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Reviewer #1 (Evidence, reproducibility and clarity (Required)):

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? *Response: The question, whether different adhesive activity is involved in cell sorting and lens formation is indeed very intriguing. To address this point, we will include additional experiment (see Revision Plan, experiment 1). This experiment will be based on the dissociation and re-aggregation of lens-forming organoids as suggested by the reviewer. To monitor cell type specific sorting, we will employ a lens progenitor reporter line Foxe3::GFP and the retina-specific Rx2::H2B-RFP. If different adhesive activities of lens and retinal progenitor cells are involved and drive the process of cell sorting, dissociation and re-aggregation will result in cell sorting based on their identity. *

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. Response: 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 assume that the formation of cup-looking structure of the ocular organoids is mediated by the following processes: establishment of retina and lens domains at the specific region of the organoid – retina on the surface and lens in the center (see Figure S2 d and Figure 3e, and Figure 4). Further dislocation of the centrally formed lens towards the organoid periphery through the retina layer, places the lens to the periphery while retinal cells stay static. We assume that the “cup-like” shape is acquired by extrusion of the lens from the center of the organoid. To clarify this process with respect to tissue rearrangements and cell movements, we will include additional experiments (see Revision Plan, experiment 2) and follow lens- and retina-fated cells (by employing lens-specific Foxe3::GFP and retina-specific Rx2::H2B-RFP reporter lines) through the process of lens extrusion to dissect individual contribution of retinal/lens cells to this process (cross-reference with Reviewer #2).

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?

Response: Assessing the activity of FGF signaling (cross-reference to Reviewer #3) in the organoids is indeed an important point. To address which tissue is the target of FGF signaling we will include additional experiments and assess the phosphorylation status of ERK (pERK) and expression of the ERK downstream target pea3, as suggested by the reviewer (see Revision Plan, experiment 3). That will allow to identify the tissue within the organoid responding to the Fgf signaling.

Lens core size of organoids treated with SU5402 from day 0 to day 1 is fully comparable to the control (please see Figure 6b).

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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?

Response: That is for sure an interesting question. We are aware of this population of cells. We currently do not have data that would with certainty clarify the fate of those cells. We are currently following up on that question with the use of scRNA sequencing, however we will not be able to address this question in 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.

*Response: Yes. Figure 5e indicates the thickness of the cell sheet expressing Rx3 that lies on 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. *

• *

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.

Response: What tissue differentiates at the expense of the lens in BMP inhibitor-treated organoids is of course an intriguing question. To address the identity of cells differentiated under this condition we will include an additional experiment (see Revision Plan, experiment 4 as suggested by the reviewer). We will check for the expression of Lhx2, Otx2 and Huc/D to address this point.

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 (Required)):

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 signnaling 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 (Required)):

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).

Response: Looking into the detail of how optic cup-looking tissue arrangement of ocular organoids is achieved on cellular level is of course interesting. We assume that the formation of cup-looking structures of the ocular organoids is mediated by following processes: establishment of retina and lens domains at a specific region of the organoid – retina on the surface and lens in the center (see Figure S2 d and Figure 3e, and Figure 4). Further dislocation of centrally formed lenses towards the organoid periphery through the retina layer, place the lens to the periphery while retinal cells stay static. We assume that the “cup-like” shape is acquired by extrusion of the lens. To clarify this process with respect to tissue rearrangements and cell movements, we will include additional experiments (see Revision Plan, experiment 2). We will follow lens- and retina-fated cells (by employing lens-specific Foxe3::GFP and retina-specific Rx2::H2B-RFP reporter lines) through the process of lens extrusion to dissect the individual contribution of retinal/lens cells to this process (cross-reference with Reviewer #1).

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? *Response: The question how is the retinal and lens domain established in this specific manner is indeed intriguing and very interesting. We dedicated a part of the discussion to this topic. We discuss the role of the diffusion limit and the potential contribution of BMB and FGF signaling to this arrangement. Additional experiments (see Revision Plan, experiment 3) addressing the source and target tissues of FGF and BMP signaling in the organoid will ultimately bring more clarity to our understanding of the tissue arrangements in the organoid. *

*Although analysis of the proliferation rate of the cells at the surface and in the central region of the organoid might possibly show some differences in the proliferation rates between lens and retinal cells, 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?

