithm (GA) to optimize the stimulus sequence. We explained how this design maximizes statistical power specifically for contrast detection (i.e., cued vs. uncued) while maintaining high estimation efficiency, thereby directly overcoming the power constraints that had likely obscured these subtle neural signatures in prior ER-fMRI work (pages 7-8).

Second, we clarified that the manipulation of cognitive conflict was introduced with the additional aim of examining IOR expression mechanisms, specifically investigating how spatial attention modulates ongoing cognitive processing after target onset, rather than the generation of IOR itself. We have now provided a clearer rationale for embedding a modified Stroop task within the cue-target paradigm, and explained how this design allows us to dissociate semantic and response conflicts while avoiding methodological confounds present in previous studies (page 8).

The presentation of the results can be further improved, especially the neuroimaging results. For instance, Figure 4 is challenging to interpret. If "deactivation" (or a reduction in activation) is regarded as a neural signature of IOR, this should be clearly stated in the manuscript.

We thank the reviewer for pointing out the interpretational challenges in Figure 4. To address this, we have revised Figure 4 and provided a clearer and more precise interpretation of these interaction effects in the manuscript.

First, we have added explicit panel titles to Figure 4 (page 17). Panel A is now clearly labeled as the “Effect of IOR on Semantic Conflict”, while Panel B is labeled as the “Effect of IOR on Response Conflict”. We hope this visual labeling helps readers clearly identify the IOR modulation effects specific to each conflict type.

Second, we have revised the figure caption to explicitly define the interaction contrasts used to quantify these modulations, providing specific formulas (e.g., [UncuedRI – Uncued-SI] > [Cued-RI – Cued-SI] for response conflict) to ensure transparency.

Finally, regarding the reviewer’s comment on “deactivation”, we realized that our original figure terminology (e.g., “IOR effect under...”) might have caused confusion by mixing the interaction effect with the IOR effect itself. We have clarified that Figure 4 specifically illustrates the “Effect of IOR on the Semantic Conflict and the Response Conflict” (i.e., interaction effect between IOR and cognitive conflict). To interpret this interaction, we further examined the simple effects of conflict under each cueing condition. Specifically, we analyzed the neural signatures of semantic conflict (SI minus NE) and response conflict (RI minus SI) separately for the cued and uncued targets. Importantly, regarding the nature of the IOR effect itself (as displayed in Figure 3, page 14), it is not simply a uniform deactivation. Instead, by directly comparing the cued and uncued conditions for the neutral words, we observed neural changes in two directions: some specific regions exhibited an increased activation (Cued > Uncued), while others showed a reduced activation (Uncued > Cued). These differential patterns involved distinct brain networks and corresponded to the distinct integration and segregation mechanisms, respectively, rather than a global loss of activation (pages 20-21).

Reviewer #3 (Public review):

Summary:

This study aims to provide the first direct neuroimaging evidence relevant to the integration-segregation theory of exogenous attention - a framework that has shaped behavioral research for more than two decades but has lacked clear neural validation. By combining an inhibition-of-return (IOR) paradigm with a modified Stroop task in an optimized event-related fMRI design, the authors examine how attentional integration and segregation processes are implemented at the neural level and how these processes interact with semantic and response conflicts. The central goal is to map the distinct neural substrates associated with integration and segregation and to clarify how IOR influences conflict processing in the brain.

Strengths:

The study is well-motivated, addressing a theoretically important gap in the attention literature by directly testing a long-standing behavioral framework with neuroimaging methods. The experimental approach is creative: integrating IOR with a Stroop manipulation expands the theoretical relevance of the paradigm, and the use of a genetic algorithm-optimized fMRI design ensures high efficiency. Methodologically, the study is sound, with rigorous preprocessing, appropriate modeling, and analyses that converge across multiple contrasts. The results are theoretically coherent, demonstrating plausible dissociations between integration-related activity in the fronto-parietal attention network (FEF, IPS, TPJ, dACC) and segregation-related activity in medial temporal regions (PHG, STG). The findings advance the field by supplying much-needed neural evidence for the integration-segregation framework and by clarifying how IOR modulates conflict processing.

Weaknesses:

Some interpretive aspects would benefit from clarification, particularly regarding the dual roles ascribed to dACC activation and the circumstances under which PHG and STG are treated as a single versus separate functional clusters. Reporting conventions are occasionally inconsistent (e.g., statistical formatting, abbreviation definitions), which may hinder readability. More detailed reporting of sample characteristics, exclusion criteria, and data-quality metrics-especially regarding the global-variance threshold-would improve transparency and reproducibility. Finally, some limitations of the study, including potential constraints on generalization, are not explicitly acknowledged and should be articulated to provide a more balanced interpretation.

We thank the reviewer for the positive and constructive assessment of our study. In response to the concerns raised, we have carefully revised the manuscript and addressed all points in detail below. In brief, we have clarified key interpretation issues in the Discussion section, including the complementary roles of dACC activation and the distinction between statistical clustering and functional interpretation of PHG and STG activations (pages 20-21). We have also improved transparency and reporting throughout the manuscript by providing more detailed sample characteristics, clarifying exclusion criteria and global variance computation, adding illustrative supplementary figures, and standardizing statistical reporting and abbreviations (pages 28, 33). Finally, we have added a concise paragraph on limitations of the study to provide a more balanced interpretation of the findings (pages 26-27). Detailed, point-by-point responses to all specific comments are provided below (see the “Recommendations for the authors” Section).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Specific comments:

(1) The figure caption contains an unclear sentence (lines 195-196): "The target was a 450-ms colored Chinese character presented 600 ms after the fixation cue onset at the two target locations with equal probabilities." This description is ambiguous and should be revised for clarity.

Thanks for pointing this out. In the revised manuscript, we have rephrased the figure caption to improve clarity as follows (pages 9-10):

“Each trial started with a 150-ms non-informative cue presented at one of the two peripheral boxes. After a 150-ms interstimulus interval (ISI), a 150-ms fixation cue was presented at the central fixation box. Following a further 450-ms ISI, the target, a colored Chinese character, appeared at one of the two target locations with equal probabilities and remained on the screen for 450 ms. The trial ended with a variable intertrial interval (ITI) of 850, 1050, 1250, or 1450 ms (with equal probabilities).”

(2) Please provide a more detailed and clearer description of the SI and RI experimental conditions in the Methods section.

Thanks for this helpful suggestion. We have revised the Methods section to provide a more detailed description of the SI and RI conditions. Specifically, we have further described the stimulus-response mapping and clarified how the SI and RI conditions are defined based on whether the ink color and the character meaning fell into the same or different response categories under this mapping. In addition, we have added a clarification in the Methods section to make it clearer that the SI trials involved semantic conflict without response conflict, whereas RI trials involve both semantic and response conflicts (page 29).

(3) As the data were collected across two research centers, please clarify the number of participants enrolled at each site.

Thanks for this suggestion. We have now explicitly stated in the Apparatus and Data Acquisition section that 16 participants were enrolled at each site. The revised text reads (page 31)：

“The imaging data were acquired at two research sites following comparable protocols, with equal numbers of participants scanned at each site (n = 16 per site).”

(4) In the behavioral data analysis, please provide the rationale or justification for the criteria used to exclude trials.

Thanks for this comment. In the revised manuscript (page 32), we have clarified that reaction times (RTs) shorter than 150 ms were excluded as anticipatory responses, and RTs longer than 1,300 ms were excluded to limit the influence of unusually slow responses. These exclusion criteria are commonly adopted in RT research and were applied consistently across all conditions (Ratcliff, 1993; Whelan, 2008).

(5) Given that the behavioral interaction effect was not statistically significant, the conclusion on lines 236-237, "These data clearly isolated the two distinct conflict effects in the Stroop effect, namely the semantic conflict (SI-NE difference) and the response conflict (RI-SI difference)" appears overstated and should be softened accordingly.

We thank the reviewer for this important comment. We have clarified that our original statement was intended to highlight the successful isolation of conflict types based on the significant main effects of congruency (validating the task design), rather than implying a significant interaction effect. However, we agree that the original phrasing appeared unclear in this context. We have therefore revised the sentence to adopt a more cautious tone in the revised manuscript (page 12):

“These data demonstrated typical Stroop interference effects (Veen & Carter, 2005) in both the semantic (SI-NE difference) and response conflicts (RI-SI difference).”

(6) The statement on lines 281-282, "Although the IOR effect showed no effect on either the semantic conflict difference (SI-NE) or the response conflict difference (RI-SI) in the behavioral performance" lacks supporting statistical evidence. Please report the relevant test statistics.

We appreciate the reviewer’s careful reading and note that the relevant statistical evidence was missing from the original manuscript. This has now been added in the revised version. Specifically, we examined the interactions between cue validity and semantic conflict (SI vs. NE) as well as between cue validity and response conflict (RI vs. SI). Neither interaction was significant (see revised Results for full statistics on page 12), supporting our original statement that cue validity did not modulate either conflict component in behavioral performance.

(7) The manuscript mentions that a null condition (with no Chinese character presented) was included to increase statistical power for detecting differences across conditions. However, it is unclear how this null condition was actually used in the data analyses. Please clarify the role of the null condition in both the behavioral and neuroimaging analyses.

Thanks for this comment. We regret that this was not sufficiently clear in the original manuscript. The null condition was included for neuroimaging purposes and was not used in the behavioral analyses, as no response was required in these trials. In the fMRI analyses, null trials served as the implicit baseline and were not modeled as regressors of interest. Task-related activities for all experimental conditions were therefore estimated relative to this null baseline, facilitating estimations of task-related responses in randomized event-related designs (Burock et al., 1998; Friston et al., 1999; Liu, 2004). We have clarified this point in the revised manuscript (page 29).

References

Burock, M. A., Buckner, R. L., Woldorff, M. G., Rosen, B. R., & Dale, A. M. (1998). Randomized event-related experimental designs allow for extremely rapid presentation rates using functional MRI. NeuroReport, 9(16), 3735-3739. https://doi.org/10.1097/00001756-199811160-00030

Friston, K. J., Zarahn, E., Josephs, O., Henson, R. N. A., & Dale, A. M. (1999). Stochastic designs in event-related fMRI. NeuroImage, 10(5), 607-619. https://doi.org/10.1006/nimg.1999.0498

Liu, T. T. (2004). Efficiency, power, and entropy in event-related fMRI with multiple trial types: Part II: design of experiments. NeuroImage, 21(1), 401-413. https://doi.org/10.1016/j.neuroimage.2003.09.031

Ratcliff, R. (1993). Methods for dealing with reaction time outliers. Psychological Bulletin, 114(3), 510-532. https://doi.org/10.1037/0033-2909.114.3.510

Whelan, R. (2008). Effective analysis of reaction time data. The Psychological Record, 58(3), 475-482. https://doi.org/10.1007/BF03395630

Reviewer #2 (Recommendations for the authors):

(1) The paper is a bit too lengthy, with a lot of information that is hard for non-experts to grasp.

We thank the reviewer for this comment. We realized that the Introduction was the most challenging section for general readers. In the revision, we refined the text in the Introduction for a better structure and more reader-friendly wording to improve readability. In addition, following the reviewer’s suggestion (Recommendation 4 below), we have added short subsection titles to the Introduction, Results, and Discussion sections to better organize the content and highlight the main ideas. We hope these revisions make the manuscript more accessible and easier for a broader audience to follow.

(2) Please double-check the stats, as some of the results presented in the main text do not align well with the figures. Take Figure 2 as an example.

We appreciate the reviewer’s concern and have double-checked all statistics. All the results are consistent between the figures and the main text. Take Figure 2 as an example (page 12), the perceived discrepancy probably was caused by the fact that the descriptive values reported in the main text are marginal means for the main effects (i.e., the overall average of one factor, collapsed over the other factor), whereas Figure 2 shows the mean for each Congruency × Cue Validity condition (i.e., simple effect).

(3) The reasoning that the neuroimaging findings support the dissociation between integration and segregation needs to be improved.

We thank the reviewer for this important comment. In the revised Discussion (pages 1921), we have strengthened the reasoning linking our neuroimaging findings to the dissociation between the integration and segregation processes. Specifically, we make it clear how the distinct activation patterns observed for the cued and uncued targets map onto the different functional demands proposed by the integration-segregation theory. The cued targets were theorized to recruit the frontoparietal attentional control networks, consistent with the re-engagement of an existing object file (integration). On the other hand, the uncued targets should engage the medial temporal and temporal association regions responsible for novelty detection and episodic encoding, consistent with the creation of a new object file (segregation). We hope the reviewer finds that the revision offers a clearer explanation of how the observed neural patterns are consistent with a dissociation between the integration and segregation processes.

(4) Please use short section titles to organize the introduction, results, and discussion sections. For instance, the discussion section is a long chunk of text (almost 9 pages) and is pretty dense, making it hard to quickly grasp the ideas the authors want to convey.

Thanks for this helpful suggestion. Following the reviewer’s recommendation, we have now added short subsection titles to the Introduction and Discussion sections to improve structure and readability. For the Results section, we have maintained and further refined the existing subheadings to ensure consistent organization.

Reviewer #3 (Recommendations for the authors):

I found this manuscript to be a timely and substantive contribution to the study of attention and cognitive neuroscience. To my knowledge, it provides the first direct neuroimaging evidence relevant to the integration-segregation theory of exogenous attention, a framework that has been influential in behavioral work for more than two decades but has lacked clear neural support. The study is conceptually well motivated, methodologically solid, and generally clearly reported. The findings differentiate neural substrates associated with integration and segregation processes and further show how inhibition of return (IOR) interacts with semantic and response conflicts at the neural level.

The manuscript is well organized, the writing is mostly clear, and the progression from theory to hypotheses and methods is easy to follow. The combination of IOR with a modified Stroop paradigm is a clever choice that extends the theoretical scope of exogenous attention research. The use of an optimized event-related fMRI design based on a genetic algorithm is also a strength and reflects careful attention to design efficiency.

The main results are internally consistent and theoretically meaningful. Integration related activity in the fronto-parietal attention network (including FEF, IPS, TPJ, and dACC) and segregation-related activity in medial temporal areas (PHG and STG) it well with the proposed framework, and the pattern of activations is coherent across analyses.

Overall, I think this is a carefully executed study that offers much-needed neural evidence bearing on the integration-segregation theory of exogenous attention. I would recommend the following revisions.

Suggestions:

(1) In the Discussion (pp. ~17-18), dACC activation is described both in terms of general cognitive control demands and as reflecting a possible inhibitory bias toward the cued direction. It would help the reader if you could briefly indicate whether you see these as complementary (e.g., dual roles within the same region) or as more competing interpretations.

We thank the reviewer for this helpful comment. We have clarified in the revised manuscript that dACC exerts general cognitive control demands and biasing against the cued direction are complementary rather than competing interpretations. Specifically, we described how the dACC is involved in both the cognitive control required for target integration and the inhibitory bias toward the cued location, thereby highlighting its dual roles within the same region. The revised section reads as follows (page 20):

“Furthermore, the observed increase in the left dACC activity under the cued relative to the uncued condition likely reflected the engagement of cognitive control mechanisms (Botvinick et al., 2004; Chung et al., 2024; Mayer et al., 2012; Veen & Carter, 2005), particularly in resolving the conflict between the task-driven requirement of target integration and the reduced accessibility of the cue-initiated representation. In this context, the heightened activation of dACC may also reflect its role in fulfilling the inhibitory bias toward the cued location (Mayer et al., 2004) and discouraging inefficient integration attempts at a location marked as less relevant.”

(2) In the Discussion, you could consider adding a short paragraph explicitly acknowledging a few limitations and how they might constrain generalization of the findings. A concise reflection of this kind would give a more balanced picture without undermining the main conclusions.

We appreciate this helpful suggestion. In the revised manuscript, we have added a concise paragraph explicitly addressing a key limitation of the present study (pages 26-27). Specifically, we acknowledge that the absence of behavioral interactions alongside clear neural effects requires cautious interpretation. We discussed how this dissociation may reflect differences in measurement sensitivity between behavioral and neural indices, consistent with prior findings (Chen et al., 2006; Wilkinson & Halligan, 2004). We also note that the use of a GA-optimized sequence, while improving statistical efficiency, may have introduced unintended regularities in event order that could influence behavioral strategies.

(3) Since the dataset is hosted on GitHub, adding a short note in the Data Availability section about whether the repository will also include analysis scripts or future replication data would further enhance transparency and long-term usefulness.

Thanks for this helpful suggestion. We have revised the Data Availability section (page 35) to clarify that the GitHub repository contains the processed data used in the final analyses. Analysis scripts and additional materials for replication are available from the authors upon reasonable request.

(4) In the Results section, the formatting of statistics is not fully consistent. For example, some reports use spaces around symbols (e.g., "η² = 0.301") whereas others do not (e.g., "p< .001"). It would be good to standardize this (e.g., "p < .001", "η² = .30") across the manuscript.

Done as suggested.

(5) A few abbreviations appear before they are defined-for instance, SPC (superior parietal cortex) shows up in the Results (response conflict section) before the full name is given. Ensuring that each abbreviation is defined at first mention would help readers who may be less familiar with all of the regional acronyms.

Thanks for this comment. We have conducted a thorough check of the manuscript and ensured that all abbreviations are defined upon their first occurrence.

(6) The text sometimes refers to "PHG/STG" as a combined cluster, while at other points, PHG and STG are described separately. It would be useful to clarify under what circumstances they are treated as a single functional cluster versus distinct regions of interest, and to keep the nomenclature as consistent as possible between the main text and the tables.

Thanks for raising this point. In the revised manuscript, we have clarified this issue by distinguishing between statistical clustering and functional interpretation. In the whole brain analysis, activations in the left hemisphere formed a single continuous cluster spanning the PHG and STG; therefore, this cluster is labeled as “PHG/STG” in Table 1. We have explicitly noted the continuous nature of this cluster in the Results section (page 15) to ensure clarity:

“Notably, in the left hemisphere, these activations formed a continuous cluster spanning both regions (labeled as PHG/STG in Table 1).”

(7) It would be helpful to provide a bit more detail about the sample characteristics (e.g., age range, handedness, and inclusion/exclusion criteria) and to state explicitly how many participants, if any, were excluded from the analyses and for what reasons. This would help readers better evaluate data quality and generalizability.

Thanks for this helpful suggestion. We have revised the Participants section (page 28) to provide the full details regarding our sample:

“32 healthy participants with normal or corrected-to-normal vision and normal color vision were recruited. All participants were right-handed and reported no history of neurological or psychiatric disorders. Data from three participants were excluded due to excessive head movements and high global variances (see fMRI Data Analysis), leaving 29 participants for analysis (18 female, 11 male; aged 18-30 years, M = 22.69, SD = 2.58).”

Furthermore, we have provided a clearer description of the exclusion criteria in the Data Analysis section (pages 33-34) as follows:

“Runs with motions exceeding one voxel length in any direction were excluded (resulting in the exclusion of two runs) …Runs with global variance equal to or over 0.1% were excluded, resulting in the exclusion of eight runs (see Supplementary Information for details). Ultimately, three participants were excluded because neither run met the quality criteria. All remaining participants retained both runs, except for three individuals who each contributed only one valid run.”

(8) Given that participants were excluded based on global variance exceeding 0.1%, it would be very informative to include, in the Supplementary Materials, an illustrative figure showing the signal time series (or global signal variance over time) for excluded participants.

We appreciate this valuable suggestion. In the revised Supplementary Materials, we have included a new figure (Figure S2) that plots the global signal time series for the excluded runs to illustrate the signal patterns that led to their exclusion based on global variance.

(9) Relatedly, it may help to more explicitly describe how global variance was computed (e.g., over which time window, after which preprocessing steps, and whether it was calculated on whole-brain signal or within specific masks). A concise clarification would make the exclusion criterion easier to interpret.

Thanks for this helpful suggestion. We have now clarified in the manuscript how global variance was computed (page 33) and have also provided a more detailed description of the computation procedure in the Supplementary Materials (page 4). Specifically, after the standard preprocessing (slice timing correction, 3D motion correction, spatial smoothing, linear trend removal, and high-pass temporal filtering), the global signal was computed for each run as the mean signal across voxels with intensity values greater than 100 in each volume. Global variance was then quantified as the temporal variance of this run-wise global-signal time course across all volumes, providing a quality-control index of signal stability.

(10) Rather than only reporting a single overall exclusion rate (e.g., 5.52% of total trials), it would be informative to break this down by source, reporting separately the proportion of trials excluded as RT outliers and the proportion excluded due to response errors. This would further improve transparency regarding the behavioral preprocessing pipeline.

Thanks for this helpful suggestion. We have now broken down the overall exclusion rate by source in the revised manuscript. Specifically, we reported that 4.29% of trials were excluded due to incorrect responses, and 1.24% of trials were excluded as RT outliers (page 32).