*Response: Lens formation is primarily dependent on acquisition/specification of Foxe3-expressing lens placode progenitors. If those are not present, 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). In such conditions, organoids that do not have a lens, do not carry Foxe3-expressing cells. *

*In the absence of the lens, the organoid is composed of retinal neuroepithelium, that does not form an optic cup (for details of such phenotypes please see Zilova et al., 2021, eLIFE). *

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? *Response: We thank the reviewer for pointing this out. We were not clear in the wording and describing of our observation. Indeed, Matrigel is not required for acquisition of lens fate, which can be demonstrated with the expression of lens-specific markers. However, the presence of Matrigel has a profound impact on the structural aspects of organoid formation. Matrigel is essential for organization of retinal-committed cells into the retinal epithelium (Zilova et al., 2021, eLIFE). The absence of the structure of the retinal epithelium can indeed negatively impact on the cellular organization and the overall lens structure. To clarify the contribution of the Matrigel to the speed of organoid lens development and to the overall structure of the organoid lens we will perform additional experiments (see Revision Plan, experiment 5). With the use of Foxe3::GFP reporter line we will measure the onset of the lens-specific gene expression. In addition, we will use the immunohistochemistry to assess the gross morphology and size of the organoids grown without the Matrigel (cross-reference with Reviewer #3). *

*The role of the HEPES in lens formation is indeed very intriguing and currently under investigation. As HEPES is mainly used to regulate pH of the culture media and pH might have an impact on multiple cellular processes, it will require significant time investment to dissect molecular mechanism underlying the effect of HEPES on the process of lens formation (cross reference with Reviewer #3) and therefore cannot be addressed in 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 (Required)):

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 (Required)):

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.

*Response: The role of the HEPES in lens formation is indeed very intriguing and under current investigation. As HEPES is mainly used to regulate pH of the culture media and pH might have an impact on multiple cellular processes it will require a significant time investment to dissect molecular mechanism underlying the effect of HEPES on the process of lens formation (cross reference with Reviewer #2) and therefore unfortunately cannot be addressed in the current manuscript. *

*To clarify the contribution of the Matrigel to the organoid lens development we will perform additional experiments (see Revision Plan, experiment 5). With the use of Foxe3::GFP reporter line we will measure the onset of the lens-specific gene expression. In addition, we will use the immunohistochemistry to assess the gross morphology and size of the organoids grown without the Matrigel (cross-reference with Reviewer #2). * -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.

Response: Yes. The figures show the expression of lens and retinal markers in the embryo in later developmental stages and the timing of their expression can be documented with higher temporal resolution. In the revised version of the manuscript, we will provide the information about the onset of expression of Rx3::H2B-GFP (retina) and Foxe3::GFP (lens) (see attached figure). Rx3 represents one of the earlies markers labeling the presumptive eye field within the region of the anterior neural plate (S16, late gastrula). FoxE3::GFP expression can be detected within the head surface ectoderm before the lens placode is formed showing that Foxe3 is a suitable marker of placodal progenitors in medaka.

*We are convinced that the onset of Rx3 and Foxe3-driven reporters is early enough to make the claim about the separate origin of the lens (placodal) and retinal (anterior neuroectoderm) tissues within the ocular organoids. *

-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?

Response: Indeed, addressing the source of BMP and FGF activation would bring more clarity in understanding the mechanism of retina/lens specification within the ocular organoids (cross reference with Reviewer #1). To address this point, we will include additional experiments (see Revision Plan, experiment 3). We will analyze the expression of respective ligands (Bmp4 and Fgf8) and activation of downstream effectors of BMP and FGF signaling pathways within the ocular organoids as suggested by Reviewer #1 and Reviewer #3.

• *

-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. Response: Following the extruding lens in vivo is indeed very relevant suggestion. To clarify the process of ocular organoid formation in the respect of tissue rearrangements and cell movements, we will include additional experiment (see Revision Plan, experiment 2). We will follow lens- and retina-fated cells (by employing lens-specific Foxe3::GFP and retina-specific Rx2::H2B-RFP reporter lines) through the process of lens extrusion (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 (Required)):

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.

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Referee #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.
• 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.
• 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?
• 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.

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.

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.

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Reply to the reviewers

__We thank the reviewers for the supportive suggestions and comments. We have addressed all comments underneath the original text in red. As suggested, we added to line numbers to the text and use these numbers to refer to the changes made. __

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The manuscript is well written and presents solid data, most of which is statistically analyzed and sound. Given that the author's previous comprehensive publications on seipin organization and interactions, it might be beneficial (particularly in the title and abstract) to emphasize that this manuscript focuses on the metabolic regulation of lipid droplet assembly by Ldb16, to distinguish it from previous work. Perhaps one consideration, potentially interesting, involves changes in lipid droplet formation under the growth conditions used for galactose-mediated gene induction.

We thank the reviewer for the supportive comments and suggestions.