References

Botvinick, M. M., Cohen, J. D., & Carter, C. S. (2004). Conflict monitoring and anterior cingulate cortex: an update. Trends in Cognitive Sciences, 8(12), 539-546. https://doi.org/10.1016/j.tics.2004.10.003

Chen, Q., Wei, P., & Zhou, X. (2006). Distinct neural correlates for resolving stroop conflict at inhibited and noninhibited locations in inhibition of return. Journal Of Cognitive Neuroscience, 18(11), 1937-1946. https://doi.org/10.1162/jocn.2006.18.11.1937

Chung, R. S., Cavaleri, J., Sundaram, S., Gilbert, Z. D., Del Campo-Vera, R. M., Leonor, A., Tang, A. M., Chen, K.-H., Sebastian, R., Shao, A., Kammen, A., Tabarsi, E., Gogia, A. S., Mason, X., Heck, C., Liu, C. Y., Kellis, S. S., & Lee, B. (2024). Understanding the human conflict processing network: A review of the literature on direct neural recordings during performance of a modified stroop task. Neuroscience Research, 206, 1-19. https://doi.org/10.1016/j.neures.2024.03.006

Mayer, A. R., Seidenberg, M., Dorflinger, J. M., & Rao, S. M. (2004). An event-related fMRI study of exogenous orienting: supporting evidence for the cortical basis of inhibition of return? Journal Of Cognitive Neuroscience, 16(7), 1262-1271. https://doi.org/10.1162/0898929041920531

Mayer, A. R., Teshiba, T. M., Franco, A. R., Ling, J., Shane, M. S., Stephen, J. M., & Jung, R. E. (2012). Modeling conflict and error in the medial frontal cortex. Human Brain Mapping, 33(12), 2843-2855. https://doi.org/10.1002/hbm.21405

Veen, V. V., & Carter, C. S. (2005). Separating semantic conflict and response conflict in the Stroop task: A functional MRI study. Neuro Image, 27(3), 497-504. https://doi.org/10.1016/j.neuroimage.2005.04.042

Wilkinson, D., & Halligan, P. (2004). The relevance of behavioural measures for functional imaging studies of cognition. Nature Reviews Neuroscience, 5(1), 67-73. https://doi.org/10.1038/nrn1302

Author response:

The following is the authors’ response to the previous reviews

Public reviews:

Reviewer #1 (Public review):

The sample size for the ex vivo electrophysiology conducted on the calb1+ lamina I projection neurons (Figure 5) is limited to a total of six recorded neurons. Given the difficulty and complexity of the preparation, this is understandable. Notably, since approximately 87% of lamina I projection neurons heavily innervated by Trpm8+ terminals are calb1+, these six recordings of such neurons in Figure 4E could also be calb1+.

As noted in our initial resubmission, we fully accept that the sample size is limited. We have already toned down statements related to this, to say that our findings “strongly suggest” that the cells with dense Trpm8 input are cold-selective (both in the Abstract and Results)

Reviewer #2 (Public review):

In the characterization of recorded neurons in close contact or in the absence of this contact with TRPM8 afferents, the number of recorded neurons is relatively low. In addition, the strength of thermal stimuli is not very well controlled, preventing a more precise characterization of the connectivity.

The authors acknowledge that, technically, this is a very difficult preparation with very low yield as far as obtaining successful recordings. Moreover, the tissue needs to be maintained at room temperature which is obviously not ideal when characterizing cold thermoreceptors due to the unavoidable effects of low temperature on cold-activated receptors.

Please see our response to Reviewer #1 (Public review):

Reviewer #3 (Public review):

The main limitation remains the relatively small number of neurons that could be recorded electrophysiologically. While understandable given the complexity of the preparation, this necessarily limits generalization.

Again, please see our response to Reviewer #1 (Public review):

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Line 609. The authors used the Trpm8Flp;RCE:FRT;Ai9 mice in some electrophysiological experiments. What is the function of the Ai9 allele (a Cre-dependent reporter) in this cross? Should not be a Cre line as well?

One of the mice used for electrophysiological experiments was Trpm8Flp;RCE:FRT;Ai9, and this animal received an injection of AAV encoding Cre into the caudal ventrolateral medulla, resulting in tdTomato expression in spinal projection neurons. This part of the Methods was inadvertently omitted from the resubmitted version (see next point). This has been corrected, and in addition, this information is shown in the cartoon in Fig 4A and is explained in the figure legend.

(2) Line 860. Phrase is incomplete

We apologise for this – 3 lines from the original version had been deleted inadvertently. This has now been corrected.

(3) Line 103 "These results are therefore consistent with the transcriptomic findings described above (36,37)."

I would revise the references used to support this claim. Reference 37 is a transcriptomic atlas of the brain. I could not find TRPM8 expression data in DRG in this reference.

Figure S4 of reference 37 deals with the mouse peripheral nervous system and describes Trpm8 classes of primary afferent. More detail on these cells (including expression of VGLUT3, Tac1, Calca and Trpv1) can be found in the associated website: mousebrain.org/adolescent/genesearch.html. We have therefore left this reference as it is.

(4) Line 242. "neurons with dense Trpm8 input had significantly lower sEPSC frequencies compared to those that lacked dense Trpm8 input".

This is an interesting paradox because cold thermoreceptors (i.e. the presumed direct monosynaptic input to these projection neurons) are known to be spontaneously active at physiological skin temperatures. This is well characterized in trigeminal corneal endings (DOI: 10.1038/nm.2264). In fact, the decrease in this spontaneous activity can be used by mice to faithfully detect warm stimuli (DOI: 10.1016/j.neuron.2020.02.035). This reviewer likes to remark that this low spontaneous frequency may be due to the non-physiological temperature of this preparations, leading to partial adaptation/desensitization of the afferents. Perhaps, it also influences the amplitude (e.g. release probability) of EPSPs (I do not expect you to do anything about my remark).

These are interesting points, but we do not feel that we can add anything here.

(5) Figure 3A. It would be useful to include orientation references (dorso-ventral, mediolateral) in the images. Same comment applies to Figure 5C.

Since these are horizontal sections, the axes are medio-lateral and rostro-caudal. Corresponding orientation markers have been added to both figures.

(6) Figure 3F. If I understood correctly, the light pulse used for optogenetic activation is delivered directly through the objective used for recording the cell. Thus, the distance between pre and postsynaptic neuron should be minimal. That being the case, I do not understand how a monosynaptic input can have a delay of 5 or 7 ms. Am I missing something?

The relatively long duration of latency is likely to reflect a slow rise time of depolarisation in the Trpm8 terminals, so that although channels will open very rapidly, there is a delay until the boutons reach action potential threshold. Hachisuka et al (2016) recorded from Nts^Cre;Ai32 mice (i.e. coding for channelrhodopsin) and found typical latencies of >5 ms (Fig 5E in that paper). We believe that this delay is exacerbated by the low levels of expression of ChR2 that we were able to achieve with the neonatal i.p. injection approach. We have provided a brief explanation for this, and cited the reference in the Results section (lines 197-198).

(7) Figures 4E/H. To be meaningful, the pie charts should include the n (total number of neurons). See, for example figure 5J.

Numbers have been added to the pie charts.

Author response:

Public Reviews:

Reviewer #1 (Public review):

(1) Speed and mismatch between locomotion and visual stimulation.

The authors do not clearly describe the definition of locomotion versus the resting state. The speed should, by itself, have an impact on neuronal responses, especially at the onset of locomotion. Several published studies show that the mismatch between a visual stimulus and the speed of the animal induces specific responses in V1, both in excitatory and subtypes of inhibitory neurons. The authors should address these points upfront in the manuscript, since it is likely a major variable explaining their results.

We will clarify in the methods that a trial was considered as locomotion when an animal ran at a minimum of 3 cm/s for at least 80% of the 10 s stimulus presentation, and was considered rest when running under 3 cm/s during the same fraction of time. Trials with abrupt changes from locomotion to rest were rare and excluded following these criteria.

Locomotion speed and visuomotor mismatch can influence neuronal responses in V1 but in the large majority of our trials mice either run continuously at a stable speed or remained still

i.e locomotion onsets or offsets did not occur (see Hinojosa et al. 2026 for example running traces). Furthermore, sensitizing and depressing neurons were typically recorded simultaneously within the same field of view, experiencing identical locomotor behaviour. For these reasons, we think it is unlikely that differences in speed or mismatch alone can account for the different increase in amplitude observed between depressors and sensitizers.

To directly address this point and further explore the role of speed on V1 neurons, we will quantify the relationship between running speed and amplitude increase in both PCs and interneurons, and include these analyses in the revised version of the manuscript.

(2) Use of deconvolution with MLSpike.

Some results (Figure 2) exclusively depend on the deconvolution of calcium signals into spikes (since the initial peak is not seen in calcium transients). The authors should validate this result either with electrophysiological recordings or with the use of another deconvolution method (e.g CASCADE), emphasising the limitations of this approach and the limitations of the time resolution of calcium imaging.

A similar initial increase in amplitude followed by fast depression has been observed previously with electrophysiological recordings in V1 (Chance et al., 1998; Jin & Glickfeld, 2020; Varela et al., 1997). We will further validate our results using an alternative spike inference method like CASCADE (Rupprecht et al., 2021), as well as expanding on the limitations of our approach.

(3) The manuscript is centred around a specific increase in visual responses in sensitizing neurons during locomotion, both in the fraction of responsive neurons and response magnitudes.

It is hard to tell whether this difference is due to a greater scaling effect of locomotion, a difference in responses during the resting state, or both. The manuscript should further explore and discuss the differences in responses between sensitizing and depressing neurons, both during the resting state and locomotion. Adding metrics and direct comparisons of the magnitudes of fast responses, slow responses, and time integrals between sensitizing and depressing neurons in resting and locomotion states would help to clarify this. Same for fractions of responsive neurons of each type in each condition. E.g., the slow phase is harder to judge from the plots, but the DeltaF/F integral shown in Figure 1G seems to suggest the difference in response magnitude between sensitizing and depressing neurons is largest in locomotion state, rather than resting state. How do these integrals look for inferred firing rates shown in Figure 2?

We will further explore the response dynamics of adaptive types within the locomotion and resting state, highlighting the differences between calcium signals and inferred spikes. We will then include our findings in the new version.

(4) There is something counterintuitive about how the changes in inhibition onto sensitizing and depressing neurons during locomotion explain the reported activity changes.

Sensitizers receive reduced SST input and increased PV input during locomotion. If SSTs depress and PVs sensitize (and this is the main reason why sensitizers, which receive dominant input from SSTs sensitize, and vice-versa), how is it possible that this switch does not alter the sensitizing or depressing nature of these neurons' responses in locomotion? Are these changes insufficient to flip the dominant SST-PV drive? Figure 6D-E seems to show there is a flip, at least for sensitizers. How do authors explain this? Do authors think this is related to the narrowing of the adaptive index distribution shown in Figure 1C?

This result is only counterintuitive if we consider exclusively the internal connections within V1. The PV:SST ratio changes from 0.9 during rest, dominated by SST induced sensitization, to 1.2, dominated by PV depression. Although adaptation is strongly driven by the opposing inhibition of PV and SST in PCs during locomotion, its origin is more easily explained by an external input (SS) that targets VIPs, PVs and PCs. As a result, when locomotion increases the drive coming from SS input, it injects a source of sensitization that partly balances the decrease in PV:SST ratio, preventing a switch in their adaptive properties which, although reduced, remain sensitizing. We will include these calculations in the revised version.

(5) Presentation of the experimental data and the model.

The manuscript introduces the results of interneuron recordings during the description of the model. Similarly, the results of optogenetic manipulations are presented inside the model's description. It would be clearer to present all experimental data first and introduce the model later, fitting it to all experimental evidence previously presented.

We understand that a clear separation between experimental and modelling results is often preferred in papers that combine these approaches but in our case modelling and experimental data are highly interdependent and we believe that an overlapping presentation make it easier for the reader to appreciate the links. One example is Fig. 2G-L that shows experimental results validating a key feature of the model - the use of average response dynamics for each population of interneuron. Similarly, the results in Fig. 3 validate the use of the VIP response dynamics as the template for the slow modulatory input to layer 2/3. Then the results of optogenetic experiments in Fig. 4 are used to narrow down fits to the model. For these reasons, we have chosen to present experimental results and the model in this more integrated manner.

Reviewer #2 (Public review):

In the model, they postulate that synapses within the 6-cell-type network - sensitizing, intermediate, and depressing E cells, and PV, SST, and VIP I cells - and from three sources of external input to each of the six types all change between rest and locomotion (except that connections between the E cells don't depend on their types). There are a lot of degrees of freedom, and this makes interpretation of the results difficult. I would have liked to have seen more efforts to constrain the degrees of freedom. For example, there seems to be very little difference between the three E cell types in any of the three types of external input received. Why not constrain them all to get the same external input and see if it significantly affects model fit? Or what if synapses from the three types of external input are left unchanged, and only change their strengths between rest and locomotion? How well could this do? During optimization, why not constrain the changes between rest and locomotion, for example, by putting an L1 penalty on the changes or the relative changes, trying to force them to be sparse, and see whether there are roughly equally good fits? And then, if the main changes are in a small set of synapses, can the authors isolate changes to that small set and do roughly equally well? What about looking at the principal components of the weight changes across models, to isolate patterns of change that are most important?

To reduce the number of degrees of freedom and ease interpretation we did limit the model fitting for adaptive subtypes by fixing the PC-PC (𝑤_{𝑃𝐶_𝑃𝐶}) and restricting the external inputs weights (𝑤_{𝐹𝐹_𝑃𝐶}, 𝑤_{𝑆𝑆_𝑃𝐶}, 𝑤_{𝐹𝐵_𝑃𝐶}) to changes of ± 10 %. We will explicitly explain these constrains in the methods and discuss its limitations.

We thank the reviewer for their suggestions of testing different conditions to find those providing the best fit for sensitizing and depressing PCs. We tried an approach similar to that described by Dipoppa et al. 2018 by using the locomotion weights as initial conditions for the rest traces and introducing penalties at later stages. However, the local optimization algorithms failed to reach distant regions of parameter space containing minimum solutions for the rest condition. We finally opted for repeating the same process of initial condition searching for locomotion and rest, making the L1 penalty approach impracticable in our case. We believe this approach is effective because it has both allowed us to describe circuit changes during internal-state transitions (the present paper) and, more recently, it has made a series of predictions about different learning states that have been confirmed by optogenetic tests (Hinojosa et al., 2026). We will nevertheless explore this and other of the reviewer suggestions to further optimize the fitting in the revised manuscript.

In terms of comparing to previous works, when optogenetic manipulations of SST and PV are done to test various hypotheses, I would like to see some discussion of what is already known from the authors' 2022 paper and what they are adding or testing that wasn't known or tested from that paper. And Dipoppa et al (2018) also found weight changes to account for the difference between rest and locomotion. They were looking at a fixed point of responses of neurons across retinotopic space to stimuli of various sizes with only one E-cell type, whereas they are accounting for trajectories across time considering 3 E-cell subtypes but without variation in stimuli or retinotopic position of neurons, so the efforts are somewhat different, but still, it would be good to see a bit more discussion of what is in agreement or in contradiction in the conclusions.

Thanks for this prompt. We will add further discussion of this work in light of the Heintz et al. (2022) and Dipoppa et al. (2018) papers.

(1) The main result is that sensitizers increase their responses with locomotion ~2X (for dF/F) or about 3.5X (for spikes) more than depressors. But there are other differences between sensitizers and depressors, for example sensitizers have smaller initial stimulus responses at rest, and depressors have larger. What if cells were divided into tertiles by initial stimulus response at rest? Would the authors see the same differences in the effects of locomotion? If so, can they establish whether the difference is really attached to the adaptation properties rather than to, for example, the initial responses, for example, by comparing the regression of response increase against AI vs the regression of response increase against initial resting response? And there might be other controls to be done for other features in which sensitizers and depressors differ.

We will explore the possibility that initial response influences the increase in amplitude. Preliminary data suggest that initial amplitude is higher in depressors than in sensitizers.

(2) Lines 103 and following: the authors refer to a "second notable change" which is the narrower distribution of adaptive effects, but I think this is trivial. The adaptive index is AI=(R1-R2)/(R1+R2), where R1 is response 0.5-2.5s after stimulus onset and R2 over 8-10s. But if the change is additive, as suggested by the dF/F figures (and I believe the distributions of AI here are based on dF/F measurements) -- adding the same constant to R1 and R2 will shrink |AI| without changing the sign of AI. So this would seem to just be a signature of a change that is primarily additive rather than multiplicative.

Also, if the authors do decide that they are going to focus on spikes after showing the raw dF/F, then this analysis should be repeated for spikes.

We agree with the reviewer and will change the text accordingly to highlight the additive nature of the change in amplitude. We will also show the analysis with spikes (this shows similar results as the calcium data).

(3) Figure 2, F is supposed to be D minus E, but it doesn't look like it. For example, the initial response under locomotion is very similar in sensitizers and depressors, so the initial difference in F should be small, but it's not; and at rest, depressors initially have larger responses than sensitizers, whereas later depressors have smaller responses than sensitizers, yet the difference at rest is positive at all times. Something seems wrong here.

We apologize for the confusion this has caused. Figure 2F does not represent the difference between sensitizing and depressing PCs from panels D and E. Instead, it shows the time-varying difference between locomotion and rest states of sensitizers (blue, in figure 2D) and depressors (green, in figure 2E). Thus, panel F shows within-population modulation by behavioural state, rather than differences between sensitizing and depressing neurons. We will amend the figure legend and main text to explain this point and avoid misinterpretation.

Reviewer #3 (Public review):

(1) Key concern is the usage of dF/F signals for all analyses, especially when comparing responses.

(1a) Figure 1G: Comparison of sensitisers and depressors. It is important to consider what the baseline rates are when making these comparisons, especially when comparing the degree of effects between different cell types. For example, if baseline rates for sensitizers were overall higher, it would mean the difference in gain of response would be lower, and could affect the results in the opposite direction of what is claimed. One option to account for this would be to z-score the overall responses, using the same normalization for locomotion and rest. We also suggest plotting differences in sensitisers, intermediates, and depressors as a function of firing rate. Matching for firing rate across each PC categorization and calculating delta AI for each matched firing rate bin.

(1b) Figure 2A-F: The above is an even more significant issue when it comes to estimating spiking rates. The methods do not state how dF/F is calculated. If these are based on using the pre-stim as the reference, the algorithms for spike rate used might not be appropriate if this were used. Using pre-stimulus referencing could result in the estimate going into the wrong range in the calculation of the spike rate.

(1c) In both cases above, it could be a problem if baseline firing rates are different between cell types, or states (locomotion/stationary). The latter is established to have effects on many cell types measured, and so needs to be account ted for very carefully.

The DF/F0 trace was calculated using the mode of the whole trace as F0. While this approach is less sensitive to biases than subtracting the pre-stimulus, it does not consider noise levels like the z-score suggested by the reviewer. We will, therefore, normalize the calcium traces to z-score to further account for changes in the baseline. Spike inference using MLSpike, however, explicitly models baseline noise and subtracts its effect from that of the spikes calculated from the calcium signal (Deneux et al., 2016). This transformation preserved the difference in amplitude triggered by locomotion between depressing and sensitizing PCs while revealing their similar baseline activity (see Figs. 2D,E and F). These results indicate that the distinct changes in response amplitude between sensitizing and depressing PCs during locomotion are not driven by baseline differences. We will add this explanation to the methods section.

We will also plot the changes in activity with locomotion across cell types as a function of firing rate and add these results to the revised manuscript.

(1d) It would be informative to see per-neuron comparison for adaptive indices during rest and locomotion states. This could be visualized using a scatter plot with AI-rest vs. AI-locomotion for Figures 1D- 1F and 2J- 2L.

(1e) Are neurons more strongly modulated between locomotion and rest, also more likely to experience a shift in AI indices (i.e. delta AI). Is there a correlation between the change in firing rate between behavioral states and Delta AI (Loco-Rest)? If so, is this present for all neuron subtypes (e.g. VIP, SST, and PV)?

Sorting was carried out separately on locomotion and rest data sets to capture the adaptive properties of the network under each condition. When assessing the change in adaptive index in individual cells there was a weak but significant correlation (r = 0.10, p<0.05), probably due to trial to trial stochasticity in the network which has been shown to be present in V1 (Carandini, 2004; Lee et al., 2010). Although adaptation profiles of individual PCs are not fully conserved across rest and locomotion, the observed overlap exceeds that expected by chance, suggesting that stochastic fluctuations modulate an underlying, stable circuit organization. Despite including the stochastic component of the responses, the conclusions hold: sensitizers undergo a larger gain modulation than that of depressors. We will include this analysis and the correlation between change in firing rate and Delta AI in the revised version of the paper.

(1f) Optogenetic inhibition of VIP neurons on average abolished the slow depressive effects of adaptation in SST (Figure 3). The strength and prevalence of this effect are unclear. Perhaps one can perform a bootstrap control and opto AI indices and calculate whether AI was significantly reduced following optogenetics inhibition, and if so, on average, how likely was this to occur for the recorded SST neurons? This is important in knowing that the average effects (Figure 3D) aren't driven by a portion of SST neurons, especially as this is later used to confirm the region of parameter space and affects the subsequent results in Figure 4.

The strength and prevalence of the effect are reflected in the distribution of AI changes across SST neurons, which is centred at AI = -0.3 ± 0.3, indicating a consistent reduction in AI across the population instead of being driven by a small portion of SST neurons. To further clarify this, we will report the proportion of SST neurons showing a reduction in AI and include statistical analyses on the changes.

(2) Statistics for the effects. There is a mention of Liner mixed models, but no information is given on the actual models being used and tested. This is particularly for the case of Figure 1G, where there is a composition of effect sizes between different populations. What precise significance test is being used? Are the stats on paired cells when considering locomotion and rest?