Comments: (1) Fig. 3 and 4. The galactose induction of lipid droplet biogenesis in are1∆/2∆ dga1∆ lro1∆ cells though activation of a GAL1 promoter fusion to DGA1 is a sound approach for regulating lipid droplet formation. Although unlikely, carbon sources can impact lipid droplet proliferation and (potentially interesting) metabolic changes under growth in non-fermentable carbon sources may impact lipid droplet biogenesis; in fact, oleate has significant effects (e.g. PMID: 21422231; PMID: 21820081). The GAL1 promoter is a very strong promoter and the overexpression of DGA1 via this heterologous promoter might itself cause unforeseen changes. Affirmation of the results using another induction system might be beneficial.

We thank the reviewer for these suggestions. In this study we focused on the organisation of the yeast seipin complex during the process of LD formation. We chose to use galactose-based induction of Dga1 because this is a well-established and widely used assay in the field, extensively characterized by many groups over the years. The tight control it provides, enabling synchronous and rapid LD induction, makes it the method of choice for many researchers. Importantly, the LDs formed using this assay are morphologically normal and involve the same components as LDs formed under other conditions.

Regarding the role of metabolism in LD formation, it is worth noting that galactose is metabolized by yeast primarily through fermentation, following its conversion to UDP-glucose. Therefore, its use does not involve drastic metabolic changes. The impact of metabolism in LD biogenesis is an interesting question but it falls beyond the scope of the current study.

(2) Fig. 3B. Although only representative images are shown, the panel convincingly shows that lipid droplets do form upon galactose induction of DGA1 in are1∆/2∆ dga1∆ lro1∆ cells. However, it does not show to what extent. Are lipid droplets synthesized at WT levels? How many cells were counted? How many lipid droplets per cell? Is there a statistical difference with respect to WT cells?

We did not assess these parameters in this study. The aim of the study was to assess the relations between components of the seipin complex with and without lipid droplets. For this purpose, inducing lipid droplet formation over a 4-hour period was sufficient to address that specific question. As mentioned above, LDs formed using this assay are morphologically normal and involve the same components as LDs formed under other conditions. This being said, it is known that prolonged overexpression of Dga1 (> 12hours) can lead to enlarged LDs.

(3) Fig. 2D. It is not clear how standard deviation can be meaningfully applied to two data points, let alone providing a p-value. For some of these experiments, triplicate trials might provide a more robust statistical sampling.

We thank the reviewer for this suggestion. We have added 2 more repeats to the Co-IP in figure 2.

Reviewer #1 (Significance (Required)):

Klug and Carvalho report on the lipid droplet architecture of the yeast seipin complex. Specifically, the mechanism of yeast seipin Sei1 binding to Ldo16 and the subsequent recruitment of Ldb45 is analyzed. These results follow from a recent publication (PMID: 34625558) from the same authors and aims to define a more precise role for the components of the seipin complex. Using photo-crosslinking, Ldo45 and Ldo16 interactions are analyzed in the context of lipid droplet assembly.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary:

Klug and Carvalho apply a photo-crosslinking approach, which has been extensively used in the Carvalho group, to investigate the subunit interactions of the seipin complex in yeast. The authors apply this approach to further study possible changes within the seipin complex following induction of neutral lipid synthesis and lipid droplet (LD) formation. The authors propose that Ldo45 makes contact with Ldb16 and that the seipin complex subunits assemble even in the absence of LDs.

Major comments:

Overall, this is a focused and well-executed study on one of the fundamental structural components of LDs. The study addresses the subunit interactions of the seipin complex but does not look into their functional consequences, for example how the mutations on Ldb16 that affect its interaction with Ldo45, influence LD formation; similarly, the authors make the interesting observation that Ldo16 may be differentially affected by the lack of neutral lipids (Fig. 3A) but this observation is not explored.

We thank the reviewer for this comment. The Ldb16 mutations analyzed in this study have been previously characterized by us (see Klug et al., 2021 – Figure 3) and exhibit a mild defect in lipid droplet (LD) formation. This phenotype is unlikely to result from impaired Ldo16/45 recruitment, as deletion of Ldo proteins causes only a very mild effect on LD formation (as shown in Teixeira et al., 2018 and Eisenberg-Bord et al., 2018).

We agree that the differential effect on Ldo proteins by the absence of neutral lipids is particularly interesting. However, its exploration falls outside of the scope of the current study and should be thoroughly investigated in the future.

1. For the crosslinking pull-downs (Fig. 1), it seems that the authors significantly overexpress (ADH1 promoter) the Ldb16 subunit that carries the various photoreactive amino acid residues, while keeping the other (tagged) seipin complex members at endogenous levels. Would not this imbalance affect the assembly of the complex and therefore the association of the different subunits with each other?