We used Linear mixed models to test for statistical significance between different conditions composed of hundreds of cells from several mice, i.e. nested analysis (cells nested within mice; see (Judd et al., 2017)). For analyses such as Fig. 1G, we considered locomotion state, adaptive type and their interaction (loco’adap) as fixed effects and mouse number as the random effect. The p-values depicted in the legend indicates the interaction between locomotion and adaptive type, i.e. the increase in amplitude during locomotion is significantly different in sensitizers compared to depressors with p < 0.0001. We will revise the method section and figure legends to explicitly describe the model and statistical test used.

(3) Model parameters: It is acknowledged that there is a large range of parameters that can model the responses effectively, up to 11% of initial conditions. At 9000 initial conditions, this is around 1000. The parameter estimates are then considered as the mean of each parameter. This seems like a strange choice for a few different reasons:

(3a) A mean solution might not be one of the solutions. Let's say the parameters range over a large dimensional space. They could occupy non-overlapping / discontinuous subspaces. In that case, the mean parameters do not necessarily fall within the solution subspaces. Therefore, this reduction to means might not be valid.

(3b) Compare distributions rather than means. There are multiple distributions of parameters between conditions. All stats should be on the comparison of distributions rather than just the means.

To test for the presence of subsets of solutions grouped around different parameter values we plotted the distribution of each parameter across all the good solutions found. Most of the weights were a gaussian distribution centred around the mean and, most importantly, none of them had two peaks. Furthermore, after computing the mean weight values we plotted the solutions given by them in the model, and it rendered a good fit as shown in the figures. We will include those distributions in the new version and base the overall comparison on these distributions.

(4) Visualizing weight matrices: It is very challenging to interpret the weight matrices. Furthermore, it appears that the stationary and locomotion conditions fit independently, and given the large parameter spaces, it is even harder to interpret. Can the fitting instead be done by fitting on one and using those at the initial conditions for the other state? Figure 7 shows an initiative cartoon, but it is not clear how the matrices in Figures 5 and 6 lead to the summary shown in Figure 7. It is also not clear why the connections between inhibitory neurons are not shown in Figure 7. One option is to perhaps run some kind of dimensionality deduction on the parameter space to better interpret the data. When showing deltaWeights, was the model initialised with 'Rest' weights and allowed to change? It is not obvious what the difference is between 'relative change in connection weights' and 'relative change in synaptic weights'.This needs to be clarified.

Thanks for raising this concern. We will firstly try to make the weight matrices clearer to interpret.

Regarding the fitting of rest and locomotion conditions, we fitted the locomotion traces first and used those solutions as initial conditions for the rest traces. However, this rendered no good solutions as minimums in the parameter space were too far from the initial starting points. We opted, therefore, for repeating the same process of initial condition searching for locomotion and rest. This approach is less biased in satisfying our aim of finding solutions that fit the data and can explain their dynamics, which are different for each condition. We believe this approach is effective, as not only has it allowed us to describe circuit changes during internal-state transitions but has also made a series of predictions under different learning states that were confirmed by optogenetic tests (Hinojosa et al., 2026).

We simplified Fig. 7 for clarity but we will make it more accurate and explain it more in detail in the legend, including connections between interneurons.

Interpreting high-dimensional parameter spaces can be challenging. In this study, we focused on low-dimensional summaries of the parameter space (e.g., average connection weights and their distributions across populations), which revealed consistent and interpretable differences between sensitizing and depressing neurons. Importantly, our conclusions do not rely on individual parameter values, but rather on systematic differences across populations that are robust across solutions. Additionally, we ran clustering analysis and found that there is no parameter that can be removed. We focused, therefore, on the larger and more robust differences. We will explore additional dimensionality reduction approaches and include these results if they provide further insight beyond the current analyses.

Finally, the change in weights was calculated with equation 4, in which the weight from locomotion and rest, obtained through independent fits, were used to calculate the relative change from rest to locomotion. These were either connection weights (equation 2) which consider the strength of the connection between cell j and i, or synaptic weights (equation 3) which express the weight of individual synapses by dividing connection weights by the number of presynaptic cells and probability of connection. This distinction arises because we used average traces from all the neurons imaged to fit the model, requiring considering the number of cells to know the strength of individual synapses. We will add this explanation in the results and methods sections.

(4a) Model parameters were reduced differently for locomotion and rest (Figure 4). We suggest evaluating the results for locomotion and rest using the same chi-square value of 3 for both behavioral states (at least in controls).

Thank you for this prompt, this is an important point that we tried to resolve during our analysis. We used the reduced chi-square () to evaluate model fits within locomotion and rest condition independently. As defined in equation 12, reduced chi-square is inversely proportional to the standard error of the data which is higher in the rest dataset. As a consequence, setting the same threshold across conditions would not correspond to an equivalent goodness-of-fit criterion, and would impose a disproportionately strict constraint on the condition with lower variability, where deviations between model and data are more heavily penalized. For this reason, we used condition specific thresholds to ensure comparable fit quality relative to the noise level in each condition. In addition, to enable direct comparison across conditions independent of their noise levels, we used the RMSE as a complementary metric.

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Author response:

The following is the authors’ response to the original reviews

Thank you very much for the positive and constructive feedback on our manuscript. We have revised the manuscript accordingly and have added a substantial number of additional experiments and have extended the data.

Questions of the reviewers were focused mostly on mechanical insight into organoid formation, touching following aspects of lens organoid formation presented in the manuscript:

- Cellular arrangements/re-arrangements during the process of lens formation including potential contribution of differential adhesion-mediated cell sorting to the cellular arrangement in the organoid and characterization of individual contributions of lens- and retina- committed progenitors to this process.

- Activity of BMP and FGF signaling pathways during organoid formation, namely identification of tissue responding to the signaling withing forming organoids.

- Contribution of externally supplemented Matrigel to the differentiation process and cellular arrangements in ocular organoids. 

To address those points in detail we included additional experiments that are now presented in revised version of the manuscript, namely in revised Figure 2-figure supplement 1 (addressing contribution of Matrigel); new Figure 4-supplement 1/Video S5 (addressing contribution of differential adhesion-mediated cell sorting); revised Figure 4/Video S6/Video S7 (addressing contribution of lens-committed progenitors); revised Figure 6 (addressing BMP and FGF signaling pathway activities).

Reviewer #1 (Evidence, reproducibility and clarity):

Summary

The authors focused on medaka retinal organoids to investigate the mechanism underlying the eye cup morphogenesis. The authors succeeded to induce lens formation in fish retinal organoids using 3D suspension culture with minimal growth factor-containing media containing the Hepes. At day 1, Rx3:H2B-GFP＋ cells appear in the surface region of organoids. At day 1.5, Prox1+cells appear in the interface area between the organoid surface and the core of central cell mass, which develops a spherical-shaped lens later. So, Prox1+ cells covers the surface of the internal lens cell core. At day 2, foxe3:GFP+ cells appear in the Prox1+ area, where early lens fiber marker, LFC, starts to be expressed. In addition, foxe3:GFP+ cells show EdU+ incorporation, indicating that foxe3:GFP+ cells have lens epithelial cell-characters. At day 4, cry:EGFP+ cells differentiate inside the spherical lens core, whose the surface area consists of LFC+ and Prox1+ cells. Furthermore, at day 4, the lens core moves towards the surface of retinal organoids to form an eye-cup like structure, although this morphogenesis "inside out" mechanism is different from in vivo cellular "outside -in" mechanism of eye cup formation. From these data, the authors conclude that optic cup formation, especially the positioning of the lens, is established in retinal organoids though the different mechanism of in vivo morphogenesis.

Overall, manuscript presentation is nice. However, there are still obscure points to understand background mechanism. My comments are shown below.

Major comments

(1) At the initial stage of retinal organoid morphogenesis, a spherical lens is centrally positioned inside the retinal organoids, by covering a central lens core by the outer cell sheet of retinal precursor cells. I wonder if the formation of this structure may be understood by differential cell adhesive activity or mechanical tension between lens core cells and retinal cell sheet, just like the previous study done by Heisenberg lab on the spatial patterning of endoderm, mesoderm and ectoderm (Nat. Cell Biol. 10, 429 - 436 (2008)). Lens core cells may be integrated inside retinal cell mass by cell sorting through the direct interaction between retinal cells and lens cells, or between lens cells and the culture media. After day 1, it is also possible to understand that lens core moves towards the surface of retinal organoids, if adhesive/tensile force states of lens core cells may be change by secretion of extracellular matrix. I wonder if the authors measure physical property, adhesive activity and solidness, of retinal precursor cells and lens core cells. If retinal organoids at day 1 are dissociated and cultured again, do they show the same patterning of internal lens core covering by the outer retinal cell sheet?

The question, whether different adhesive activity is involved in cell sorting and lens formation is indeed very intriguing.

To address this point, we included additional experiments in the revised manuscript. As proposed by the reviewer, we performed dissociation and re-aggregation experiments of day one organoids at the timepoint, when retinal cell fate is already established and first cells with early lens fate (Foxe3::GFP positive) start appearing (see new Figure 4-figure supplement 1).

After dissociation we followed Foxe3::GFP cells over time and observed that initially equally dispersed GFP⁺ lens-committed cells gradually sort and establish contact with other GFP⁺ cells, ultimately resulting in the formation of a central GFP⁺ sphere within a retinal neuroepithelium (AcTub⁺) localized on the surface of the organoid (see new Figure 4-figure supplement 1e and new Video S5). This data show that differential adhesive properties of lens/retinal precursor cells can enable the formation of a spherical lens in the center of the organoid. This is now clearly stated in the revised version of the manuscript. 

(2) Optic cup is evaginated from the lateral wall of neuroepithelium of the diencephalon. In zebrafish, cell movement occurs from the pigment epithelium to the neural retina during eye morphogenesis in an FGF-dependent manner. How the medaka optic cup morphogenesis is coordinated? I also wonder if the authors conduct the tracking of cell migration during optic cup morphogenesis to reveal how cell migration and cell division are regulated in lens of the Medaka retinal organoids. It is also interesting to examine how retinal cell movement is coordinated during Medaka retinal organoids.

Looking into the detail of how optic cup-looking tissue arrangement of ocular organoids is achieved on cellular level is of course interesting. Our previous study showed that optic vesicles of medaka retinal organoids do not form optic cups (for details please see Zilova et al., 2021, eLife). We provide evidence that the formation of cup-looking structure of the ocular organoids presented here is mediated by the following processes: establishment of retina and lens domains at specific regions of the organoid – retina on the surface and lens in the center (see Figure 3-figure supplement 1d and Figure 3e, and Figure 4). Further, the dislocation of the centrally formed lens towards the organoid periphery results in the opening of the retina layer, moving the lens to the periphery while retinal cells stay static. We propose that the “cup-like” shape is acquired by an extrusion-like process of the lens from the center of the organoid.

To address the cellular mechanisms involved in this process, we included additional experiments and followed the movements of retinal and lens cells (see new Figure 4c and 4d, new Videos S6, S7 and S8). Retinal cells (tracked as nuclei of the Rx3::H2B-GFP transgenic line) established in the periphery display repeated short distance movements restricted to the retinal epithelium. These movements are characteristic for interkinetic nuclear migration as found in the developing retina. In contrast, Foxe3::GFP lens progenitor cells performed long distance movements from the center to the periphery of the organoid. This movement was accompanied by profound cell shape changes of lens progenitor cells, suggesting an active movement of lens cells to the organoid periphery. These movements are shown in new/extended figures and in new supplementary videos (new Figure 4c and 4d, new Videos S6, S7 and S8) in the revised version of the manuscript.

(3) The authors showed that blockade of FGF signaling affects lens fiber differentiation in day 1-2, whereas lens formation seems to be intact in the presence of FGF receptor inhibitor in day 0-1. I suggest the authors to examine which tissue is a target of FGF signaling in retinal organoids, using markers such as pea3, which is a downstream target of ERK branch of FGF signaling. Since FGF signaling promotes cell proliferation, is the lens core size normal in SU5402-treated organoids from day 0 to day 1?

Assessing the activity of FGF signaling (cross-reference to Reviewer #3) in the organoids is an important point that we have taken care of and included in the revised manuscript.

To address this point, we assessed which tissue/part of the organoid is responding to FGF signaling. To do so we analyzed the presence of phosphorylated ERK (pERK1/2) as FGF signaling target in ocular organoids from day 1 to day 2. At day 1, only low levels of FGF signaling activity were detectable in presumptive retinal or/and lens tissue (see revised Figure 6b). Only half a day later, a significant increase in FGF activity was observed specifically in the central region of the organoids (lens progenitor domain) (at day 1.5), prior to the onset of differentiation of lens fiber cells. This, together with inability of lens progenitor cells to differentiate to lens fiber cells in the presence of FGF inhibitor SU5402 provided during this critical period (day 1 to day 2) demonstrates that FGF signaling activity localized in the lens progenitor cells is required for lens fiber differentiation.

By day 2, FGF activity was detected in both lens and retinal tissue of the organoid. Similar patterns of FGF activity were observed in embryos at 2 days post fertilization (see revised Figure 6b).

The treatment with the FGF signaling inhibitor SU5402 from day 0 to day 1 did have no impact on the core size of organoid the dimension of which were fully comparable to the control (please see Figure 6d).

(4) Fig. 3f and 3g indicate that there is some cell population located between foxe3:GFP+ cells and rx2:H2B-RFP+ cells. What kind of cell-type is occupied in the interface area between foxe3:GFP+ cells and rx2:H2B-RFP+ cells?

That is for sure an interesting question. We are aware of this population of cells. We currently do not have data that clarify the fate of those cells with the required certainty. Rather than speculating, we are currently following up on that question by scRNA sequencing, however we see that beyond the scope of the current manuscript.

(5) Fig. 5e indicates the depth of Rx3 expression at day 1. Is the depth the thickness of Rx3 expressing cell sheet, which covers the central lens core in the organoids? If so, I wonder if total cell number of Rx3 expressing cell sheet may be different in each seeded-cell number, because thickness is the same across each seeded-cell number, but the surface area size may be different depending on underneath the lens core size. Please clarify this point.

The referee is right, figure 5e indicates the thickness of the cell sheet expressing Rx3 positioned at the surface of the organoid. Indeed, the number of Rx3-expressing cells (and lens cells) scales with the size of the organoid as stated in the submitted manuscript. We have taken care to remove ambiguities related to that point in the revised version of the manuscript.

(6) Noggin application inhibits lens formation at day 0-1. BMP signaling regulates formation of lens placode and olfactory placode at the early stage of development. It is interesting to examine whether Noggin-treated organoid expands olfactory placode area. Please check forebrain territory markers.

What tissue differentiates at the expense of the lens in BMP inhibitor-treated organoids is of course an intriguing question.

To address this point, we labeled Noggin treated organoids at day 2 and day 3 with forebrain and olfactory placode markers. We could identify an increase in the domains expressing Lhx2, HuC/D and Otx2 in Noggin-treated organoids, showing a shift of the preferential differentiation of the neurons of anterior forebrain identity (see attached figure for reviewer). However, the available markers Lhx2, HuC/D and Otx2 found in the olfactory placode are in addition also co-expressed in further neuronal cell types of the anterior forebrain. While the speculation is tempting, the shift in expression does not allow to conclusively state the expansion of the olfactory placode.

Author response image 1.

Expression of forebrain and olfactory placode markers.

I have no minor comments

Referees cross-commenting

I agree that all reviewers have similar suggestions, which are reasonable and provided the same estimated time for revision.

Reviewer #1 (Significance):

Strength:

This study is unique. The authors examined eye cup morphogenesis using fish retinal organoids. Eye cup normally consists of the lens, the neural retina, pigment epithelium and optic stalk. However, retinal organoids seem to be simple and consists of two cell types, lens and retina. Interestingly, a similar optic cup-like structure is achieved in both cases; however, underlying mechanism is different. It is interesting to investigate how eye morphogenesis is regulated in retinal organoids,under the unconstrained embryo-free environment.

Limitation:

Description is OK, but analysis is not much profound. It is necessary to apply a bit more molecular and cellular level analysis, such as tracking of cell movement and visualization of FGF signaling in organoid tissues.

Advancement:

The current study is descriptive. Need some conceptual advance, which impact cell biology field or medical science.

Audience:

The target audience of current study are still within ophthalmology and neuroscience community people, maybe translational/clinical rather than basic biology. To beyond specific fields, need to formulate a general principle for cell and developmental biology.

Reviewer #2 (Evidence, reproducibility and clarity):

In this study from Stahl et al., the authors demonstrate that medaka pluripotent embryonic cells can self-organise into eye organoids containing both retina and lens tissues. While these organoids can self-organize into an eye structure that resembles the vertebrate eye, they are built from a fundamentally different morphogenetic process - an "inside-out" mechanism where the lens forms centrally and moves outward, rather than the normal "outside-in" embryonic process. This is a very interesting discovery, both for our understanding of developmental biology and the potential for tissue engineering applications. The study would benefit from some additional experiments and a few clarifications.

The authors suggest that the lens cells are the ones that move from the central to a more superficial position. Is this an active movement of lens cells or just the passive consequence of the retina cells acquiring a cup shape? Are the retina cells migrating behind the lens or the lens cells pushing outwards? High-resolution imaging of organoid cup formation, tracking retina cells in combination with membrane labeling of all cells would help elucidate the morphogenetic processes occurring in the organoids. Membrane labeling would also be useful as Prox1 positive lens cells appear elongated in embryos while in the organoids, cell shapes seem less organised, less compact and not elongated (for example as shown in Fig 3f,g).

Looking into the detail of how the optic cup-like arrangement of ocular organoids is achieved on the cellular level is indeed highly interesting. In the revised manuscript we now provide evidence that the formation of cup-like structure of the ocular organoids presented here is mediated by the following processes: establishment of retina and lens domains at distinct regions of the organoid – retina on the surface and lens in the center (see Figure 3-figure supplement 1d and Figure 3e, and Figure 4). Further, the dislocation of the centrally formed lens towards the organoid periphery results in the opening of the retina layer, moving the lens to the periphery while retinal cells stay static. We propose that the cup-like shape is acquired by an extrusion process of the lens from the center of the organoid.

To address cellular mechanisms involved in this process, we included additional experiments and followed the movements of retinal and lens cells (see new Figure 4c and 4e, new Videos S6, S7 and S8).

Retinal cells (tracked as nuclei of the Rx3::H2B-GFP transgenic line) display repeated short distance movements within the retinal epithelium. These movements are characteristic for interkinetic nuclear migration as found in the developing retina.

In contrast, Foxe3::GFP lens progenitor cells performed long distance movements from the center to the periphery of the organoid. This movement was accompanied by profound cell shape changes of lens progenitor cells, suggesting an active movement of lens cells to the organoid periphery.

These movements are shown in new/extended figures and in new supplementary videos (new Figure 4c and 4e, new Videos S6, S7 and S8) in the revised version of the manuscript.

The organoids could be a useful tool to address how cell fate is linked to cell shape acquisition. In the forming organoids, retinal tissue initially forms on the outside, while non-retinal tissue is located in the centre; this central tissue later expresses lens markers. Do the authors have any insights into why fate acquisition occurs in this pattern? Is there a difference in proliferation rates between the centrally located cells and the external ones? Could it be that highly proliferative cells give rise to neural retina (NR), while lower proliferating cells become lens?

We agree with the reviewer that this is a highly interesting question and in the revised manuscript we followed the advice and dedicated a part of the discussion to this topic. We believe that the arrangement is due to the induction of central lens fates by signal emanating from the retinal epithelium and discuss the role of the diffusion limit and the potential contribution of BMB and FGF signaling to this arrangement. Additional experiments addressing the target tissues of FGF and BMP signaling in the organoid have been provided in response to Reviewer #1. Interfering with FGF signaling that is essential for lens fiber cell differentiation interestingly did not impact on the lens size arguing against an immediate proliferative effect. Although the analysis of the respective proliferation rates at the surface or in the central region of the organoid might show some differences, we do not have any indications, that the proliferation rate itself would be instructive or superior to the cell fate decisions.

What happens in organoids that do not form lenses? Do these organoids still generate foxe3 positive cells that fail to develop into a proper lens structure? And in the absence of lens formation, does the retina still acquire a cup shape?

Lens formation is primarily dependent on the acquisition/specification of Foxe3-expressing lens placode progenitors. In the absence of Foxe3-expression, a lens does not develop. Once Foxe3-expressing progenitors are established, a lens is formed in unperturbed conditions (measured by the presence of expression of crystallin proteins). Organoids that do not have a lens, do not contain Foxe3-expressing cells.

In the absence of a lens, the organoid is composed of retinal neuroepithelium, that does not form an optic cup like shape (for details of such phenotypes please see Zilova et al., 2021, eLIFE). We took care to state that clearly in the revised manuscript.

The author suggest that lens formation occurs even in the absence of Matrigel. Is the process slower in these conditions? Are the resulting organoids smaller? While there are indeed some LFC expressing cells by day2, these cells are not very well organised and the pattern of expression seems dotty. Moreover, LFC staining seems to localise posterior to the LFC negative, lens-like structure (e.g. Fig.S1 3o'clock). How do these organoids develop beyond day 4? Do they maintain their structural integrity at later stages?

The role of HEPES in promoting organoid formation is intriguing. Do the authors have any insights into why it is important in this context? Have the authors tried other culture conditions and does culture condition influence the morphogenetic pathways occurring within the organoids?

We thank the reviewer for pointing this out. In the revised manuscript we made sure to be sufficiently clear in the wording and description of our observation. Indeed, Matrigel is not required for the acquisition of lens fate, which can be demonstrated by the expression of lensspecific markers. However, the presence of Matrigel has a profound impact on structural aspects of organoid formation. Matrigel is essential for organization of retinal-committed cells to form a retinal epithelium (Zilova et al., 2021, eLife). The absence of the structure of the retinal epithelium indeed negatively impacts on the cellular organization and the overall lens structure.

To clarify the contribution of the Matrigel to the organoid organization, we performed additional experiments (see revised Figure 2-figure supplement 1c-f). As mentioned above, the absence of Matrigel impacts on the organization and thickness of retinal neuroepithelium (Rx2⁺, Figure 2-figure supplement 1c). However, measurement of the lens in organoids at day 2 and day 5 showed that size of the lens is not impacted upon in the absence of Matrigel (Figure 3-figure supplement 1d-e). Additionally, taking advantage of the Foxe3::GFP lens reporter line, we measured the onset of lens-specific gene expression in organoids with and without Matrigel. In both conditions, with and without Matrigel supplementation, Foxe3::GFP expression was initiated at 25 hours post aggregation (see revised Figure 4b).

The role of the HEPES in lens formation is indeed very intriguing and currently under investigation. HEPES is mainly used to regulate the pH of the culture media which on its own might have an impact on multiple cellular processes. It will require a significant time investment to address the potential HEPES triggered molecular mechanisms impacting on lens formation (cross reference with Reviewer #3), which goes beyond the scope of the current manuscript.

Referees cross-commenting

Pleased to see that all the other reviewers are positive about the study and raise similar concerns and comments

Reviewer #2 (Significance):

This is a very interesting paper, and it will be important to determine whether this alternative morphogenetic process is specific to medaka or if similar developmental routes can be recapitulated in organoid cultures from other vertebrate species.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

The manuscript by Stahl and colleagues reports an approach to generate ocular organoids composed of retinal and lens structures, derived from Medaka blastula cells. The authors present a comprehensive characterisation of the timeline followed by lens and retinal progenitors, showing these have distinct origins, and that they recapitulate the expression of differentiation markers found in vivo. Despite this molecular recapitulation, morphogenesis is strikingly different, with lens progenitors arising at the centre of the organoid, and subsequently translocating to the outside.

Comments:

The manuscript presents a beautiful set of high quality images showing expression of lens differentiation markers over time in the organoids. The set of experiments is very robust, with high numbers of organoids analysed and reproducible data. The mechanism by which lens specification is promoted in these organoids is, however, poorly analysed, and the reader does not get a clear understanding of what is different in these experiments, as compared to previous attempts, to support lens differentiation. There is a mention to HEPES supplementation, but no further analysis is provided, and the fact that the process is independent of ECM contradicts, as the authors point out, previous reports. The manuscript would benefit from a more detailed analysis of the mechanisms that lead to lens differentiation in this setting.

We followed the reviewer’s advice and have included a systematic analysis of the contribution of ECM (Matrigel) to the process of lens formation. In the revised manuscript we made sure to be sufficiently clear in the wording and description of our observation. Indeed, Matrigel is not required for the acquisition of lens fate, which can be demonstrated by the expression of lensspecific markers. However, the presence of Matrigel has a profound impact on structural aspects of organoid formation. Matrigel is essential for organization of retinal-committed cells to form a retinal epithelium (Zilova et al., 2021, eLIFE). The absence of the structure of the retinal epithelium in turn indeed negatively impacts on the cellular organization and the overall lens structure.

To clarify the contribution of the Matrigel to the organoid organization, we performed additional experiments (see revised Figure 2-figure supplement 1c-f). As mentioned above, the absence of Matrigel impacts on the organization and thickness of retinal neuroepithelium (Rx2⁺, Figure 2-figure supplement 1c). However, measurement of the lens in organoids at day 2 and day 5 showed that size of the lens is not impacted upon by the absence of Matrigel (Figure 3-figure supplement 1d-e).

Additionally, taking advantage of the Foxe3::GFP lens reporter line, we measured the onset of lens-specific gene expression in organoids with and without Matrigel. In both conditions (with and without Matrigel supplementation), Foxe3::GFP expression was initiated at 25 hours post aggregation (see revised Figure 4b).

The role of the HEPES in lens formation is indeed intriguing and currently under investigation. HEPES is mainly used to adjust the pH of the culture media, which, on its own might have an impact on multiple cellular processes. It will require a significant time investment to address the potential HEPES triggered molecular mechanisms impacting on lens formation (cross reference with Reviewer #3), which clearly goes beyond the scope of the current manuscript.

The markers analysed to show onset of lens differentiation in the organoids seem to start being expressed, in vivo, when the lens placode starts invaginating. An analysis of earlier stages is not presented. This would be very informative, allowing to determine whether progenitors differentiate as placode and neuroepithelium first, to subsequently continue differentiating into lens and retina, respectively. Could early placodal and anterior neural plate markers be analysed in the organoids? This would provide a more complete sequence of lens vs retina differentiation in this model.

We have taken care to show according stages in embryo and organoid side by side. We provide additional data to highlight the expression of Rx3::H2B-GFP (retina) and Foxe3::GFP (lens and lens placode) markers in earlier developmental stages. For the presumptive eye field within the region of the anterior neural plate (S16, late gastrula) Rx3 represents one of the earliest markers (see revised Figure 3-figure supplement 1). Already before an apparent lens placode is formed (see revised Figure 3d) Foxe3::GFP expression is detected within the presumptive lens ectoderm, demonstrating that Foxe3 is ideally suited as an early marker for placodal progenitors in medaka. The onset of Rx3 and Foxe3-driven reporters is clearly early enough to support the claim about the separate origin of the lens (placodal) and retinal (anterior neuroectoderm) tissues within the ocular organoids now represented in the revised figures.

The analysis of BMP and Fgf requirement for lens formation and differentiation is suggestive, but the source of these signals is not resolved or mentioned in the manuscript. Are BMP4 and Fgf8 expressed by the organoids? Where are they coming from?

Assessing the activity of BMP and FGF signaling (cross-reference to Reviewer #1) in the organoids is an important point that we have taken care of and included in the revised manuscript.

To address this point, we assessed which tissue/part of the organoid is responding to BMP and FGF signaling. To do so we analyzed the presence of phosphorylated SMAD1/5/8 (pSMAD1/5/8) and phosphorylated ERK (pERK1/2) as BMP and FGF signaling target in ocular organoids from day 1 to day 2. BMP signaling activity was detected in the center (region of establishment of lens-committed progenitors (Figure 3e)) of the organoid at day 1 (see revised Figure 6a). At day 1, only low levels of FGF signaling activity were detectable in presumptive retinal or/and lens tissue (see revised Figure S6b). Only half a day later, a significant increase in FGF activity was observed specifically in the central region of the organoids (lens progenitor domain, at day 1.5), prior to the onset of differentiation of lens fiber cells. This, together with inability of lens progenitor cells to differentiate to lens fiber cells in the presence of FGF inhibitor SU5402 provided during this critical period (day 1 to day 2) demonstrates that FGF signaling activity localized in the lens progenitor cells is required for lens fiber differentiation.

By day 2, FGF activity was detected in both lens and retinal tissue of the organoid. Similar patterns of FGF activity were observed in embryos at 2 days post fertilization (see revised Figure S6b).

The treatment with the FGF signaling inhibitor SU5402 from day 0 to day 1 did have no impact on the core size of organoid the dimension of which were fully comparable to the control (please see Figure 6b).

Related to the presence of the corresponding ligands we can state that they are indeed expressed in the organoids at the matching stages based on RNA seq and RT-PCR analyses, however we could not find them specifically localized. This may be due to a widespread, ubiquitous expression or may simply relate to technical problems.

While we can state with confidence that the ligands are present at the relevant time points and trigger the downstream pathways in a localized manner, the question whether the response is due to a localized signal or localized competence remains to be addressed.

The fact that the lens becomes specified in the centre of the organoid is striking, but it is for me difficult to visualise how it ends up being extruded from the organoid. Did the authors try to follow this process in movies? I understand that this may be technically challenging, but it would certainly help to understand the process that leads to the final organisation of retinal and lens tissues in the organoid. There is no discussion of why the morphogenetic mechanism is so different from the in vivo situation. The manuscript would benefit from explicitly discussing this.

Following the shift of the lens in vivo is indeed very relevant suggestion and we have taken care to address this in the revised manuscript.

To clarify this process, we included additional experiments and followed the movements of lens cells (see new Figures 4c, 4d and 4e, new Videos S6 and S7). Foxe3::GFP lens progenitor cells were found to actively move over long distances from center to the organoid periphery. This movement was accompanied by profound cell shape changes of lens progenitor cells with the active extension of lamellipodia and filopodia strongly arguing for an active movement of lens cells to the organoid periphery (cross-reference with Reviewer #1 and Reviewer #2).

Referees cross-commenting

We all seem to have similar comments and concerns. I think overall the suggestions are feasible and realistic for the timeframe provided.

Reviewer #3 (Significance):

This study describes a reproducible approach to differentiate ocular organoids composed of lens and retinal tissues. The characterisation of lens differentiation in this model is very detailed, and despite the morphogenetic differences, the molecular mechanisms show many similarities to the in vivo situation. The manuscript however does not highlight, in my opinion, why this model may be relevant. Clearly articulating this relevance, particularly in the discussion, will enhance the study and provide more clarity to the readers regarding the significance of the study for the field of organoid research, ocular research and regenerative studies.

Author response:

The following is the authors’ response to the original reviews

We thank the reviewers for their time and consideration of the manuscript. We have added new data to Figure 5 (Figure 5a) to address concerns regarding the conservation of the Hsp70 phosphorylation in yeast. Additionally, we have changed the title of the manuscript to “Hsp70 is phosphorylated in a conserved response to DNA damage and contributes to cell cycle control” to more accurately represent the conclusions we draw.

Public Reviews:

Reviewer #1 (Public review):

The strength of evidence of the mechanistic and "conserved checkpoint" claims that this site is directly activated by DNA damage is inadequate and fundamentally incorrect.

We respectfully disagree with the reviewer’s characterization of our conclusions. Our data demonstrate that DNA damage induces this phosphorylation in a cell-cycle–dependent manner. We do not claim to have defined the direct kinase or full mechanistic pathway; rather, we establish that site activation is damage-responsive and functionally linked to cell-cycle regulation. Consistent with this, phospho-mutants in yeast exhibit clear cell-cycle defects, supporting a conserved functional role. We address each of the reviewer’s specific concerns below.

Specific comments:

(1) Activation of T495:

The author's premise for the site being activated by DNA damage is Albuquerque et al, where PTMs on MMS treated yeast are analyzed. T492 (the yeast equivalent of human T495) is observed as phosphorylated. However, the authors fail to note that there is no untreated sample analysis in this study, and it is likely that T492 phosphorylation is also present in untreated cells. This is also backed up by later evidence from the same lab (Smolka et al), where they do not identify T492 as being dependent on Mec1/Tel/Rad53 kinases.

We agree with this assessment of the Albuquerque study. Accordingly, we used their data to generate the hypothesis that this site is phosphorylated, and we took it upon ourselves to more rigorously demonstrate phosphorylation with appropriate controls. The validated antibody that we had previously generated[1] to track pHsp70 was the enabling technology to directly track this phosphorylation event. We now directly show phosphorylation of this site (Figure 5a, lines 276-284). Of note, as Reviewer 1 suggested, there is a smaller amount of pHsp70 in the untreated cells, which corresponds with findings from Holt et al 2009 [2]. This could reflect a baseline role of Hsp70 phosphorylation for normal growth that is accentuated upon MMS insult.

(2) The kinase(s) directly responsible for T495 phosphorylation are not identified. Instead, the authors show that knockdown or pharmacological inhibition of DNA-PKcs, ATM, Chk2, and CK1 attenuate pHsp70.

We agree with reviewer 1 that identifying the direct kinase would be an exciting finding, and we believe our manuscript will provide the foundation for future studies to address these questions. While these findings will be impactful, we do not believe their lack detracts from the observations we have made.

(3) ATM siRNA knockdown has no effect, while ATM inhibitors do, which the authors acknowledge but do not resolve. This discrepancy raises concerns about off-target drug effects.

We agree with reviewer 1 that off-target drug effects are always a concern when employing pharmacological inhibitors. To that end, we tested structurally distinct inhibitors of ATM (Figure 3b) to decrease the likelihood of the same off target effect. While complementing this with a genetic knockdown would be ideal, the discrepancies between pharmacological and genetic inhibition of ATM have been well reported (lines 214-216).[3,4] Parallel discrepancies in other kinases have been mechanistically explored by other groups.[5] The preponderance of pharmacological evidence in conjunction with RNAi suggests the most likely interpretation of our data is that ATM is involved in signaling upstream of Hsp70 phosphorylation. Thus, our data compel future work to use more sophisticated genetic methods to more specifically determine how ATM connects with pHsc70.

(4) No in vitro kinase assays, motif analysis, or phosphosite mapping confirming these kinases as direct T495 kinases are presented. Thus, the proposed signaling cascade remains speculative.

We agree that we should carefully circumscribe our conclusions about the potential signaling cascade. To communicate our conclusions more clearly, we rewrote lines 223-226 to highlight that our findings implicate these kinases in upstream signaling rather than direct phosphorylation of Hsp70.

(5) Smolka and many other labs characterized DDR sites as SQ/TQ motifs, and T492 doesn't fit that motif.

We agree, and our response to comment 4 addresses this point. Briefly, we do not claim that Hsp70 is a direct target for DDR. Notably, the SQ/TQ motifs mentioned specifically pertain to ATM and DNA-PK[6], though we would like to note several studies have demonstrated DNA-PK phosphorylation outside of these motifs.[7] Chk2 and CK1 do not prefer SQ/TQ motifs[9]. Additionally, Chk2 is known to phosphorylate non-consensus sequences as well[10].

(6) No genetic tests in yeast (e.g., BER mutants) are used to connect Ssa1 T492 phosphorylation to BER in that system, despite the strong BER-centric model.

We agree that it would be interesting to study BER mutants in yeast, and we believe this will be an exciting prospect for future studies to better establish the signaling cascade. We have included a Western blot (Figure 5a) showing that MMS treatment causes increased Hsp70 phosphorylation in yeast. MMS damage is repaired through BER in S. cerevisiae,[11] and the pathway itself is highly conserved.[12] Our experiments demonstrate that the phosphorylation of Hsp70 occurs as a conserved response to alkylation damage, which is the major conclusion of our paper.

(7) Overexpression of MPG gives only a modest increase in pHsp70, while APE1 overexpression has no effect, and Polβ overexpression does not decrease pHsp70. These mixed results weaken the central claim that Hsp70 phosphorylation is a tuned sensor of BER burden.

We appreciate this incisive question. Though not immediately intuitive, we do not believe these results are necessarily ‘mixed’. The lack of APE1 over-expression having an effect could be attributed to APE1 activity being necessary for the phosphorylation, but not rate-limiting. Regarding Polβ, it is important to note that not its binding, but rather its dRP lyase activity is rate-limiting in base excision repair.[13] As such, if binding sites are already saturated or near saturated, but the lyase activity remains slow, we may not observe a decrease in BER intermediates. While we do claim that phosphorylation of Hsp70 is triggered by BER intermediates (lines 193-194), we do not claim that pHsp70 is a tuned sensor of BER burden.

(8) A major concern is that pHsp70 is only convincingly detected after very high, prolonged MMS (10 mM, 5 h) or 0.5 mM arsenite treatments. Other DNA-damaging agents (bleomycin, camptothecin, hydroxyurea) that robustly activate DDR kinases do not induce pHsp70. This suggests to me that the authors are observing a side effect of proteotoxic stress. This is likely (see Paull et al, PMID: 34116476).

Our data indicate that pHsp70 specifically occurs downstream of base excision repair. Therefore, it is not surprising that drugs that do not activate BER (bleomycin, camptothecin, hydroxyurea) do not elicit the same response. While pHsp70 may arise due to DSBs generated through BER, the fact we do not see phosphorylation after bleomycin treatment could be explained by the cell-cycle dependencies we report (Figure 4e). It is also important to note that MMS-induced pHsp70 occurs primarily in the nucleus, and Western blots of whole cell lysate will contain large amounts of cytosolic Hsp70 that could dilute the signal. Indeed, in our nuclear extraction (Figure 4d), we see faint pHsp70 signal as soon as 1 h after treatment, though it increases in robustness as the time-course progresses. These data are both concordant with a model in which high BER-induced lesion burden in mitosis leads to Hsp70 phosphorylation in late M/G1.

We would like to add that, in the review article cited by Reviewer 1, the authors specifically cite studies implicating a loss-of-function in DDR pathways leading to increased proteotoxic stress (e.g. ATM deficient cells producing higher levels of aggregated proteins compared to WT). However, we find that inhibition of DDR kinases decreases, rather than increases Hsp70 phosphorylation. We thus believe that DNA damage rather than proteotoxic stress is the parsimonious cause of Hsp70 phosphorylation.

(9) A recent study in Nature Communications (Omkar et al., 2025) demonstrates rapid phosphorylation of yeast T492 in a pkc1-dependent manner, diminishing the impact of these findings.

We were excited to see this paper when it was published 3 months after we posted a preprint on bioRxiv, which was released three weeks after our submission to eLife. Rather than diminishing the impact of this paper, we believe that independent lines of evidence from different groups mutually reinforces the impact of the work. We have added a sentence to say that during the review of our work, this group independently observed this phosphorylation event in response to a different stress (lines 421-423). We believe in celebrating the scientific process arriving at consistent results, and the editorial policies of eLife reinforce that philosophy by offering ‘scoop protection.’

We would also like to highlight several differences between the scope of our papers. The phosphorylation reported by Omkar et al. appears highly constrained to yeast as part of the Cell Wall Integrity pathway, whereas ours occurs as a more highly conserved response. Additionally, our paper provides additional biochemical insight into the consequences of this phosphorylation, which is lacking in Omkar et al. If anything, this paper highlights the important regulatory capacity of this residue on Hsp70, and suggests it may serve multiple functions in the cell.

(2) Downstream Effects of T492/T495:

(10) The manuscript's central conceptual advance is that pHsp70 is a cell-cycle-regulated brake on G1/S. Yet in mammalian cells, the authors show only that pHsp70 appears late, after cells have traversed mitosis, and that blocking CDK1 (G2/M) prevents its accumulation.

We would like to clarify the central contribution of this study. Prior work identified this phosphorylation in yeast, but its existence and conservation in human cells had not been established. A primary advance of our study is demonstrating that this site is phosphorylated in mammalian cells and that its accumulation is cell-cycle regulated — coinciding with late M/G1.

We further show that phosphorylation depends on cell-cycle progression, as CDK1 inhibition prevents its accumulation. While these data establish regulation, we agree that they do not by themselves define causality in mammalian cells. To address functional consequences, we leveraged the genetic tractability of S. cerevisiae. Phosphomimetic Ssa1 T492E increases the proportion of G1 cells in the absence of MMS and enforces a stronger G1 arrest following MMS treatment. Together, these findings support a conserved, cell-cycle–linked role for this phosphorylation and provide a foundation for future mechanistic work in mammalian systems.

(11) There is no functional test in human cells: no knockdown/rescue experiments with T495A or T495E, no cell-cycle profiling upon altering Hsp70 phosphorylation state, and no demonstration that pHsp70 actually causes any delay in S-phase entry, rather than simply correlating with late damage responses. The strong conclusion that pT495 "stalls cell cycle progression" (e.g., Figure 6 model) is therefore not supported in the human system.

We agree that we did not directly test the functional consequences of Hsp70 phosphorylation in human cells. Our intent was not to claim that we have demonstrated causality in the mammalian system, but rather to establish that this conserved phosphorylation exists in human cells and is cell-cycle regulated.

We instead used S. cerevisiae to interrogate this due to its increased genetic tractability. In this system, phosphomimetic mutation increases the proportion of G1 cells under basal conditions and enhances G1 arrest following MMS treatment, mirroring the damage-associated phenotype observed in human cells. These findings support a conserved functional role for this modification, although we agree that direct mechanistic testing in mammalian cells will be important for future work.

While we intended the cartoon model to be a speculative illustration of what may be occurring in order to motivate future studies. We now see how this may lead to confusion, so to improve clarity, we have removed Figure 6 from the manuscript.

(12) All functional conclusions rely on T492A/E point mutants at the endogenous SSA1 locus, usually in an ssa2Δ background, in a family of highly redundant Hsp70s. Without showing that this site is actually modified during their MMS treatments, the assignment of phenotypes to loss of a physiological phospho-switch is premature. The authors need to repeat their studies in an Ssa1-4 background, as in https://pubmed.ncbi.nlm.nih.gov/32205407/.

Thank you for this feedback. We have included a Western blot to Figure 5 (Figure 5a) addressing this comment. Briefly, we show that, in yeast, Hsp70 phosphorylation increases upon MMS treatment and is not detectable in the point-mutants in the ssa2∆ background. The latter data suggest that Ssa3-4 modification is negligible in our system.

(13) The authors infer that T495E "locks" Hsc70 in a pseudo-open state based on reduced J-protein-stimulated ATPase activity, unchanged ATP binding, altered trypsin sensitivity, and retained tau binding. However, there is no direct comparison of phosphorylated vs T495E protein (e.g., via in vitro phosphorylation with LegK4 followed by side-by-side biochemical assays, or structural analysis). Thus, it remains unclear to what extent the glutamate substitution mimics a phosphate at this position.