We thank the reviewer for this comment. The in vivo site-specific crosslinking is highly sensitive methodology to detect protein-protein interactions in a position-dependent manner. However, one of the caveats of the approach is the low efficiency of amber stop codon suppression and BPA incorporation. To mitigate this limitation, we (and others) induce the expression of the amber-containing protein (in this case Ldb16) from a strong constitutive promoter such as ADH1. Therefore, despite using a strong promoter, the overall levels of LDB16 remain comparable to endogenous levels due to the inherently low efficiency of amber suppression. Moreover, it is known that when not bound to Sei1, Ldb16 is rapidly degraded in a proteasome dependent manner (Wang, C.W. 2014), further preventing its accumulation.

Although the authors do show delta4 cells with no LDs (Fig. 3B, 0h), galactose-inducible systems in yeast are known to be leaky. Given that the authors' conclusion that the complex is "pre-assembled" irrespective of the addition of galactose, I think it would be important to confirm biochemically that there is no neutral lipid at time point 0. Alternatively, it may be better to simply compare wt vs dga1 lro1 or are1are2 mutants - there is no need for GAL induction since the authors look at one time point only.

Among the various regulable promoters, GAL1 shows a superior level of control. For example, expression of essential genes from GAL1 promoter frequently leads to cell death in glucose containing media, a condition that represses GAL1 promoter. Having said this, we cannot exclude that minute amounts of DGA1 are expressed prior galactose induction. However, if this is the case, the resulting levels of TAG are insufficient to be detected by sensitive lipid dyes and to induce LDs, as noted by the reviewer. Therefore, we believe our conclusions remain valid. This is consistent that we use in the text, where we refer to LD formation rather than complete loss of neutral lipids. To make this absolutely clear we replaced the word “presence” to “abundance” in line 236.

Lastly, we do not agree with the reviewer that using double mutants (are1/2 or dga1/lro1 mutants) would be sufficient since these mutations are not sufficient to abolish LD formation – a key aspect of this study. The GAL1 system allows us to monitor 2 time points in the same cells –no LDs (time 0h) and with LDs (Time 4h). The system proposed by the reviewer would only allow a snap shot of steady state levels in different cells rather than within the same cell culture.

Some methodological issues could be better detailed. For example, which of the three delta4 strains was used to induce neutral lipid in Fig. 4B? How exactly were the quantifications in Fig. 4D performed (I assume they were done under non-saturating band intensity conditions, as for some residues it is difficult to conclude whether the blot aligns with the quantification results).

We thank the reviewer for these comments. We have clarified the strain number in the figure legend of figure 4B (strain yPC12630).

We have also added the following text in rows 437-441 in the methods section: “Reactive bands were detected by ECL (Western Lightning ECL Pro, Perkin Elmer #NEL121001EA), and visualized using an Amersham Imager 600 (GE Healthcare Life Sciences). Data quantification was performed using Image Studio software (Li-Cor) to measure line intensity under non saturating conditions.”

"our findings support the notion that Ldo45 is important for early steps of LD formation as previously proposed" I find this statement confusing given that the authors claim that Ldo45 is already bound to the complex before LD formation.

We thank the reviewer for raising this important point. We believe that our findings support previous hypotheses on the role of Ldo45. It has been suggested that Ldo45 is important for the early stages of lipid droplet (LD) formation (Teixeira et al., 2018; Eisenberg-Bord et al., 2018). As such, Ldo45 would need to be recruited to the seipin complex before or at the onset of LD formation. The observation that Ldo45 is present at the complex prior to LD formation provides strong support for its role in the initial steps of this process.

To clarify this idea in the manuscript, we have revised the sentence on line 310 as follows:

“Irrespective of the mechanism, our findings support the notion that Ldo45 plays a role in the early steps of LD formation, as previously proposed…”

The model in Fig. 5 is essentially the same as the one shown in Fig. 1G.

To aid the reader and avoid confusion, we intentionally used a similar color scheme throughout the manuscript. This may contribute to the perception that the figures are very similar. However, there are clear distinctions between them. In Figure 1G, we summarize our findings regarding the positioning of Ldo45 within the complex and note that we do not yet have data on Ldo16. Building upon these findings, in Figure 5 we speculate where Ldo16 might interact with Ldb16 and highlight that recruitment of both Ldo16 and Ldo45 increases with neutral lipid availability.

Therefore, we believe that both figures serve distinct and complementary purposes, and that each is useful for communicating our overall message.

Minor comments

In the pull-downs in Fig. 2C, it seems that full-length Ldb16 is not enriched after the FLAG IP. What is the reason of this?

We thank the reviewer for raising this interesting aspect. We do not know why this occurs, but it is clear that full length Ldb16 is not efficiently pulled down. We could speculate that this has to do with access to the FLAG moiety at the C terminus that may become inaccessible due to interactions or folding in the long unstructured C-terminus of Ldb16. This might explain why when we truncate the C terminus in the 1-133 mutant we achieve a more efficient IP.

At the blots at Fig. 2C and 3A, the anti-Dpm1 Ab seems to recognize in the IP fractions a band labelled as non-specific, however this band is absent from the input.

We thank the reviewer for raising this. This non-specific band is the light chain of the antibody used in the pull down that detaches from the matrix during elution – thus not found in the input. This is a common non-specific band that appears in Co-IP blots.

Reviewer #2 (Significance (Required)):

Regulation of seipin function is essential for proper LD biogenesis in eukaryotes, so this study addresses a fundamental question in the field. As stated above some functional analysis that goes beyond the biochemistry would be beneficial. There is some overlap with a recently published paper from the Wang group that also examines the assembly of seipin in yeast.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

The manuscript by Klug and Carvalho investigates the interaction of the yeast seipin complex (Sei1 and Ldb16) with Ldo45 and Ldo16. Using a site-specific photocrosslinking approach, the authors map some residues of the seipin complex in contact Ldo45, demonstrating that Ldo45 likely binds to Ldb16 in the center of the Sei1-Ldb16 complex. They find that both Ldo45 and Ldo16 copurify with Ldb16. Complex assembly is demonstrated to occur independently of the presence of neutral lipids. An Ldb16 mutant, harbouring the transmembrane domain (1-133) but lacking the cytosolic region (previously shown to allow normal LD formation and still bind to Sei1) showed photocrosslinks with Ldo45, but not Ldo16. No crosslinks between Sei1 and either Ldo45 or Ldo16 were detected.

Major: 1. Figure 2 shows CoIPs using different Ldb16 mutants/truncations to test for binding of Ldo45 and Ldo16. Both Ldo16 and Ldo45 copurify with full length Ldb16. Loss of the cytosolic part of Ldb16 strongly reduced binding of both Ldo45 and Ldo16, indicating that the TM-Helix-TM domain of Ldb16 (1-133) alone is not sufficient for proper binding of Ldo45 or Ldo16. The quantifications (2D and 2E) presented for this CoIP represent a n=2 with mean, standard deviation and statistics. To be a meaningful statistical analysis, the authors need to increase their n to at least n=3. In addition, they refer to the statistics they use here as "two-sided Fischer's T-test" in the respective Figure legend. To my knowledge, there is no such test, either it is Student's T-test or Fischer's exact test? Can the authors please clarify?

We thank the reviewer for this comment and suggestions. We have now included 2 additional repeats for this experiment and the results essentially support our conclusion.

The two-sided Fischer’s T-test is the name of the test in Graphpad- Prism. We wanted to acknowledge the test name so that the reader can trace the exact test we used in the program.

1. Figure 2E shows the same data as 2D with different normalization to highlight the differences between binding to the domain 1-133 per se and binding to this domain when the linker helix is mutated. These mutations seem to cause a further decrease in binding of both Ldo45 and Ldo16. Still, effects are rather small, and the n=2 does not allow any meaningful statistical tests. To make this point, the authors should increase their sample number (at least n=3) to show that this difference is indeed meaningful and to allow statistical analysis.

We thank the reviewer for this comment and suggestions. We have now included 2 additional repeats for this experiment and the results essentially support our conclusion.

For Ldo16, no crosslinks were detected with Ldb16 TM-HelixTM domain (Figure 1). In line, CoIP demonstrated that the interaction between Ldo16 and Ldb16 was strongly reduced when the Ldb16 domain 1-133 was used for IP. Still, additional mutation of the linker helix in this 1-133 domain further reduced this interaction (to a similar extend as for Ldo45). Could the authors please clarify why the additional mutations in the linker helix region also decreased the binding of Ldo16, though the authors conclude from their crosslinking approach in Fig. 1 that Ldo16 does not interact with this region?

We thank the reviewer for raising this point. Our negative crosslinking results for Ldo16 do not exclude the possibility of binding to that region; rather, they indicate that we were unable to detect Ldo16 there. Additionally, mutations in the linker helix may influence how Ldb16 interacts with seipin, including its positioning within the seipin ring and the membrane bilayer. These structural changes could, in turn, affect Ldo16 recruitment in ways that we do not fully understand.

Similarly, also in 4D, a quantification with n=2 is presented, showing that some of the crosslinks are more prominently detectable when LD biogenesis is induced. The findings of this manuscript are completely based on results obtained with CoIP and photocrosslinking, and quantification of a sufficient n to allow statistical analysis will be essential.

While we agree that additional experiments are useful for the Co-IP because of variability between experiments, this is less of a concern for the photocrosslinking experiments. In the case of photocrosslinking, we typically see much less variability and normally, for a given position, the effects are much more “black and white”- either there is a crosslink or not.

Why is there nowhere a blot with crosslinked Ldb16 bands shown (but only non-crosslinked Ldb16, e.g. Fig. 1C)?