Previously we did show that phosphorylation impacts the ATPase cycle of Hsp70.[1] In this paper, with the phosphomimetic mutant we see an even greater decrease of activity. This is consistent with incomplete phosphorylation yielded by in vitro phosphorylation with LegK4.[1] Due to this incomplete phosphorylation in vitro, we determined that the phosphomimetic mutant would be more useful for the assays we performed, as they rely on bulk readouts.

(14) No client release kinetics, co-chaperone binding assays, or in vivo chaperone function tests are provided, yet the discussion builds a detailed model of a "pseudo-open" state that simultaneously resembles ATP-bound conformation and allows persistent substrate engagement.

We have shown that the conformational cycle of Hsp70 (T495E) is uncoupled from nucleotide state, and that the overall conformation resembles ATP-bound Hsp70. This is consistent with prior studies on AMPylation of the same residue.[14] Additionally, we demonstrate that substrate engagement is similar between WT and T495E. This is consistent with our previously published work showing increased pHsp70 on polysomes,[1] as well as our observations that the phosphomimetic mutant in yeast exerts a phenotype even in the presence of the compensatory isoform SSA2. This dominant-like phenotype is consistent with those seen in mutations locking Hsp70 in a ‘closed’ conformation.[15] We agree that future studies examining client release kinetics and co-chaperone binding would be useful for future structural studies validating and elaborating on our findings.

Reviewer #2 (Public review):

Weaknesses:

The kinase(s) responsible for the phosphorylation have not been identified (and hence remain inaccessible to experimental i.e., genetic or pharmacological manipulation). The mechanistic links to DNA damage repair and the fitness benefits of this proposed adaptation remain obscure. Of greater concern, the data provided in the paper fail to exclude the trivial possibility that the phosphorylation event described (and characterized through biochemical proxies) is biologically neutral, reflecting nothing more than a bystander event in which kinase(s) activated by application of high concentrations of a powerful alkylating agent (MMS) phosphorylate, at meaninglessly low stoichiometry, an abundant protein (Hsp70) on a surface exposed residue. Failure to exclude this (plausible) scenario is this paper's weakness.

We agree that we have not directly quantified the absolute stoichiometry of Hsp70 phosphorylation. However, several lines of evidence argue against the interpretation that this represents a biologically neutral, bystander modification.

First, our pulse-chase experiment (Figure 4e) shows that, after MMS removal, pHsp70 levels increase as cells progress through the cell cycle. Notably, total Hsp70 levels remain constant. This indicates that the fraction of phosphorylated Hsp70 increases in a regulated, cell-cycle dependent manner, rather than through a bystander event during acute stress.

Second, functional perturbation of the homologous site in yeast produces phenotypic consequences. The phosphomimetic Ssa1(T492E) mutant exhibits reduced growth, increased G1 accumulation, and impaired cell-cycle re-entry following MMS treatment (Figure 5). These phenotypes argue that the modification of this residue is functionally consequential.

While the upstream kinase remains to be identified, the genetic and cell-cycle phenotypes observed upon site perturbation argue that this phosphorylation is functionally consequential.

Reviewer #2 (Recommendations for the authors):

(1) The biochemical characterization of the phosphomimetic mutation (T495E) is thorough, relying on ATPase assays and conformational analysis. Figure 1b demonstrates reduced J-protein-stimulated ATPase activity, and Figure 1d shows an ATP-like proteolysis pattern consistent with an open conformation. As the authors are well aware, Hsp70 chaperones act on their substrates via a dynamic cycle that includes binding, ATP hydrolysis, and conformational shifts. One wonders, therefore, at the relevance of the measurement shown in Figure 1f. While it is highly plausible that the T495E mutation mimics the phosphorylation event (BiP T518E mimics key aspects of AMPylation), the lack of a biochemical characterisation of Hsp70 with pThr495 is an important limitation of this paper. Even if such a preparation cannot be accomplished with the endogenous kinase(s) whose identity remains unknown, a characterisation of LegK4-phosphorylated Hsp70 should suffice.

We agree with Reviewer 2 that the rationale for figure 1f does not logically follow the results of 1b and 1d. Rather, this experiment was motivated by the prior findings that phosphorylation of Hsp70 by L.p. lead to an increase occupancy on polysomes[1] (lines 137-139). We sought to better understand the discrepancy between this finding and our own by assaying the capacity of the T495E mutant to bind substrate.

Reviewer 2 raises a valid point in that phosphomimetic proteins do not necessarily behave the same as truly phosphorylated proteins. Previous work from our lab characterized the ATPase activity and in vitro folding capacity of Hsc70 that had been directly phosphorylated by LegK4[1] (lines 114-115). We were motivated to turn to a phosphomimetic mutant as LegK4 only phosphorylates around half of the Hsc70 present in solution[1] (line 116); this mixture of species makes batch analysis difficult. As we had previously published with the in vitro phosphorylated Hsc70, we didn’t believe it necessary to include along with our future analyses.

(2) As noted, the kinase(s) that phosphorylate T495 remain to be identified and is inaccessible genetically. The phenotypic consequences of impaired pThr495 are therefore assessed by a T495A mutation. This most certainly eliminates phosphorylation at that site however, Figure 5C shows quite clearly that the T/A mutation is not neutral. This is expected, given the role of an H-bond network centered upon the homologous residue in the ADP-bound configuration of Hsp70's. Importantly, the biochemical non-neutrality of the T/A mutation also compromises the interpretation of the associated phenotype, as this cannot be attributed solely to a loss of phosphorylation; it may reflect features of the T/A mutations exposed by MMS, but unrelated to the inability of the residue to undergo regulated phosphorylation.

We appreciate this insightful critique. We agree that the alanine substitution may perturb the local H-bond network, and have added a sentence to our discussion to highlight this caveat (lines 379-381). That being said, our conclusions do not solely rely on the T to A mutant. The phenotypes observed in our phosphomimetic mutant overlap with the TA mutant (increased sensitivity to MMS; defects in cell cycle re-entry after MMS treatment) (Figure 5). While the alanine mutation may not represent a purely ‘loss-of-phosphorylation’ state, our findings do implicate the importance of this residue in cell cycle control after DNA damage.

(3) It thus remains formally possible that pThr495 arises as an irrelevant side reaction due to activation of a kinase (with other relevant substrates).

This dismal interpretation of the data would be dispelled somewhat if the stoichiometry of pThr495 were substantial, whereas very low stoichiometry of phosphorylation should leave one wary of the possibility that the surface-exposed Thr495 of ATP-bound Hsc70 is a physiologically irrelevant bystander target of a kinase activated in DNA-damaged cells.

We have included a Western blot in Figure 5 showing pHsp70 in our yeast samples. Here we can see low abundance of Hsp70 phosphorylation in untreated WT yeast, with a clear increase in MMS treated yeast. Additionally, as mentioned in a previous response, Figure 4e shows the accumulation of pHsp70 in human cells even after MMS removal, indicating it is not simply the byproduct of over-activation of the DNA damage response.

Unfortunately, the study does not quantify the stoichiometry of Hsp70 phosphorylation; detection relies on phospho-specific immunoblotting, leaving open the question of whether this modification occurs at physiologically significant levels. This worry is compounded by Figure 2a,f that suggests that phosphorylation occurs only under high-dose MMS or arsenite, raising concerns about physiological relevance.

We agree that we did not quantify absolute phosphorylation stoichiometry. While a precise measurement would be informative, our conclusions are based on regulated dynamics and functional perturbations rather than magnitude alone. Specifically, our pulse-chase (Figure 4e) shows that total Hsp70 levels remain constant while pHsp70 increases in a cell-cycle dependent manner following MMS removal. This indicates a regulated modification rather than a side-effect of kinase over-activation during acute stress. Additionally, perturbation of the homologous site produces cell-cycle phenotypes (Figure 5) in yeast, supporting functional relevance.

However, as mentioned in responses to Comment 3, our pulse-chase assay in Figure 4e indicates the stoichiometry of pHsp70 increases after MMS removal in a cell-cycle dependent manner. Furthermore, as discussed in response to Reviewer 1 Comment 8, Figure 4d highlights a technical limitation with regards to detection of pHsp70 by Western blotting. Namely, as pHsp70 accumulates in the nucleus, signal appears to be diluted by unmodified Hsp70 in the cytosol when whole-cell lysate is probed, thereby reducing detection capacity. It is therefore possible that less stringent doses do lead to phosphorylation, but due to the experiments being run in asynchronous cells and on whole cell lysate we failed to detect it.

Reviewer #3 (Recommendations for the authors):

Major Comments:

(1) Figure 1e - Which antibody was used to probe this blot?

Thank you for catching this omission. This was stained with Coomassie. We have edited the figure legend to reflect this.

(2) Figure 1c- Do the authors have the data of the WT and T495E with DJA2?

The assay was performed with increasing concentrations of DJA2 for both constructs (from 0 µM to 4 µM) (lines 118-119, Figure 1c).

(3) Figure 2- The labeling of the right side of the immunoblots is missing.

We apologize for the confusion. The labeling is on the left. The lines on the right are intended to demarcate blots that came from the same membrane (for easier comparison of loading controls).

(4) Figure 2d- Does MMS treatment lead to a heat shock response?

We have not directly tested this. However, we do not see the massive upregulation of HSPs that would be expected from a heat shock response.

(5) Figure 4c and e - Total protein level of some of the phospho-proteins is missing.

We used housekeeping proteins as loading control. We do not have antibodies for all the non-phospho proteins. For those we have, blots not included in the publication do not show any marked discrepancies between the non-phospho form and the housekeeping proteins.

(6) Figure S1A- Although the authors suggest that the phosphorylation event is reversible, they have not integrated it into the final model in Figure 6.

In line 403 we postulate that dephosphorylation may permit client release. In the interest of clarity, we have now removed the model figure.

(7) Yeast genotype is missing.

We used W303a yeast (line 612).

(8) It is unclear which phosphatase inhibitor was used in their assay (Figure S1A).

We repeated the experiment with both Halt Phosphatase Inhibitor Cocktail (Thermo Scientific 78440) and Roche PhosStop (Roche 04906837001) (lines 524-525).

(9) Please add this most recent and up-to-date reference (PMID: 40976416) related to your study.

We have now added that reference

(10) Can the authors speculate on whether Hsp70- T495E is expected to primarily reside in the nucleus?

We have no data to indicate whether or not phosphorylation at T495 or a phosphomimetic mutation in this site would directly affect nuclear import or export. In cells expressing the Legionella kinase LegK4, pHsp70 exists in the cytoplasm,[1] indicating the phosphorylation in of itself does not force nuclear localization. We thus imagine that the nuclear localization seen in Figure 4d is more likely due to the location of the kinase rather than as a consequence of the phosphorylation. In an over-expression system or in the case of a genomic mutation, we believe the protein is most likely to exist in both the cytoplasm and in the nucleus, though we did not directly test this.

References

(1) Moss, S. M. et al. A Legionella pneumophila Kinase Phosphorylates the Hsp70 Chaperone Family to Inhibit Eukaryotic Protein Synthesis. Cell Host Microbe 25, 454-462.e6 (2019).

(2) Holt, L. J. et al. Global Analysis of Cdk1 Substrate Phosphorylation Sites Provides Insights into Evolution. Science 325, 1682–1686 (2009).

(3) Choi, S., Gamper, A. M., White, J. S. & Bakkenist, C. J. Inhibition of ATM kinase activity does not phenocopy ATM protein disruption. Cell Cycle 9, 4052–4057 (2010).

(4) Menolfi, D. & Zha, S. ATM, ATR and DNA-PKcs kinases—the lessons from the mouse models: inhibition ≠ deletion. Cell Biosci. 10, 8 (2020).

(5) Weiss, W. A., Taylor, S. S. & Shokat, K. M. Recognizing and exploiting differences between RNAi and small-molecule inhibitors. Nat. Chem. Biol. 3, 739–744 (2007).

(6) Kim, S.-T., Lim, D.-S., Canman, C. E. & Kastan, M. B. Substrate Specificities and Identification of Putative Substrates of ATM Kinase Family Members*. J. Biol. Chem. 274, 37538–37543 (1999).

(7) Jette, N. & Lees-Miller, S. P. The DNA-dependent protein kinase: A multifunctional protein kinase with roles in DNA double strand break repair and mitosis. Prog. Biophys. Mol. Biol. 117, 194–205 (2015).

(8) O’Neill, T. et al. Determination of Substrate Motifs for Human Chk1 and hCds1/Chk2 by the Oriented Peptide Library Approach*. J. Biol. Chem. 277, 16102–16115 (2002).

(9) Fulcher, L. J. & Sapkota, G. P. Functions and regulation of the serine/threonine protein kinase CK1 family: moving beyond promiscuity. Biochem. J. 477, 4603–4621 (2020).

(10) Craig, A. et al. Allosteric effects mediate CHK2 phosphorylation of the p53 transactivation domain. EMBO Rep. 4, 787–792 (2003).

(11) Xiao, W., Chow, B. L. & Rathgeber, L. The repair of DNA methylation damage in Saccharomyces cerevisiae. Curr. Genet. 30, 461–468 (1996).

(12) Memisoglu, A. & Samson, L. Base excision repair in yeast and mammals. Mutat. Res.Fundam. Mol. Mech. Mutagen. 451, 39–51 (2000).

(13) Srivastava, D. K. et al. Mammalian Abasic Site Base Excision Repair IDENTIFICATION OF THE REACTION SEQUENCE AND RATE-DETERMINING STEPS*. J. Biol. Chem. 273, 21203–21209 (1998).

(14) Preissler, S., Rato, C., Perera, L. A., Saudek, V. & Ron, D. FICD acts bifunctionally to AMPylate and de-AMPylate the endoplasmic reticulum chaperone BiP. Nat. Struct. Mol. Biol. 24, 23–29 (2017).

(15) Fontaine, S. N. et al. Isoform-selective Genetic Inhibition of Constitutive Cytosolic Hsp70 Activity Promotes Client Tau Degradation Using an Altered Co-chaperone Complement*. J. Biol. Chem. 290, 13115–13127 (2015).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigated the extent to which phase-amplitude coupling (PAC) of respiratory and electrophysiological brain activity recordings was related to episodes of life-threatening apnoea in human newborns.

Strengths:

I want to commend the authors for acquiring unique and illuminating data; the difficulty in recording and handling these data has to be appreciated. As far as I can tell, Zandvoort and colleagues are the first to provide robust evidence for respiration-brain coupling in newborns. Their creative use of the phase-slope index for peripheral-central interactions is innovative and credible. If proven to be robust, the authors' findings have important implications well beyond the field of brain-body research.

Weaknesses:

While the analyses were overall competently conducted and well-justified, I was not entirely convinced by a few methodological choices, specifically i) the computation of PAC surrogates, ii) details of the linear mixed-effects model, and iii) the electrode selection for linking phase-amplitude coupling to apnoea frequency.

Thank you for your kind comments and helpful review of our paper. We have now clarified computation of PAC surrogates, added further details of the linear-mixed effects models and calculated the link between the strength of the cortico-respiratory coupling (phase-amplitude coupling) and apnoea rate with data acquired at all electrodes. We provide further details for each of these in response to your ‘Recommendations for the authors’.

Reviewer #2 (Public review):

Summary:

The author's central hypothesis was that the strength of cortico-respiratory coupling in infants is negatively associated with apnoea rate. To prove this, they first investigated the existence of cortico-respiratory coupling in premature and term-born infants, the spatial localisation of the cortical activity and its relationship with the phase of the respiratory cycle, and the directionality of coupling. 

Strengths:

The researchers used synchronised EEG and impedance pneumography to detect the phase amplitude coupling.

They have studied a wide range of gestations, from 28 weeks to 42 weeks, including males and females. Their exclusion criteria ensured that healthy babies were studied and potential confounders of impaired respiratory activity were avoided. Their sequential approach in addressing the objectives was appropriate.

Weaknesses:

As a neonatal clinician and neuroscientist, I have commented based on my expertise. I have not commented on signal processing.

I did not identify any major weaknesses in the study. Some minor weaknesses include:

(1) Data relating to the cortical oscillations and the respiratory phase is given. However, whether this would lead to their hypothesis that the strength of cortico-respiratory coupling is negatively associated with apnoea rate is unclear. What preceding data enabled the authors to link the strength of coupling to the rate of apnoea?

(2) If we did not know of data showing the existence of cortico-respiratory coupling in newborn infants, then should it not be the first research question to examine?

(3) What are the characteristics of the infants who contributed data to establish the cortico-respiratory coupling (Figures 2 and 3)?

(4) Although it is the most plausible direction of the relationship, with neural activation driving respiratory muscle contraction, how can the authors prove this with their data? Given that they show coherence between signals, how do we know that the cortical signal precedes the respiratory muscle contraction?

(5) Apgar score is an ordinal variable. The authors should summarise this as median (range).

Thank you for your useful comments. We have revised the manuscript to address these comments and improve the clarity.

(1) We agree that proceeding data leading to the hypothesis that the strength of cortico-respiratory coupling is negatively associated with apnoea rate is limited. We have clarified in the introduction that adult studies have previously suggested that cortical motor activity may prevent hypoventilation and apnoea seen in patient groups. We have also added further clarification to our hypothesis. In the introduction we now state:

“In adults with congenital central hypoventilation syndrome or obstructive sleep apnoea, a respiratory-linked increase in cortical motor activity suggests that the motor cortex plays an important role in maintaining autonomous respiration, with the authors postulating that cortico-respiratory drive whilst participants are awake may prevent the hypoventilation/apnoea observed in these patients whilst they are asleep.”

And later:

“We hypothesised that cortico-respiratory coupling occurs in newborns and that the strength of cortico-respiratory coupling is negatively associated with apnoea rate (in line with the suggestions made from studies of adults with congenital central hypoventilation syndrome[6] and obstructive sleep apnoea[7]).”

(2) We agree that this was the first research question we examined. We have clarified this in the introduction, now re-writing the hypothesis and aims to state “We hypothesised that cortico-respiratory coupling occurs in newborns and that the strength of cortico-respiratory coupling is negatively associated with apnoea rate (…). To this end, we first examined whether cortico-respiratory coupling exists in both premature and term infants.”

(3) Figures 2 and 3 used the full dataset. We have clarified this in the Figure captions by stating: “For all panels, data included is from 68 infants (28-42 weeks postmenstrual age [PMA] at time of recording) on 104 recording occasions. See Table 1 for further clinical and demographic characteristics.”

(4) We used a cross-frequency version of the phase-slope index to quantify the directionality and strength of information flow between cortical and breathing time series (Figure 3C,D). The phase-slope index investigates phase lags and how these change over narrow frequency ranges by examining the slope of the phase spectrum of their complex coherency. This indicates whether one signal leads or trails another signal (and thus indicating directionality). However, we agree (and as was also noted by Reviewer 3) that this analysis does not ‘prove’ directionality as other factors may influence the analysis. We have added the following to the text to address this point:

“However, caution is needed in the interpretation of these results as signal processing techniques such as the phase-slope index estimate directionality but do not confirm causality. Rather, they show a statistical relationship which can be influenced by a multitude of factors (e.g., signal-to-noise ratio and preprocessing steps). Nevertheless, the results suggest that cortical activity may precede respiration in newborns. Future work is needed to confirm this association by, for example, employing other metrics to estimate directionality, such as the time-lagged cross-correlation and Granger causality and through direct mechanistic studies.”

(5) We have revised Table 1 so that Apgar scores are provided as median and interquartile range.

Reviewer #3 (Public review):

Summary:

This is a strong and important report that presents a framework for understanding cortical contributions to neonatal respiration. Overall, the authors successfully achieved their goal of linking cortical activity to respiratory drive. Despite the correlational nature of this study, it is a crucial step in establishing a foundation for future work to elucidate the interaction between cortical activity and breathing.

Strengths:

(1) The introduction and use of workflows that establish correlational relationships between breathing and brain activity.

(2) The execution of these workflows in human neonates.

Weaknesses:

Interpretations related to causal inference, confounds of sleep and caffeine, and the spatial interpretation of EEG data need to be addressed to ensure that the data appropriately support the conclusions.

Thank you for your useful comments. We have now substantially revised the manuscript in relation to causal inference and our interpretations of the data, in particular adding further detail to the discussion with regards to the limitations of our approach and revising wording that has causal implications. We provide more detail in response to your ‘Recommendations for the authors’.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I want to elaborate on the three points of methodological criticism, and my apologies in case I have some misconceptions:

(1) It seems like the surrogate distribution to determine PAC significance was computed by shuffling EEG segments and recomputing PAC each time. Surrogate computations are a difficult topic when handling signals as regular as respiration time series. However, random shuffling of data segments is almost always an overly liberal approach (except for trial-based data) since it destroys the temporal autocorrelation of the underlying signal. As the resting-state data in the present study were per sé continuous (and just segmented for analytical purposes), I am not convinced that random shuffling provides an adequate control. Could the authors either a) provide convincing evidence that the temporal autocorrelation of verum and surrogate time series did not differ from one another, or b) conduct additional control analyses based on an alternative approach, e.g., by constructing surrogate respiration phase vectors and recomputing PAC accordingly? We have had good experiences with the IAAFT approach (outlined in Kluger et al., Nat Comms 2023), but others certainly exist.

Thank you for this important comment on the construction of surrogates. We agree that it is essential for any surrogate approach that it destroys the cross-signal coupling whilst preserving the signals’ internal structure (e.g., autocorrelation, spectral profile, and non-stationarities) as much as possible. We apologies for not describing this clearer in the initial manuscript, but we want to clarify that in the surrogate analysis, we did not shuffle time points/segments within EEG trials itself. Instead, we permuted the trial order so that respiration trial T1 was paired with an EEG trial other than T1. This leaves the 4-sec segments used in the PAC analysis unaltered. This surrogate technique preserves the important internal properties of each signal (within-trial autocorrelation, auto-spectra and power distribution of the signals) while destroying the cross-signal alignment across trials, and thus the trial-wise phase locking (e.g., coherence) between respiration and EEG. We have clarified this in the manuscript as follows:

“The surrogate analysis was performed by randomly permuting the trial (4-s segment) order of the EEG amplitude while leaving the respiration trial order unchanged (i.e., respiration segment S1 was paired with an EEG segment Sj, j ≠ 1). Importantly, no temporal samples were shuffled within segments. Thus, the full within-segment temporal structure, including autocorrelation and spectral profile (auto-spectra), was preserved for both signals. This permutation destroys trial-wise cross-signal phase alignment (and therefore coherence) while retaining the intrinsic dynamics of each signal.”

(2) The LMEM approach is very sound, but it seems like ID was the only random effect included in the model. Could the authors clarify whether multiple sessions from individual neonates were considered or whether each ID was only represented once? In case of the former, one possibility would be to include 'session' as an additional random effect; otherwise, the group statistic could be biased. Many thanks in advance for providing insight on this.

Thank you for this important point. Of the 68 infants included in the study, 49 only had a single session. The remaining 19 infants had between 2 – 5 sessions included. Given that most infants only had a single session it is not possible to identify random effects of session reliably and so we have not included session as a random factor. Moreover, postmenstrual age [PMA] (which is related to session order within a subject and is likely a more reliable indicator of variance given that sessions were not at fixed intervals) is already included as a factor in the analysis. Indeed, session ID is not a distinct source of clustering and will be indistinguishable from subject and PMA variance.

In relation to this question, we carefully checked the analysis and realised that we had included infant with a random effect of both slope and intercept. Given that most infants have only one session the random effect of slope cannot be estimated and so we have now removed this from the analysis leading to very minor changes in the results (and no changes in the interpretation). We have clarified in the manuscript that “Infant ID was included as a random effect acting on the intercept.”

(3) It is not entirely clear to me why the authors selected the two electrodes with the strongest overall PAC for the analysis of apnoea frequency. Why not consider all electrodes individually? What is the worry/hypothesis regarding electrodes with low PAC - would one not expect simply to find no relationship with apnoea frequency, and would that information not be instructive? Again, I want to thank the authors in advance for their take on this comment.

We initially included only the two electrodes with the strongest coupling as we would not expect a relationship with apnoea rate at those electrodes without significant coupling (as you say). For completeness, we have now included the relationships with all electrodes individually in Supplementary Figure S4. As expected, the relationship between apnoea rate and coupling (coherence) was not significant for the electrodes without strong coupling.

Reviewer #3 (Recommendations for the authors):

Major Comments:

(1) Causal Language and Overinterpretation are evident throughout the manuscript. The manuscript repeatedly uses language suggesting causality (e.g., "cortical motor activity reduces apnoea"), despite the correlational nature of the findings.

It is recommended that the authors reframe their claims in the abstract and discussion to clarify that the observed associations do not establish causal influence. For example, Abstract: "...revealing novel mechanistic insight....". This correlational observation does not reveal a mechanism but rather supports the concept of mechanistic interactions.

Thank you for this important point. We have now rephrased the manuscript throughout, particularly in the abstract and results/discussion. We have also added the following sentences to the discussion to address the point on causation:

“Nevertheless, it is important to recognise that a limitation of this analysis is that correlation does not imply causation, and future mechanistic studies are required to determine whether and how cortico-respiratory coupling plays a role in reducing apnoea in infants.”

And later:

“The limitations of our study need to be considered, and in particular, directionality of the cortico-respiratory coupling, improved spatial localisation, and a direct mechanistic link between cortico-respiratory coupling and apnoea rate, should be investigated in future work.”

(2) Potential Confounding by Sleep State and Caffeine. Sleep state is a significant determinant of apnoea occurrence and EEG frequency composition, yet no objective sleep-state classification is incorporated. Similarly, caffeine, administered in ~50% of recordings, is a potent respiratory stimulant. A reanalysis of the data, incorporating sleep proxies (e.g., EEG spectral ratios, delta/theta dominance) and caffeine exposure as covariates or stratification factors in the PAC-apnoea models, should be performed.

Sleep state: A limitation of our work is that we did not record sleep state and unfortunately, we do not have anyone trained to annotate sleep states from EEG recordings in our research group. We have added the following to the discussion to address this:

“It is known that most apnoeas in infants occur during active sleep[6][30] and delta- and theta-band frequencies in EEG are strongly related to sleep state[31]. A limitation of our study is that we did not record the sleep state of the infant.”

Caffeine: We agree that caffeine is a respiratory stimulant and, hence, it is important to consider this effect. Moreover, those infants prescribed caffeine are those who are at greatest risk of apnoea and so it is of interest to determine whether the relationship between PAC and apnoea rate occurs in those infants receiving caffeine treatment. We conducted a stratified analysis to address this point, now providing an additional Supplementary Figure.

(3) Directionality Inference from Phase-Slope Index. While PSI suggests a lead-lag relationship, it does not confirm causality and may be influenced by signal-to-noise or preprocessing steps. Validation PSI findings using additional metrics (e.g., time-lagged cross-correlation or Granger causality) or, at a minimum, temper interpretations of cortical "driving" respiration.

We agree that the PSI (and other metrics such as Granger causality) may be influenced by a range of factors. We have therefore changed the wording throughout and also added the following:

“However, caution is needed in the interpretation of these results as signal processing techniques such as the phase-slope index estimate directionality but do not confirm causality. Rather, they show a statistical relationship which can be influenced by a multitude of factors (e.g., signal-to-noise ratio and preprocessing steps). Nevertheless, the results suggest that cortical activity may precede respiration in newborns. Future work is needed to confirm this association by, for example, employing other metrics to estimate directionality, such as the time-lagged cross-correlation and Granger causality and through direct mechanistic studies.”

(4) Limited EEG Spatial Resolution. The attribution of CRC to "cortical motor areas" is overstated, given the use of only 8 EEG electrodes, which provides limited spatial coverage. Avoid overly precise interpretations regarding cortical localization unless source localization or higher-density EEG data are available.

We have added the following to specifically address this limitation.

“It is important to note that the number of electrodes in our montage is limited (with only 8 recording electrodes), and so source localisation was not possible; higher-density recordings are warranted to confirm whether the motor cortex plays a role.”

We have also changed the wording in the summary paragraph and abstract to add this limitation and reworded throughout the manuscript to highlight the limitations of our study.

Minor Comments

(1) Consider color-coding individual points in Figure 4A by PMA or caffeine status to visually disambiguate potential age-related or pharmacological effects.

We agree that this provides additional visual information and have colour-coded the points in Supplementary Figure S6 according to caffeine status.

(2) Clearly define PAC versus CRC. These are used interchangeably. Readers may benefit from a more consistent and precise usage, especially in the abstract.

Thank you for noticing this. We have revised the terms where necessary throughout, and the abstract and introduction to read:

“Using simultaneous electroencephalography (EEG) and impedance pneumography we investigated interactions between cortical and respiratory activity (known as cortico-respiratory coupling) using phase-amplitude coupling.”

“Recently, it was proposed that communication between the cortex and lungs, known as cortico-respiratory coupling, can be identified and quantified through phase-amplitude coupling. This functional coupling arises when the amplitude of cortical activity is modulated by the respiration phase, or vice versa. Phase-amplitude coupling is typically quantified using non-invasive recordings capturing respiratory and neural activity (e.g., magneto- or electroencephalography [EEG]).”

(3) Clarify the overlap with previously published datasets (line 358). Are any EEG-apnoea associations re-analyses of data published in Zandvoort et al., 2024?

We have amended this sentence to explain that the previous study did not investigate respiration/apnoea. We now state:

“Parts of this dataset have been reported earlier in Zandvoort et al. [33] to address a different research question (this study investigated the development of sensory-evoked potentials, which were also recorded in these infants; it did not explore respiration).”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Joint Public Review:

Summary:

The authors investigate how stochastic and deterministic factors are integrated in cell fate decisions, using Dictyostelium discoideum as a model system. They show that cells in different cell cycle phases (a deterministic factor) are predisposed to different fates, albeit with deviations, when exposed to the same environmental stimulus. However, gene expression variability (a stochastic factor) enhances the robustness of cellular responses to environmental cues that disrupt the cell cycle.

Using a simple, tractable mathematical model, the authors demonstrate that cell fate decisions in D. discoideum depend on a combination of deterministic and stochastic factors, i.e., cell cycle phase and gene expression variability, respectively. They then identify Set1 - a key regulator of gene expression variability - indicate the mechanism through which it modulates this variability, and link it to a phenotype in D. discoideum development. Finally, they confirm that gene expression variability contributes to the robustness of the cell's response to environmental disruptions that interfere with the cell cycle.

Strengths:

The authors are careful in the choice of their experiments and in measuring gene expression variability, using methods that account for expected trends with average gene expression.

Weaknesses:

However, in terms of mathematical modelling, it would be important to rule out sources of stochasticity (other than gene expression variability), and also to consider cases where stochastic factors are not necessarily completely independent of the deterministic ones.

We thank you and the reviewers for the insightful comments that have helped clarify the findings presented. We have addressed all comments and feel that the revised manuscript is much improved.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Minor typographical mistakes:

(a) in the title: Linage -> lineage

Corrected as suggested

(b) on page 19: use a full stop in "...are biased towards the stalk fate, Use of the cell cycle position..."

Corrected as suggested

(c) on page 20: become -> becoming in "...(and end up biased towards become stalk)..."

Corrected as suggested

(d) on page 16: "mu = G p k". Perhaps it should be x instead of k?

Corrected as suggested

(2) Regarding the abstract:

(a) This work tries to outline general principles (coordination/integration of deterministic and stochastic factors) in cell fate choice, especially when cells are faced with (near) identical environmental conditions. Perhaps the abstract, especially the first line, could be rephrased to reflect the generality of symmetry breaking and differentiation that is studied in this article/work. e.g., as was done in the first paragraph of the discussion.

Corrected as suggested

(b) It might be worthwhile clarifying what "this" is in the sentence "We suggest this represents an adaptive mechanism that increases developmental robustness against perturbations that affect deterministic signals." in the abstract.

Corrected as suggested

(3) Regarding the model:

(a) The model tries to combine the stochastic and deterministic parts to explain the propensity for stalk fates. It is assumed that the cell cycle-associated factors (CCAF) provide the deterministic part while the cell cycle-independent factors (CCIF) provide the stochastic part. The net result is an addition of the two, which is then compared against a threshold to decide the propensity for stalk fates. However, another simple way to introduce stochasticity would be to make the CCAF decay stochastic. Reasons to consider this scenario would be: (i) the decay process (especially in the biological context) is generally stochastic, (ii) it would not be inconsistent with the fact that cell cycle dependent genes are also variable, and (iii) this way of introducing stochasticity would also provide expression level characteristics/plots similar to the ones outlined in Figure 1C, i.e. with a probability distribution of CCAF values for a given amount of time after mitosis. Would there be arguments or experimental evidence to rule this possibility out? For instance, would the results shown in Figure 7 contradict this model?

We agree that there could be stochasticity the CCAF decay process. In this scenario, the expected value of CCAF (which would reflect the mean of a noisy distribution) would show a deterministic pattern of decay through time, representing the average value of CCAF across cells that are in the same phase of the cell-cycle. The noisiness around such a pattern of deterministic decay in the mean value of CCAF (i.e., the residual variation) would then represent CCIF since it would be, by definition, cell-cycle independent. Hence, the present model is fully consistent with this possibility since it would still lead to some variation being cell-cycle associated and some variation being cell-cycle independent. Therefore, this scenario could be viewed as a different functional/biological process leading to the same ultimate distribution we model. To clarify this, we have added text justifying the hypothesis that the noisy distribution is due to gene expression differences, rather than decay itself:

“Protein levels can vary widely between cells because it is regulated at multiple levels, including transcription, translation and stability. The position of the noisiest step in a pathway affects the overall noise dramatically, because each step usually amplifies noise in the previous steps (Alon 2007). Consistent with this idea, theory and single-cell experiments have shown that a major contributor to cell-cell variation is the bursty expression of low-copy mRNAs. We therefore hypothesized that this noisiness across cells arises from stochastic expression of a set of genes contributing to CCIF levels.”

(b) On page 7, the formula for total CCIF variance assumes independence of the genes g_i. Is this a reasonable assumption?

This concerns the argument that a set of stochastically expressed genes will yield an approximately Gaussian distribution of CCIF. Our results do not depend on the solution for the mean and the variance, only that noisy genes will generally yield such a Gaussian distribution.This is because independence is not strictly required for the central limit theorem to yield a Gaussian distribution. The distribution will still be Gaussian under a broad range of conditions (especially since gene expression is bounded, so there is no chance of the total ending up generating an infinite variance). The primary requirement is that the expression of any given gene is independent from that of most other genes. As a result, most of the variation in expression across genes is independent (even if any given gene is not independent from all other genes).

The most likely pattern of non-independence will be the case in which gene expression is ‘modular’, where there are co-expressed blocks, meaning that non-independence is limited in scale so that genes within a co-regulated block show correlated expression, but their expression is uncorrelated to genes in other blocks. This pattern is functionally analogous to what is known as m-dependence in sequences of random variables (e.g., time series), where variables close together in sequence are correlated (but otherwise uncorrelated). Derivations of the central limit theorem have shown that the means (and hence the sum) of these sorts of variables still follow an approximately Gaussian distribution over a broad range of scenarios. In the case of non-independent gene expression, this means that we can view the independent random variable as being the expression value of a group of co-expressed genes (instead of individual genes). Hence, the means (or sums) of these values will still conform to the central limit theorem.

This problem is addressed in:

Diananda, P. H. 1955. The central limit theorem for m-dependent variables. Proc. Combin. Philos. Soc. 51:92-95

Hoeffding, W. & H. Robbins. 1948. The central limit theorem for dependent random variables. Duke Math. J. 15:773-780

Orey, S. A. 1958. Central limit theorems for m-dependent random variables. Duke Math. J. 25:543-546

Rosén, B. 1967. On the central limit theorem for sums of dependent random variables, Z. Wahrscheinlichkeitstheorie und Verw. Gebiete, 7:48-82

To clarify this, we have added the following text and references:

Although this derivation implicitly assumes that stochastically expressed genes are independent, this assumption is not strictly required for the distribution of CCIF to be approximately normal. If stochastically expressed genes show clustered co-expression owing to shared regulation, then the sum across these co-expressed blocks is still expected to be approximately normally distributed (as long as there are a reasonably large number of co-expressed clusters) (Diananda 1955; Hoeffding and Robbins 1994; Rosén 1967).

(4) In section "Cell cycle independent stochastic gene expression variation is extensive in growing cells":

Regarding the statement: "We first determined the coefficient of variation (CV2) of expression for all genes. As expected, this tends to decrease as average expression level increases (Supplementary Figure 2).":

It would be good to specify how the "expected variation" was calculated exactly. For instance, it was hard to discern from Supplementary Figure 2 how CV^2 decreasing with average expression levels was used in the calculation of expected variation.

This is described in the methods on page 38

“A trend line was fitted to the data using non-linear least squares regression (Scran v1.15.9). Genes were defined as variable (2073 genes) based on a one-sided test assuming a normal distribution around the trend but one where deviation changed depending on the mean expression of a given gene (Scran v1.15.9 - modelGeneCV2) with a FDR of < 0.05.”

(5) In section "Stochastically expressed genes are associated with cell fate determination"

(a) For readers unfamiliar with the organism ‘Dictyostelium discoideum’, a short description of its life cycle with growth and development/differentiation phases would be useful to provide the right context.

Corrected as suggested

(b) In section "Cell cycle independent stochastic gene expression variation is extensive in growing cells", it was shown that cell cycle dependent genes are also highly variable (in other words, ‘stochastic’). It would, therefore, be useful to elaborate on the definitions of "stochastically expressed genes, cell cycle-associated genes, and non-variable genes", as used in this section. Admittedly, the distinction does get clearer towards the last section of Results, but some elaboration here would make the reading smoother.

Corrected as suggested

(c) If the "cell cycle associated genes" are the same as "cell cycle dependent genes", it would be good to use one term consistently.

Corrected as suggested

(d) The developmental index is divided into 10 bins from 0 to 1. Is there a rationale for the choice of a number of bins? Would this choice affect significance tests for "stochastic" vs others? <br /> (The same question may apply to the "Cell type index")

Significance is robust to the number of bins chosen (e.g. 5-25). Of course, if there are too many bins (low number of genes) or too few bins (addition of noisy data) significance falls. In the case of developmental index, our choice of bins is also based on previous analyses (de Oliveira, et al 2019), which developed the index we used, and showed that a threshold of >0.9 can be used to identify ‘developmentally expressed genes’.

(6) In Figure 5:

(a) Does the statement "*** binomial test, p<0.01." (as seen in caption for part C) actually refer to part D?

Corrected as suggested

(b) Could the authors please specify what "mis-expressed" means in Figure 5D? Are these genes that are upregulated, downregulated, or both? From what set of genes was the random sampling done?

Corrected as suggested

(c) In Figure 5F, is the decrease in CV^2 explained entirely by the increase in mean (as shown in Figure 5E)?

We appreciate the point made by the reviewer and recognise that disentangling changes in gene expression variation from changes in expression levels is extremely difficult (any changes in burst frequency will necessarily affect expression level). However, we do not think this affects our conclusions, which are supported by results with representative Set1 dependent reporter genes (Figure 5G and H) which suggest that the number of cells expressing (rather than the expression in each cell is affected) in these cases at least.

(7) In Figure 6A: Could the authors please elaborate on the difference between the rows labelled "WT" and "set1-"? Are they two different types of chimera?

Corrected as suggested

(8) In Section "Cell cycle position and gene expression variation interact to control cell type proportioning":

Is there a graph corresponding to the statement "However, the level of GFP expression in each responding cell did not significantly change."?

Corrected as suggested

(9) In section "Influence of stochastic variation on sensitivity to cell cycle perturbations" of the Supplementary text:

(a) The model for cell cycle bias is not entirely clear. For instance, is the quantity N(t) = U(t) + Q_t U(t) also a probability distribution, like U(t) is? If so, there must be a normalization factor. It was difficult to understand the procedure behind this calculation. Perhaps some more elaboration (with words or a small schematic) on this model/method would help.

The value of U(t) was originally being used to denote the uniform probability density function (for the uniform distribution), but for clarity this has been changed to follow the convention that U[a,b] denotes the uniform distribution over the interval from a to b (which, in this case would be U[0, 1]), while f(t) is now being used to make it clear that this is the probability density, where f(t) = 1 across the interval. Because the uniform distribution necessarily integrates to 1 over the defined range, it does not need to be normalised. The confusion here is perhaps due to the expression f(t) = 1 being interpreted as defining the probability of sampling a value of t (but in a continuous distribution we can only define the probabilities of sampling over an interval), instead of defining the probability density over the interval from a to b, where f(x) would be 1/(b – a), and hence over the interval of 0 to 1, f(x) would equal 1.

To help clarify this issue, this section has been rewritten and a new figure (which appears as Supplementary Figure 12) has been added that illustrates the resulting probability density functions for biased sampling from the cell cycle.

(b) References to Figure 8A, B seem to be indicating Supplementary Figure 12 instead. 

Corrected as suggested

Reviewer #2 (Recommendations for the authors):

This manuscript seems quite interesting, but many sections are so unclear that I cannot follow what has been done. I would suggest slowly going through the manuscript and carefully explaining things. This will probably considerably increase the size of the manuscript, but many sections are too terse to follow even after many, many readings of the Results and figure legend.

Corrected as suggested

Some specific comments (this is not at all comprehensive, but rather illustrative)

Page 2 - 'genes strongly associated with fate choice' - can you explain this a bit more - genes associated with one cell type or another, or genes that somehow regulate the choice?

Corrected as suggested

Page 2 - this abstract is quite vague, I would suggest being more specific to reflect what is in the manuscript.

Corrected as suggested

Page 3 - 'exhibit bivalent H3K4me3..' please explain 'bivalent' a bit more.

Corrected as suggested

Page 7 - 'Bernoulli process with probability that (meaning that is scaled to the size of the temporal interval)' (non-copying symbols deleted) could be simplified.

Corrected as suggested

Page 7 - please define all variables/ equation components. What is N? What is x bar? What is s2? The middle paragraph is very difficult to follow.

This paragraph has been rewritten and a definition of the distribution added for clarity.

Page 7 - 'genes might logically vary in the value of pi, such variability does not impact our results. Trying to decipher this paragraph, it seems that pi is a function of time, so this could affect the results.

pi is the probability that a stochastically expressed gene is actually expressed in whatever interval is being considered for all genes. pi will necessarily increase if the time interval considered is increased. The key point is we are considering the probability that any given gene is expressed in the same time interval. In this case, genes could vary in pi, and thus some burst more often and others less often.

Page 9 - '(it is 98.35 times more likely' there may be too many significant figures here.

Corrected as suggested

Page 10 - for the Area Under the Receiver Operating Characteristic Curve (AUROC), what are you classifying? AUROC is typically used for diagnostic tests to determine how well the test can discriminate between two completely different outcomes. What is the input, and what are the outcomes?

Corrected as suggested

Figures:

What are the dashed lines in Figure S2A?