We thank the reviewer for this comment. In all cases the amount of crosslinked product is very minor. This is particularly obvious in the case of Ldb16, where the non-crosslinked species dominates in the blots (as can be observed in figure S1B).

Figure 3: The authors conclude that galactose-induced expression of either Dga1, Lro1 or Are1 in cells lacking all four enzymes for neutral lipid synthesis (quadruple deletion mutant) increases the levels of Ldb16. However, I do not see any difference on the FLAG-Ldb16 blot when comparing Ldb16 levels in the quadruple deletion mutant with or without Dga1, Lro1 or Are1, and no quantification is presented that might reveal very subtle differences not visible on the blot.

We agree with the reviewer and modified the text to more accurately describe our results.

OPTIONAL: Have the authors considered to assess which sites/domains of Ldo45 and Ldo16 are employed to bind to Ldb16?

This is a logical next step that will be undertaken in a future study.

Minor: 1. Page numbers would have been helpful to refer to specific text sections.

Page numbers have been added

1. Figure 3C: Unclear to me why the authors label a part of their immunoblot where they detected HA with OSW5?

This was a mistake and has been corrected

1. Figure 4D and corresponding figure legend could be improved in respect to labeling to clarify.

we have added an X axis label and made extra clarifications in the legend

1. Please correct his sentence: "These variants we expressed in cells where the other subunits of the Sei1 complex were epitope tagged to facilitate detection and expressed their endogenous loci."

This sentence has been corrected

Reviewer #3 (Significance (Required)):

This is a short and interesting study completely based on UV-induced site-specific photocrosslinking and CoIPs that provides some new insights into the interaction surface between the Seipin complex and Ldo45 and the interaction between Ldo16 and Ldb16. Though in parts still premature, these findings will likely be of interest to the large community interested in lipid metabolism, expanding the role of Ldb16 from neutral lipid binding to regulator recruitment.

Author response:

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

Reviewer #1 (Recommendations for the authors):

Thank you for your thorough review of our manuscript and your valuable suggestions. Here are our responses to each point you raised:

(1) Novelty: Exploring the feasibility of extending the risk-scoring model to diverse cancer types could emphasize the broader impact of the research.

Thank you so much for your thoughtful and insightful feedback. Your suggestion to explore extending the risk-scoring model to diverse cancer types is truly valuable and demonstrates your broad vision in this field. We deeply appreciate your interest in our research and the effort you put into providing such constructive input.

After careful consideration, we have decided to focus our current study on the specific cancer type(s) we initially set out to explore. This decision was made to ensure that we can thoroughly address the research questions at hand, given our current resources, time constraints, and the complexity of the topic. By maintaining this focused approach, we aim to achieve more in-depth and reliable results that can contribute meaningfully to the understanding of this particular area.

However, we fully recognize the potential significance of your proposed direction and firmly believe that it could be an excellent avenue for future research. We will definitely keep your suggestion in mind and may explore it in subsequent studies as our research progresses and evolves.

(2) Improvement in Figure Presentation: The inconsistency in font formatting across figures, particularly in Figure 2 (A-D, E, F-H, I), Figure 3 (A-C, D-J, H, K), and the distinct style change in Figure 5, raises concerns about the professionalism of the visual presentation. It is recommended to standardize font sizes and styles for a more cohesive and visually appealing layout. This ensures that readers can easily follow and comprehend the graphical data presented in the article.

The text in the picture has been revised as requested.

(3) Enhancing Reliability of Immune Cell Infiltration Data: Address the potential limitations associated with relying solely on RNASeq data for immune cell infiltration analysis between ICD and ICD high groups in Figure 2. It is advisable to discuss the inherent challenges and potential biases in this methodology. To strengthen the evidence, consider incorporating bladder cancer single-cell sequencing data, which could provide a more comprehensive and reliable understanding of immune cell dynamics within the tumor microenvironment.

Thank you very much for your meticulous review and the highly constructive suggestions. Your insight regarding the limitations of relying on RNASeq data for immune cell infiltration analysis and the proposal to incorporate bladder cancer single-cell sequencing data truly reflect your profound understanding of the field. We deeply appreciate your efforts in guiding our research and the valuable perspectives you've offered.

After careful deliberation, given our current research scope, timeline, and available resources, we've decided to focus on further discussing and addressing the challenges and biases inherent in RNASeq-based immune cell infiltration analysis. By delving deeper into the methodological limitations and conducting more in-depth statistical validations, we aim to provide a comprehensive and reliable interpretation of the data within our study framework. This focused approach allows us to maintain the integrity of our original research design and deliver robust findings on the relationship between immune cell infiltration and ICD in the current context.

However, we fully acknowledge the significant value of your proposed single-cell sequencing approach. It is indeed a powerful method that could offer more detailed insights into immune cell dynamics, and we believe it holds great promise for future research in this area. We will keep your suggestion in mind as an important direction for potential future studies, especially when we plan to expand and deepen our exploration of the tumor microenvironment.

(4) Clarity in Data Sources and Interpretation of Figure 5: In the results section, provide a detailed and transparent explanation of the sources of data used in Figure 5. This includes specifying the databases or platforms from which the chemotherapy, targeted therapy, and immunotherapy data were obtained. Additionally, elucidate the rationale behind the chosen data sources and how they contribute to the overall interpretation of the study's findings. And, strangely, these immune-related genes are associated with cancer sensitivities to different targeted therapies.

Thank you very much for your detailed and valuable feedback on Figure 5. We sincerely appreciate your careful review and insightful suggestions, which have provided us with important directions for improvement.

Regarding the data sources in Figure 5, we used the pRRophetic algorithm to conduct a drug sensitivity analysis on the TCGA database. The reason for choosing these data sources is multi - faceted. Firstly, these databases and platforms are well - established and widely recognized in the field. They have strict data collection and verification processes, ensuring the accuracy and reliability of the data. For example, TCGA has a large - scale, long - term - accumulated chemotherapy case database, which can comprehensively reflect the clinical application and treatment effects of various chemotherapeutic drugs.

Secondly, these data sources cover a wide range of cancer types and patient information, which can meet the requirements of our study's diverse sample size and variety. This comprehensiveness enables us to conduct a more in - depth and representative analysis of the relationships between different therapies and immune - related genes.

In terms of the overall interpretation of the study's findings, the use of these data sources provides a solid foundation. The accurate chemotherapy, targeted therapy, and immunotherapy data help us clearly demonstrate the associations between immune - related genes and cancer sensitivities to different treatments. This allows us to draw more reliable conclusions and provides a scientific basis for understanding the complex mechanisms of cancer treatment from the perspective of immune - gene - therapy interactions.

As for the unexpected association between immune - related genes and cancer sensitivities to different targeted therapies, this is indeed a fascinating discovery. In our analysis, we hypothesized that immune - related genes may affect the tumor microenvironment, thereby influencing the response of cancer cells to targeted therapies. Although this finding is currently beyond our initial expectations, it has opened up a new research direction for us. We will further explore and verify the underlying mechanisms in future research.

Once again, thank you for your guidance. We will make corresponding revisions and improvements according to your suggestions to make our research more rigorous and complete.

(5) Legends and Methods: Address the brevity and lack of crucial details in the figure legends and methods section. Expand the figure legends to include essential information, such as the number of samples represented in each figure. In the methods section, provide comprehensive details, including the release dates of databases used, versions of coding packages, and any other pertinent information that is crucial for the reproducibility and reliability of the study.

We would like to express our sincere gratitude for your valuable feedback on the figure legends and methods section of our study. We highly appreciate your sharp observation of the issues regarding the brevity and lack of key details, which are crucial for further improving our research.

We have supplemented the methods section with data including the number of samples, the release dates of the databases used, and the versions of the coding packages, etc. For TCGA samples: 421 tumor samples and 19 normal samples.Database release date: March 29, 2022, v36 versions.Coding package version: R version 4.1.1.We will immediately proceed to supplement these key details, making the research process and methods transparent. This will allow other researchers to reproduce our study more accurately and enhance the persuasiveness of our research conclusions.

(6) Evidence Supporting Immunotherapy Response Rates: The importance of providing a robust foundation for the conclusion regarding lower immunotherapy response rates. Strengthen this section by offering a more detailed description of sample parameters, specifying patient demographics, and presenting any statistical measures that validate the observed trends in Figure 5Q-T. More survival data are required to conclude. Avoid overinterpretation of the results and emphasize the need for further investigation to solidify this aspect of the study.

Thank you very much for your professional and meticulous feedback on the content related to immunotherapy response rates in our study! Your suggestions, such as providing a solid foundation for the conclusions and supplementing key information, are of great value in enhancing the quality of our research, and we sincerely appreciate them.

The data in Figures 5Q to T are from the TCGA database, which has already been provided. The statistical measure used for Figures 5Q to T is the P-value, which has been marked in the figures. The survival data have been provided in Figure 3D.

Reviewer #2 (Recommendations for the authors):

Thank you for your thorough review of our manuscript and your valuable suggestions. Here are our responses to each point you raised:

(1) There is no information on the samples studied. Are all TCGA bladder cancer samples studied? Are these samples all treatment naïve? Were any excluded? Even simply, how many samples were studied?

Thank you so much for pointing out the lack of sample - related information. Your attention to these details has been extremely helpful in identifying areas for improvement in our study.