Corrected as suggested

What are the X-axes in Figure S3?

Corrected as suggested

I do not understand what you are showing in Figure S3.

Corrected as suggested in results

In Figure 2B, I cannot find in the text or figure legend any description or explanation of 'Group 1', 'Group 2', or 'Group 3'.

Corrected as suggested

Figure 3D needs a lot more explanation; I cannot understand this based on the text and the figure legend.

Corrected as suggested

The Set1 work should discuss the work in PMID: 39242621

Corrected as suggested

Figure 8 D needs a size bar

Corrected as suggested

Author response:

The following is the authors’ response to the original reviews

Public review:

Reviewer #1 (Public review):

Summary:

Badarnee and colleagues analyse fMRI data collected during an associative threatlearning task. They find evidence for parallel processes mediated by the mediodorsal, LGn, and pulvinar nuclei of the thalamus. The evidence for these conclusions is promising, but limited by a lack of clarity regarding the preprocessing and statistical methods.

Strengths:

The approach is inventive and novel, providing information about thalamocortical interactions that are scant in the current literature.

Weaknesses:

(1) There are not sufficient details present to allow for the direct interrogation of the methods used in the study.

We thank the reviewer for this comment. We have added more detailed information about the methods to clarify our procedure. In addition to the original description of our threat learning paradigm in humans, we included the following to page 39-40:

“Experimental procedure

Threat learning: Please see the original description in the manuscript.

Shock level: The shock intensity used in the fear learning paradigm was determined during a preexperiment calibration. Electrodes were attached to the participant’s right hand, and stimulation began at a low level (0.1 mA), gradually increasing in small increments. After each increment, participants verbally rated their discomfort. The procedure continued until the participant identified a level they described as “highly annoying but not painful.” This individualized intensity was then used for that participant throughout the experiment. For safety and ethical reasons, the maximum intensity was capped at 20 mA, and no participant received a shock above this limit.

Instructions to the participants: Each visual stimulus in our paradigm was first shown to participants for 6 seconds. This initial presentation served as habituation, allowing us to isolate the responses to genuinely new stimuli. Before the experiment began, participants were informed that they would see pictures illuminated with different colored lights, such as red or blue. During the experiment, some pictures might be paired with an electric shock, while others might not. Participants were instructed to pay attention to whether a specific color or pattern was associated with the shock. These instructions were adopted from previous studies in which our group developed this paradigm and found them highly effective for human learning. We therefore used the same approach in the current experiment. These instructions were provided throughout all phases of threat learning, and participants were informed that any shocks delivered would be at the same intensity determined on Day 1.”

(2) The figures do not contain sufficiently granular details, making it challenging to determine whether the observed effects were robust to individual differences.

We thank the reviewer for this suggestion. We agree that visualizations exposing the full data distribution can be highly informative, and we therefore present distribution-based plots for several analyses (e.g., connectivity results in Figure 7). However, for the activation analyses, our primary goal was to highlight trial-to-trial changes and overall patterns across thalamic nuclei, rather than the distribution of individual data points per se. For this purpose, bar plots with standard errors provide a clearer representation of the directional effects and facilitate comparison across trials and conditions.

Reviewer #2 (Public review):

Summary:

The authors quantify human fMRI BOLD responses in pulvinar and mediodorsal thalamic nuclei during a fear conditioning and extinction task across two days, in a large sample size (hundreds of participants). They show that the BOLD responses in these areas differentiate the conditioned (CS+) and safety (CS-) stimuli. Additionally, this changes with repeated trials, which could be a neural correlate of fear learning. They show that the anterior pulvinar is most correlated with the MD, and that this is not due to anatomical proximity. They perform graph analysis on the pulvinar subnuclei, which suggests that the medial pulvinar is a hub between the sensory (lateral/inferior) and associative (anterior) pulvinar. They show different patterns of thalamic activity across conditioning, extinction, recall, and renewal.

Strengths:

The data has a large sample size (n=293 in some measures, n=412 in others). This is a validated human fear conditioning/extinction task that Dr Milad's group has been working with for several years. Few labs have investigated the thalamus activity during fear conditioning and extinction, particularly with a large sample size. There is an independent replication of the pulvinar network structure (Figure 3), which suggests that the processing in the more sensory-related inferior and lateral pulvinar is relayed to the anterior pulvinar (and possibly thereby to more action-related prefrontal areas) via an intermediate step in the medial pulvinar - potentially a novel discovery, but that needs more validation.

Weaknesses:

(1) The authors cannot make causal claims about their results based on correlational neuroimaging evidence. Causal claims should be pared back. E.g., sentence 1 in the Results section: "The anterior pulvinar and MD contribute to early associative threat learning, as evidenced by increased functional activation in response to CS+ compared to CS- at the block level (Fig. 1b-c)." needs to be reworded to something like "The anterior pulvinar and MD have increased functional activation... This suggests that these areas may contribute to early associate threat learning."

We acknowledge the limitations of fMRI studies and agree with the reviewer that causal claims cannot be made based on correlational neuroimaging evidence. Accordingly, we revised the text to reduce causal interpretations. Specifically, we reworded the sentence identified by the reviewer in the Results section and systematically updated language throughout the manuscript.

Page 9: “At the block level, both the anterior pulvinar and MD showed increased activation to CS+ vs. CS− (anterior pulvinar: t₍₂₉₂₎ = 4.41, p = 0.00001, d = 0.25; MD: t₍₂₉₂₎ = 6.41, p = 5.83x10^-10, d = 0.37; Fig. 1b–c), suggesting a possible involvement of these regions in early associative threat learning.”

Throughout the manuscript, we replaced terms such as “reflects” with “likely reflects” and “indicating” with “consistent with,” and introduced explicitly correlational phrasing where appropriate (e.g., “apparently,” “closely align,” and “seems to”). All revisions are highlighted in green in the revised manuscript.

(2) Figure 1: The fact that the difference in BOLD activity between CS+ and CS- goes away on the third trial is not addressed. This is a very large effect in the data.

We thank the reviewer for highlighting this important pattern in Trial 3. The CS+ vs. CS− contrast in the third trial in the mediodorsal thalamus remained statistically significant after FDR correction and was correctly reported in the Supplementary Tables. However, we acknowledge that the statistical marker was inadvertently omitted from Figure 1. We have now corrected the figure to include the appropriate significance annotation.

In addition, we now explicitly describe the attenuation of the CS+ vs. CS− difference by the third trial in the mediodorsal thalamus but not in the pulvinar (page 32):

“This suggested rapid initial acquisition of the predictive value of the CS+ is thought to be pronounced during the first two trials. The attenuated CS+ vs. CS− differentiation on the third trial specifically in the pulvinar may reflect a decreased requirement for differential thalamic engagement once the initial association has been acquired, or an initial survival fear reaction is expressed. Notably, because the MD sustained the BOLD response to the CS+ in the third trial which may indicate involvement of this nucleus in the consolidation or stabilization of the learned association. This aligns with the wellestablished MD-PFC circuit involved in cognitive processes (Wolff and Halassa, 2024). Additionally, in a previous study using a similar paradigm, we observed sustained CS+ vs. CS− differentiation on the third trial in the nucleus reuniens, as well (Tuna et al., 2025). These findings suggest that trialdependent learning dynamics may vary across thalamic nuclei rather than reflecting a uniform thalamic learning signal. Together, while our paradigm does not inherently distinguish between different stages of learning, such as early acquisition and stabilization, our findings are consistent with stronger associative learning–related engagement during the first two trials, with a reduced differential response by the third trial that may reflect the involvement of different neural processes”.

(3) Figure 3: Could the observed network structure be due to anatomical proximity? Perhaps the authors should do an analogous analysis to what they did in Figure 2 for this intra-pulvinar analysis. This analysis doesn't take into account the indirect connections through corticothalamic and thalamocortical connections with the visual cortex and the pulvinar. There is an implicit assumption that there are interconnections between the pulvinar subnuclei, but there are few strong excitatory projections between these subnuclei to my knowledge. If visual areas are included in the graph, it would make things more complex, but would probably dramatically change the story. In this way, the message is somewhat constructed or arbitrary.

We thank the reviewer for this insightful comment. We agree that the network analysis in Figure 3 does not provide a direct anatomical account of pulvinar connectivity and cannot distinguish between direct inter-nuclear interactions and indirect coupling mediated via corticothalamic and thalamocortical pathways, including visual cortex.

Our intention with this analysis was to characterize functional statistical dependencies among pulvinar divisions during conditioning, rather than to infer monosynaptic anatomical connectivity. Accordingly, the observed network structure should not be interpreted as evidence for direct excitatory projections between pulvinar subnuclei.

We agree that including visual cortical regions in the network would substantially increase model complexity and could alter the inferred network structure. However, doing so would require a trial-wise, multiregional modeling framework that goes beyond the scope of the present intra-pulvinar analysis.

In response to this comment, we have now explicitly clarified the assumptions, interpretational limits, and alternative explanations of the network model in the Discussion (page 33):

“Yet, these intrapulvinar relationships should be understood as a functional and computational model, reflecting statistical dependencies among pulvinar divisions during threat learning, rather than as evidence of direct monosynaptic anatomical connections. Because detailed inter-nuclear anatomical connectivity within the pulvinar remains incompletely characterized, our analysis does not presuppose strong direct excitatory projections between subnuclei. Instead, our findings are intended to highlight candidate functional relationships within the pulvinar during conditioning with different level of data processing, rather than to provide a definitive anatomical map.”

We also included the following in the Limitations and Future Directions section (page 36):

“The observed relationships among pulvinar divisions during conditioning are purely functional and do not distinguish direct inter-nuclear interactions from indirect coupling mediated by corticothalamic and thalamocortical pathways, including visual cortical regions. Thus, the pulvinar model may reflect indirect cortical loops, weak or currently undocumented inter-nuclear interactions, or a combination of both.”

Finally, we added this note to the legend of Fig. 3:

“Note: The functional relationships among pulvinar divisions during threat learning should be interpreted as computational dependencies derived from statistical associations. These effects may reflect indirect interactions mediated by corticothalamic and thalamocortical pathways (e.g., via visual cortex), rather than direct inter-nuclear connectivity. Elucidating the underlying anatomical mechanisms will require future studies.”

(3) In the results section describing Figures 4-7, there are no statistics supporting the claims made. There needs to be a set of graphs comparing the results across the study sessions and days, with statistical comparisons between the different experiments to confirm differences.

We thank the reviewer for this suggestion. In this study, each phase (conditioning, extinction, recall, and renewal) was analyzed separately to characterize thalamic function within that specific phase. Our primary conclusions focus on differences between CS+ and CS− within each phase, rather than comparisons across phases or sessions. Direct statistical comparisons across phases were therefore not performed, as they fall outside the scope of our main hypotheses.

We have clarified this in the revised manuscript to make the rationale for our analytic approach explicit. Added to page 8:

“The purpose of this study is to investigate thalamic function during each learning phase separately, focusing on CS+ vs. CS− differences within phases rather than comparing activation across phases. This phase-specific approach allows us to characterize thalamic functional dynamics within each stage of learning and memory, avoiding potential confounds arising from the distinct processes of conditioning, extinction, and recall.”

(4) Figure 7 does not include the major corticothalamic and thalamocortical projections from early, mid-level, and higher visual cortex to the different pulvinar nuclei. I doubt that there are strong direct projections between the pulvinar nuclei; rather, the functional connections are probably mediated through interconnections with cortical visual areas.

We thank the reviewer for this point. Reciprocal connections between the visual cortex and the pulvinar are established, but the precise projections to specific pulvinar divisions remain unknown. We have added a note to the Figure 8a caption to clarify this (Figure 7a in the original version).

“Note (panel a): Known pulvinar–cortical connections, as well as sensory input pathways (e.g., visual inputs via the retina/LGN and nociceptive inputs via the spinothalamic tract), are not explicitly shown. These connections are well established anatomically but were omitted due to their heterogeneity and incomplete characterization at the level of pulvinar subnuclei. Their absence should not be interpreted as a lack of anatomical or functional relevance.”

(5) Stylistic: There are a lot of hypotheses and interpretations presented in this primary literature paper, which may be better suited for a review or perspective piece.

We thank the reviewer for this comment. We aimed to integrate our empirical findings within a broader conceptual framework to provide a complementary narrative, rather than presenting isolated observations without connecting them to theoretical context. This approach is intended to strengthen the interpretive value of the study while remaining grounded in primary data.

(6) In the discussion, there is an assumption that the fMRI BOLD responses to CS+ and CS- need to be different to indicate that an area is processing these distinctly, but the BOLD signal can only detect large-scale changes in overall activity. It's easy to imagine that an area could be involved in processing these two stimuli distinctly without showing an overall difference in the gross amount of activity.

We thank the reviewer for raising this important point. We fully agree that the fMRI BOLD signal reflects large-scale changes in population activity and may fail to capture more subtle or distributed neural representations. Accordingly, the absence of a CS+ vs. CS− BOLD difference should not be interpreted as evidence that a region is not involved in discriminating these stimuli. Rather, our inferences are limited to differences in aggregate activation at the spatial and temporal resolution of fMRI.

To partially address this limitation, we analyzed anatomically defined thalamic subregions; however, we acknowledge that finer-scale subdivisions and cell-type– specific processing likely exist that are not currently resolvable in human fMRI. Such distinctions may be better investigated using invasive recordings or circuit-level approaches in rodents or non-human primates. This limitation has now been explicitly acknowledged in the Limitations section of the manuscript (page 36):

“Pulvinar divisions, MD, and LGN each contain diverse neuron subtypes and finer anatomical subdivisions that may serve distinct functions. Importantly, the absence of CS+ vs. CS− differences in BOLD activity should not be interpreted as a lack of stimulus-specific processing, as such distinctions may occur without changes in overall activation detectable by fMRI…”

(7) There is strong evidence that the BOLD responses to the threat-related and safetyrelated stimuli are different, modest evidence for their claims of learning/plasticity in these pathways, and circumstantial evidence supporting their hypothesized graph network models. Overall, most of the claims made in the discussion are better considered possible interpretations rather than proven findings - this is not a criticism, as these experiments and subject matter are extremely complex.

We thank the reviewer for this constructive suggestion. In response, we have revised the discussion to present our interpretations as possible or plausible explanations, rather than definitive conclusions, to better reflect the strength of the current evidence. The changes are marked in green throughout the Discussion section.

This study continues to validate the power and utility of this in human fear conditioning/extinction paradigm, and extends this paradigm to investigating fear learning beyond the traditional limbic system pathways. It's possible that their models for the pulvinar nuclei interconnections could guide future neuromodulation or DBS studies that could provide more causal evidence for their hypotheses.

Reviewer #3 (Public review):

Summary:

The present work was aimed at investigating the specific contributions of thalamic nuclei to associative threat learning and extinction. Using fMRI, they examined activation patterns across pulvinar divisions, the lateral geniculate nucleus (LGN), and the mediodorsal thalamus (MD) during threat acquisition, extinction, and recall. Their goal was to uncover whether distinct thalamic systems support different modes of learningautomatic survival mechanisms versus more deliberate processes - and to propose a hierarchical pulvinar model of fear conditioning. They also try to refine current neuroanatomical models of threat learning and memory, highlighting the role of thalamic nuclei in it.

Strengths:

(1) Valuable theoretical elaboration and modeling regarding the differential role of pulvinar subdivisions on feedforward (inferior, lateral) and higher-order integration (anterior), and their functional interplay with other relevant subcortical and cortical structures in associative threat and extinction learning.

(2) Large sample sizes and multipronged analytical approaches were used for hypothesis testing.

(3) Exhaustive literature review in the field of associative threat, as well as regarding the role of thalamic nuclei and other brain structures in it.

Weaknesses:

(1) Several weaknesses should be pointed out regarding how fMRI data were collected, as well as decisions regarding how the fMRI data were preprocessed and analyzed:

(a) fMRI data have low resolution (3 cubic mm), which certainly limits the examination of small nuclei such as the ones investigated here, and especially the examination of the LGN and inferior pulvinar.

We thank the reviewer for raising this point. While the spatial resolution of fMRI (3 mm isotropic) does limit voxel-wise examination of very small nuclei, our analyses were not performed at the single-voxel level. Instead, signals were extracted using anatomically defined masks for each thalamic nucleus, which is a standard and widely used approach for studying small subcortical structures with fMRI. This strategy increases signal-to-noise ratio and mitigates partial-volume effects by aggregating activity across voxels belonging to the same anatomical region.

(b) fMRI was normalized to standard space. Analyzing the data in individual-subject space would have given you the options of avoiding altering every participant's brain and of using a probabilistic thalamic atlas that better adapts to each subject's brain and thalamic nuclei (see, for instance, Iglesias et al., 2018). This would have been ideal and would have given the authors more precision, especially considering the low resolution of the fMRI data and the size of the thalamic nuclei of interest.

We thank the reviewer for pointing out the availability of specialized thalamic atlases. In our study we used the Automated Anatomical Labelling Atlas 3 (AAL3 atlas), which includes thalamic subdivisions (including pulvinar and other nuclei) among its 150+ whole-brain regions and is widely used for ROI extraction in normalized fMRI analyses. This choice allowed us to define consistent ROIs across the entire brain such as the amygdala and hippocampus within the same parcellation framework and to extract functional signals at the resolution of our preprocessed fMRI data.

While histology-informed probabilistic atlases offer finer microanatomical segmentation of the thalamus, they are implemented primarily for structural segmentation pipelines (e.g., FreeSurfer) and do not change the fact that AAL3’s thalamic subdivisions are established and anatomically reasonable ROIs for functional studies at standard fMRI resolutions. AAL3 thus provides a practical and valid choice for our whole-brain activation and connectivity analyses.

(c) On top of the two previous points, the authors decided to smooth the data to 6mm, which means that every single voxel within these small nuclei was blurred/mixed with the 2 immediately contiguous voxels (if they followed the standard SPM12 normalization resampling default which resamples, or upsamples the data in this case, to 2 x 2 x 2mm). Given the strong changes in structural connectivity and function that can occur, especially in the thalamus, on voxels of this size, this and the previous 2 decisions do not favor anatomical precision.

We thank the reviewer for raising this concern regarding anatomical precision. The data were resampled to 2 × 2 × 2 mm resolution in SPM12, and a 6 mm FWHM Gaussian smoothing kernel was applied. Gaussian smoothing does not uniformly mix immediately adjacent voxels; rather, it applies distance-weighted averaging with a standard deviation of approximately 2.55 mm (FWHM = 2.355σ). At 2 mm resolution, this corresponds to ~1.3 voxels, meaning that signal contribution decreases smoothly with spatial distance rather than reflecting simple voxel averaging. Moreover, all statistical analyses were conducted at the ROI level using anatomically defined masks, rather than voxel-wise inference within nuclei.

To empirically assess whether smoothing may have introduced boundary-driven spillover effects, we divided the mediodorsal (MD) thalamus into medial and lateral divisions and examined the CS effect separately in each. The CS effect did not differ between subdivisions (MD subdivision X CS interaction: F_{(1, 292)} = 0.50, p = 0.48).

Additionally, across trials, the CS+ vs. CS− effect was observed in both subdivisions and showed comparable magnitudes (see Author response image 1). The effect sizes were also comparable across MD divisions as presented in Author response table 1).

Author response image 1.

Mean activation in MD subdivisions during threat learning

Author response table 1.

Point estimates and 95% confidence intervals of effect sizes (Cohen’s d) for CS+ vs. CS− contrasts in MD, MDm, and MDl During Early Threat Learning

If smoothing had artificially driven the MD effect via boundary spillover, one would expect consistent asymmetry or substantially larger effects in one subdivision relative to the other. Instead, the CS effect was distributed across both medial and lateral MD, supporting the interpretation that the observed activation reflects intrinsic MD signal rather than smoothing-related contamination.

(d) Motion during scanning was poorly controlled in the preprocessing. Including the motion parameters as covariates of no interest in the GLM does not fully guarantee that motion is not influencing the results, and that motion is not differentially influencing some experimental conditions more than others.

Our analyses are within-subject, so each participant serves as their own control, minimizing the impact of motion differences across conditions. Functional data were preprocessed with fMRIPrep 20.0.2, which estimates motion parameters. The motion estimations are included in the GLM to account for residual motion-related variance in SPM12. The connectivity analyses were conducted in CONN, which also includes these motion parameters as regressors and applies additional denoising steps to further reduce motion-related effects. Together, these procedures make it highly unlikely that motion systematically influenced the observed condition differences.

(2) It is not clearly indicated in the manuscript how many subjects and how many trials went into each of the analyses. It would be important to indicate this in the text and/or the figures.

We thank the reviewer for this important comment. We have now explicitly reported the number of participants and trials contributing to each analysis throughout the manuscript, including the main text, figure captions, and supplementary materials.

Specifically, under Materials and Methods (page 38), we now clarify the sample sizes for each learning phase:

“We analyzed fMRI data from 293 participants during fear conditioning, 320 during extinction, 412 during extinction recall, and 312 during threat renewal.”

In addition, all figure captions now report the corresponding sample sizes and trial numbers. For example, the caption to Figure 1 (pages 7–8) states:

“…Block-level comparisons were assessed using paired t-tests, while trial-level effects were examined using a 2 × 2 repeated-measures ANOVA, followed by post hoc comparisons between CS+ and CS− across four trials. Multiple comparisons were controlled using false discovery rate (FDR) correction. Conditioning sample size: n = 293. Detailed statistical parameters are provided in Supplementary Tables 1–2.”

(3) It is not clear either, why, given the large sample size, some of the results were not conducted using reproducibility strategies such as dividing the sample into 2 or 3 groups or using further cross-validation strategies.

Cross-validation strategies were applied to the mediation analyses, which are regressionbased and can be sensitive to extreme values or overfitting, ensuring that observed effects generalize beyond the sample. In contrast, the repeated-measures ANOVA tests within-subject condition differences, and is inherently robust to between-subject variability. For these inferential tests, cross-validation or sample-splitting is not typically applied.

However, following the reviewer’s recommendation, we conducted a cross-validation analysis focusing on the anterior pulvinar and the mediodorsal thalamus, the primary regions of interest in this study. The full sample (N = 293) was randomly divided into three subsamples (n₁ = 106, n₂ = 91, n₃ = 96). For each iteration, we conducted a repeatedmeasures ANOVA (RM-ANOVA) within one subsample and then examined the stability of the CS+ vs. CS− difference in the remaining two subsamples combined. The CS+ vs. CS− difference was statistically significant in most folds for both the mediodorsal thalamus and the anterior pulvinar. Importantly, effect sizes were comparable across folds within each nucleus, indicating stable estimates of the CS effect.

Finally, we observed a comparable pattern of CS+ vs. CS− differences at the trial level in both the mediodorsal thalamus and the anterior pulvinar. Critically, the effect sizes of these differences were stable across most cross-validation folds

(4) Limited testing of alternative hypotheses. The results clearly seem to be a selection of the findings supporting the hypotheses that the authors sought to confirm. (just one example: in the analysis reported in Figures 1-2; are there other correlations between the activation of the anterior pulvinar and MD with other pulvinar nuclei? only the MDanterior Puv is reported).

We thank the reviewer for raising this important point. We would like to clarify that the analyses were not limited to a single, selectively reported association. The relationship between the MD and the anterior pulvinar was evaluated while explicitly accounting for other pulvinar subdivisions, as well as for thalamic input outside the pulvinar.

Specifically, potential contributions from other pulvinar nuclei were controlled by including them in the regression model (Fig. 2 in the manuscript), and the LGN was included as an additional control region. These analyses therefore test whether the MD–anterior pulvinar association is specific, rather than reflecting a more general thalamic or pulvinar-wide effect. With respect to hypothesis testing, the study was explicitly hypothesis-driven, grounded in functional evidence motivating a specific prediction about MD–anterior pulvinar interactions.

Still, in response to the reviewer’s suggestion, we further examined pairwise relationships among thalamic subregions. Specifically, we assessed the association between the MD and each pulvinar subdivision using partial correlations, controlling for the remaining pulvinar subdivisions in each analysis. For example, the partial correlation between the MD and the lateral pulvinar was computed while controlling for the activation of the anterior, inferior, and medial pulvinar subdivisions.

The partial correlation between the MD and the anterior pulvinar was consistent across all four trials of threat learning, whereas the other pulvinar subdivisions did not exhibit a consistent pattern. To evaluate the robustness of these effects, we applied a bootstrap procedure (10,000 resamples) to estimate 95% confidence intervals for each partial correlation. As presented in Figure 4b, only the anterior pulvinar–MD association remained robust, with confidence intervals that did not include zero. In contrast, the confidence intervals for most other pulvinar subdivisions included zero, indicating non-robust associations.

(5) The manuscript does not contain a limitations subsection. Practically every study has limitations, and this one is not an exception. Better to tell the limitations to the readers upfront so they can factor them into their evaluation of the relevance of the manuscript and reported evidence.

We thank the reviewer for this constructive suggestion. While the original manuscript already discussed key limitations in the Discussion section (page 36; e.g., “Although distinct thalamic roles in threat learning have been proposed, fMRI data do not fully capture the complexity of this structure…”), we agree that these considerations would benefit from clearer organization and visibility.

To address this point directly, we have now added a dedicated “Limitations and Future Directions” subsection to the manuscript. This subsection explicitly summarizes the principal limitations of the study—including methodological constraints of fMRI and anatomical resolution—and outlines specific avenues for future research to address them. This change makes the limitations more transparent and allows readers to more easily incorporate them into their evaluation of the findings.

(6) Data should be made available to the scientific community. Code too. Even if you just used standard fMRI toolboxes, any code used to run analyses will be helpful to the community, or if someone decides to try to replicate your findings.

We thank the reviewer for this important suggestion and fully agree with the value of data and code sharing for transparency and reproducibility.

The data supporting the findings of this study are derived from a larger, actively used database that is currently involved in ongoing projects. For this reason, the full dataset cannot yet be publicly released. However, the data underlying the reported analyses are available upon reasonable request from the corresponding author, subject to standard data-use agreements.

To facilitate reproducibility, all analysis scripts and pipelines used in this study—including preprocessing and analysis workflows implemented in SPM12, and CONN—are available upon request and can be shared with researchers seeking to replicate or extend the reported findings.

We have clarified this data and code availability statement in the manuscript (page 46).

Despite these weaknesses and what can be derived from them, this manuscript constitutes a valuable contribution to the field to start characterizing and conceptualizing the involvement of thalamic nuclei and their interactions with other brain regions in the associative threat learning circuitries. It also paves the road for further testing of the functional dynamics among these regions and circuitries, and modeling testing.

Recommendations for the authors:

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and, where appropriate, 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

We thank the editors for this important note. Full statistical reporting, including test statistics, degrees of freedom, exact (raw and corrected) p-values, effect sizes, and 95% confidence intervals, is provided for all key analyses in Supplementary Tables 1–9. In addition, uncertainty estimates and major statistics tests are now explicitly reported throughout the main text, as recommended by the reviewers, irrespective of statistical significance.

During this revision process, we conducted a comprehensive internal consistency check of all reported statistics and figure annotations. We identified and corrected minor discrepancies between some statistical annotations in the figures and the corresponding results reported in the Supplementary Tables. All figures have now been updated to ensure full consistency with the reported analyses. These corrections do not alter the results or conclusions of the study.

Reviewer #1 (Recommendations for the authors):

(1) What is the significance of using two different head coils? Were the data comparable from each coil? How did the authors determine this?

We thank the reviewer for this important question. Data were acquired using two different receiver head coils across participants. Receiver coils primarily influence signal-to-noise ratio (SNR) and spatial sensitivity profiles, rather than the physiological basis of the BOLD response itself (Triantafyllou et al., 2011).

Importantly, all analyses were based on within-subject contrasts (CS+ vs. CS−), which are robust to global signal scaling differences that may arise from coil sensitivity variations. In addition, standard preprocessing procedures—including intensity normalization, spatial normalization, and nuisance regression—further minimized potential coil-related variability.

To empirically evaluate whether acquisition differences influenced our results, we conducted a repeated-measures ANOVA testing the Trial × CS × Site interaction (where Site reflects acquisition location and associated scanning setup, including receiver coil configuration) during fear conditioning (N = 293). As shown in Author response table 2, none of the thalamic nuclei demonstrated a significant interaction effect, and all effect sizes were negligible (η²p ≤ .01)

Author response table 2.

Repeated-Measures ANOVA results for the Trial X CS X site interaction across all relevant thalamic nuclei during fear conditioning.

(2) Why were the data smoothed? This could have a negative impact on the specificity of the signals averaged within the pre-defined thalamic ROIs.

Spatial smoothing was applied to improve signal-to-noise ratio and statistical stability in small, deep thalamic subregions, which are particularly susceptible to noise. We acknowledge that smoothing can reduce spatial specificity. However, our analyses were based on anatomically predefined thalamic ROIs and focused on average activation within each region rather than voxel-wise localization. Under this approach, modest smoothing (i.e., a 6-mm full-width at half-maximum smoothing kernel, rather than the commonly used 8-mm kernel) primarily increases reliability while any signal mixing across adjacent regions would be expected to reduce regional specificity and bias effects toward the null, rather than produce spurious or false-positive differences.

Additionally, we conducted robustness analyses to examine whether spatial smoothing artificially influenced our results. Specifically, we subdivided the mediodorsal thalamus into medial and lateral anatomical regions and compared activation across these subregions. The activation patterns were comparable across both subdivisions, indicating that the observed mediodorsal thalamus effect is unlikely to reflect boundary spillover resulting from smoothing. If smoothing had driven the effect, we would expect differential signal patterns across the subdivisions rather than comparable activation. (See full response to Weakness C, Reviewer 3, as well as Author response image 1 and Author response table 1 in our response).

(3) Did the authors consider using any null models to determine whether the observed PPI results could have been observed by chance? E.g., block-resampling nulls scramble temporal order while preserving temporal autocorrelation, and can determine whether subtle differences in autocorrelation across regions can give rise to the observed signatures.

We thank the reviewer for this thoughtful suggestion. All PPI analyses were conducted using the default CONN toolbox pipeline. In this framework, PPI effects are estimated within a GLM at the first level following standard denoising procedures that reduce motion- and physiology-related variance and apply temporal filtering. Importantly, PPI effects are modeled as subject-level contrast terms rather than computed from raw timeseries correlations.

Group-level inference was performed on these subject-level contrast estimates using paired t-tests with FDR correction across regions. To further assess whether the observed effects could arise by chance, we additionally performed 10,000 bootstrap resamples of the CS+ vs. CS− differences to evaluate the stability of the effects. While we did not implement explicit block-resampling null models that preserve temporal autocorrelation, the combination of first-level GLM modeling following denoising, large sample size (N ≈ 300), and convergent inferential and resampling procedures provides a rigorous and standard assessment of PPI effects. We have revised the manuscript to clarify these procedures and their rationale.

We added this language to directly address the reviewer’s concern and revised the connectivity analyses section to clarify the workflow (page 44):

“Following standard denoising procedures—including regression of motion- and physiology-related confounds and temporal filtering—condition-dependent connectivity effects were inferred from subjectlevel generalized psychophysiological interaction (gPPI) contrast estimates rather than from raw timeseries correlations. This GLM-based framework reduces the likelihood that observed PPI effects reflect differences in temporal autocorrelation or spectral properties across regions rather than genuine task-dependent interactions.”

(4) The authors may wish to report results in text, as there are currently many demonstrative statements that are not associated with requisite uncertainty estimates, making inference challenging.

We thank the reviewer for this helpful suggestion. We have revised the Results section to explicitly report statistical outcomes in the main text for all key findings, including appropriate uncertainty estimates (e.g., test statistics, effect sizes, and p-values) alongside demonstrative statements. This ensures that all inferences in the text are directly supported by quantitative evidence.

Additionally, the full statistical details, including test statistics, degrees of freedom, effect sizes, 95% confidence intervals, and both raw and FDR-corrected p-values, are provided in Supplementary Tables 1–9. These changes improve clarity and transparency while avoiding redundancy. Newly added text in the Results section is highlighted in green.

(5) I could not find any information about the EBICglasso model in the Methods section, nor information about how the centrality measures were estimated. Given the lack of transparency, I recommend down-weighting the often overly-strong language regarding the conclusions of this analysis.

We have revised and added these details along with other details to the Statistical tests section on pages 42-44:

“Statistical tests

All statistical tests were conducted using JASP versions 0.18.3 and 0.19.3(JASP Team, 2024).

Activation Differences across all phases of threat learning

In each threat learning phase, we used paired t-tests to examen the differences in activation of the thalamic nuclei in response to CS+ vs. CS- at the block level (average activation across trials), and 2x2 RM-ANOVA to estimate the differences in activation at the trial-wise level. Assumptions of sphericity were checked, and Greenhouse-Geisser corrections were applied where necessary. This model was followed by post hoc tests to estimate the differences at the trial level and False discovery rate (FDR) correction was applied for each question.

Network analyses of the within pulvinar relationships during conditioning

The network analyses examined functional relationships between pulvinar divisions. Nodes corresponded to block-level activation estimates of the CS+ minus CS− contrast for each pulvinar division, yielding four nodes (one per division). Networks were estimated using a Gaussian graphical model with EBICglasso (LASSO regularization) based on Pearson correlation matrices, with the EBIC tuning parameter set to γ = 0.5. Edge weights represent partial correlations.

Three centrality measures were computed on the estimated weighted partial-correlation network: node strength, defined as the sum of the absolute edge weights directly connected to a node; closeness, defined as the inverse of the average shortest path length from a node to all other nodes; and betweenness, defined as the proportion of shortest paths between all pairs of nodes that pass through a given node. Shortest paths were computed using inverse edge weights, consistent with standard practice for weighted networks. Centrality indices were normalized.

Network accuracy and centrality stability were assessed using nonparametric bootstrapping (10,000 iterations) to estimate confidence intervals for edge weights and centrality measures. All analyses were conducted in JASP (versions 0.18.3 and 0.19.3) using default settings unless otherwise specified, following the procedures described in Epskamp, Borsboom, and Fried (2018).

Mediation analyses of within pulvinar relationships during conditioning

Mediation models of the relationships between the activations in pulvinar divisions were estimated using the lavaan package (Rosseel, 2012) with maximum likelihood estimation. All variables were zstandardized prior to analysis. Block-level activation estimates from the inferior and lateral pulvinar were entered as predictors, activation in the medial pulvinar was specified as the mediator, and activation in the anterior pulvinar was specified as the outcome variable.

To assess the robustness and generalizability of the mediation effects, we conducted 3-fold crossvalidation. The full sample (N = 293) was randomly partitioned into three non-overlapping sub-samples (n = 91, 96, and 106). In each iteration, the mediation model was estimated in one sub-sample, while the remaining sub-samples were used to assess the stability of parameter estimates and indirect effects. This procedure resulted in six cross-validation iterations, allowing evaluation of whether the direction and magnitude of the indirect effect were consistent across independent subsets of the data. Mediation models were estimated using the lavaan package (Rosseel, 2012) with maximum likelihood estimation. Indirect effects were evaluated using bias-corrected percentile bootstrap confidence intervals based on 10,000 resamples, as recommended by Biesanz, Falk, and Savalei (2010). An indirect effect was considered significant when the 95% confidence interval did not include zero (p < 0.05).”

(6) Bar plots are not effective ways to report group-level data. I recommend replacing all bar plots with visualisations that expose the distribution of the data, such as a violin plot or a raincloud plot.

We thank the reviewer for this suggestion. In general, we agree that visualizations exposing the full data distribution can be highly informative, and we therefore present distribution-based plots for several analyses (e.g., connectivity results). However, for the activation analyses, our primary goal was to highlight trial-to-trial changes and overall patterns across conditions, rather than the distribution of individual data points per se. For this purpose, bar plots provide a clearer representation of the directional effects and facilitate comparison across trials and conditions.

(7) The thought bubbles are atypical of scientific figures.

The figure has been revised to remove the thought bubbles.

(8) Figure 7 - there are many connections not shown in this figure, suggesting that it is sufficiently oversimplified as to be potentially misleading. For instance, the authors offer no anatomical connections between pulvinar and the cortical hierarchy; however, these connections are ample and (likely) highly important for the functionality assessed here. Similarly, there is no room in the figure for the integration of the shock stimuli (presumably via the spinothalamic tract) and the visual stimuli (via the retina/LGn).

We agree that the pulvinar has extensive cortical and sensory input/output connections that are not depicted in Figure 7. Our intention was not to provide a complete anatomical wiring diagram, but rather a simplified functional model derived from observed statistical dependencies. We have revised the figure and added an explicit note to the legend clarifying that pulvinar–cortical and sensory pathways (e.g., retina/LGN and spinothalamic inputs) are intentionally omitted due to incomplete subnuclear-level anatomical characterization, and that their omission should not be interpreted as a lack of importance. We added this to Figure 7 legend:

“Note (panel a):

Known pulvinar–cortical connections, as well as sensory input pathways (e.g., visual inputs via the retina/LGN and nociceptive inputs via the spinothalamic tract), are not explicitly shown. These connections are well established anatomically but were omitted due to their heterogeneity and incomplete characterization at the level of pulvinar subnuclei. Their absence should not be interpreted as a lack of anatomical or functional relevance.”

Reviewer #2 (Recommendations for the authors):

(1) It's somewhat confusing that Figures 1,4,5 D and E are not in the text until later in the results section. Perhaps these should be presented in the figures in the same order they are discussed in the text, although this is a stylistic issue.

We thank the reviewer for this comment. To improve clarity and align the figures with the structure of the Results section, we reorganized the figures. Specifically, we added a new figure (Figure 7) that consolidates all connectivity analyses. Figures 1, 4, and 5 now focus exclusively on activation results, while Figure 7 presents connectivity results only. This reorganization allows the figures to follow the flow of the text more closely and makes the narrative of each figure clearer.

(2) Stylistic: I would strongly recommend adding n numbers and describing the basics of statistical tests used and how multiple comparisons were accounted for in the legend for Figures 1,4, and 5.

We thank the reviewer for this recommendation. We have added the sample sizes (n) and brief descriptions of the statistical tests used, including how multiple comparisons were handled, to the legends of Figures 1, 4, and 5. In addition, we direct the reader to the Supplementary Tables, which were submitted with the original manuscript and provide full statistical details, including test statistics (t, F), degrees of freedom, effect sizes, 95% confidence intervals, raw p values, and corrected p values. Finally, we further elaborated on the statistical tests on pages 42–44, as detailed in our response to Recommendation 5 (Reviewer 1).

Reviewer #3 (Recommendations for the authors):

As previously indicated, please note that no information is included in the manuscript about data and code availability. Although you mainly use toolboxes for data analyses, any script(s) that you have used to run things would be great to upload for reproducibility purposes.

Also, it would be good to include a limitations subsection in the manuscript.

Thank you for these recommendations. We added limitations subsection to the manuscript. See our responses under Comments 5 and 6 (Reviewer 3, Public Review).

In terms of data analyses:

(1) It would be ideal if you quantify in-scanner motion for the different conditions to see if there were no differences in motion due to the task.

Head motion was estimated at each time point as part of standard preprocessing, and motion parameters were included as nuisance regressors in all first-level models. Because motion estimates are defined per volume rather than per experimental condition, condition-specific motion metrics were not explicitly computed. Importantly, this approach removes motion-related variance uniformly across the time series and therefore controls for potential motion effects across all task conditions. Any residual motion would be expected to increase noise rather than systematically bias condition contrasts.

(2) You also may want to indicate if normalization followed the SPM 12 default and the data was resampled to 2 x 2 x 2 mm, or kept the same. It is not stated in the data preprocessing subsection of the methods.

We thank the reviewer for this suggestion. We have now clarified this point in the manuscript (page 41):

“In addition, spatial normalization was performed with data normalized to Montreal Neurological Institute (MNI) space and resampled to a 2 × 2 × 2 mm³ voxel grid, followed by spatial smoothing with a 6-mm full-width at half-maximum Gaussian kernel.”

(3) It is important to indicate how many subjects went into each analysis. Also, it is not clear, based on the current methods section, how many observations per condition were used. That can be reported in the text or the figures.

We thank the reviewer for this comment. This information has now been added to the Methods section and the relevant figure legends, as described in our response to Comment 2 (Reviewer 3, Public Review).

References

Triantafyllou C, Polimeni JR, Wald LL. 2011. Physiological noise and signal-to-noise ratio in fMRI with multi-channel array coils. NeuroImage 55:597–606. DOI: https://doi.org/10.1016/j.neuroimage.2010.11.084, PMID: 21167946

Author response:

eLife Assessment

This manuscript reports an important study in which the authors apply smFRET imaging to probe HIV-1 Env conformational dynamics in the presence of antibodies. Previous implementations of smFRET imaging of HIV-1 Env, which focus on gp120 conformation, have yielded limited information on antibodies that target gp41. Through the cutting-edge application of smFRET imaging, the study provides convincing insights into the mechanisms of action of relevant antibodies.

We appreciate this positive assessment and thank the reviewers for their time and constructive comments. We will make the following changes in the revised manuscript.

(1) Clarify the distinction between suppression efficiency and functional cost.

(2) Add controls: smFRET experiments in the presence of monovalent 10E8.4 and iMab individually and compare results with the bivalent 10E8.4/iMab that we currently have.

(3) Increase the number of repeats in neutralization experiments to reduce variability and, where feasible, perform infectivity and neutralization assays after click chemistry labeling.

(4) Add discussion on conformational populations probed by smFRET versus structural analyses, Env conformational heterogeneity, ligand effects, and how these approaches complement each other.

(5) Further clarify the assignments of multiple conformational states by smFRET, the heterogeneity of Env spikes and virion morphology by cryoET, and the focus of the current smFRET-focused storyline.

Please find below our provisional responses to the public reviews. We will provide detailed point-by-point responses upon submission of the revised manuscript.

Public Reviews:

Reviewer #1 (Public review):

The authors have considered a panel of antibodies that target epitopes at the gp120/gp41 interface (8ANC195 and PGT151), the fusion peptide in the gp41 domain (VRC34), and the MPER region of gp41 (DH511.2_K3 and VRC42). They also investigate 10E8.4/iMab, which is an engineered bispecific antibody that targets the MPER and the CD4 receptor. On a technical note, they have applied a double amber codon-readthrough strategy to incorporate the non-natural TCO*A amino acid, which gets labeled through click chemistry. This approach should result in less disruption of the native Env structure as compared to the peptide insertion previously used for smFRET imaging of Env. Furthermore, previous implementations of smFRET imaging of HIV-1 Env, which focus on gp120 conformation, have yielded limited information on antibodies that target gp41. Altogether, through the cutting-edge application of smFRET imaging, the study provides novel insights into the mechanisms of action of interesting and clinically relevant antibodies.