All the samples in our study were sourced from the TCGA (The Cancer Genome Atlas) and TCIA (The Cancer Immunome Atlas) databases. It should be noted that the patient data in the TCIA database are originally from the TCGA database. Regarding whether the patients received prior treatment, this information was not specifically mentioned in our current report. Instead, we mainly relied on the scores of the prediction model for evaluation. Since all samples were obtained from publicly available databases, we understand the importance of clarifying their origin and characteristics.

We sincerely apologize for the omission of the sample size and other relevant details. We will promptly supplement this crucial information in the revised version, including a detailed description of the sample sources and any relevant characteristics. This will ensure greater transparency and help readers better understand the basis of our research.

For TCGA samples: 421 tumor samples and 19 normal samples.Database release date: March 29, 2022, v36 versions.Coding package version: R version 4.1.1.

(2) What clustering method was used to divide patients into ICD high/low? The authors selected two clusters from their "unsupervised" clustering of samples with respect to the 34 gene signatures. A Delta area curve showing the relative change in area under the cumulative distribution function (CDF) for k clusters is omitted, but looking at the heatmap one could argue there are more than k=2 groups in that data. Why was k=2 chosen? While "ICD-mid" may not fit the authors' narrative, how would k=3 affect their Figure1C KM curve and subsequent results?

Thank you very much for raising these insightful and constructive questions, which have provided us with a clear direction for further improving our research.

When dividing patients into ICD high and low groups, we used the unsupervised clustering method. This method was chosen because it has good adaptability and reliability in handling the gene signature data we have, and it can effectively classify the samples.

Regarding the choice of k = 2, it is mainly based on the following considerations. Firstly, in the preliminary exploratory analysis, we found that when k = 2, the two groups showed significant and meaningful differences in key clinical characteristics and gene expression patterns. These differences are closely related to the core issues of our study and help to clearly illustrate the distinctions between the ICD high and low groups. At the same time, considering the simplicity and interpretability of the study, the division of k = 2 makes the results easier to understand and present. Although there may seem to be trends of more groups from the heatmap, after in-depth analysis, the biological significance and clinical associations of other possible groupings are not as clear and consistent as when k = 2.

As for the impact of k = 3 on the KM curve in Figure 1C and subsequent results, we have conducted some preliminary simulation analyses. The results show that if the "ICD-mid" group is introduced, the KM curve in Figure 1C may become more complex, and the survival differences among the three groups may present different patterns. This may lead to a more detailed understanding of the response to immunotherapy and patient prognosis, but it will also increase the difficulty of interpreting the results. Since the biological characteristics and clinical significance of the "ICD-mid" group are relatively ambiguous, it may interfere with the presentation of our main conclusions to a certain extent. Therefore, in this study, we believe that the division of k = 2 is more conducive to highlighting the key research results and conclusions.

Thank you again for your valuable comments. We will further improve the explanation and description of the relevant content in the paper to ensure the rigor and readability of the research.

(3) The 'ICD' gene set contains a lot of immune response genes that code for pleiotropic proteins, as well as genes certainly involved in ICD. It is not convincing that the gene expression differences thus DEGs between the two groups, are not simply "immune-response high" vs "immune-response low". For the DEGS analysis, how many of the 34 ICD gene sets are DEGS between the two groups? Of those, which markers of ICD are DEGs vs. those that are related to immune activation?

a. The pathway analysis then shows that the DEGs found are associated with the immune response.

b. Are HMGB1, HSP, NLRP3, and other "ICD genes" and not just the immune activation ones, actually DEGs here?

c. Figures D, I-J are not legible in the manus.

We sincerely appreciate your profound insights and valuable questions regarding our research. These have provided us with an excellent opportunity to think more deeply and refine our study.

We fully acknowledge and are grateful for your incisive observations on the "ICD" gene set and your valid concerns about the differential expression gene (DEG) analysis. During the research design phase, we were indeed aware of the complexity of gene functions within the "ICD" gene set and the potential confounding factors between immune responses and ICD. To distinguish the impacts of these two aspects as effectively as possible, we employed a variety of bioinformatics methods and validation strategies in our analysis.

Regarding the DEG analysis, among the 34 ICD gene sets, 30 genes showed significant differential expression between the groups, excluding HMGB1, HSP90AA1, ATG5, and PIK3CA. We further conducted detailed classification and functional annotation analyses on these DEGs. The ICD gene set is from a previous article and is related to the process of ICD. Relevant literature is in the materials section. HMGB1: A damage-associated molecular pattern (DAMP) that activates immune cells (e.g., via TLR4) upon release, but its core function is to mediate the release of "danger signals" in ICD, with immune activation being a downstream effect.HSP90AA1: A heat shock protein involved in antigen presentation and immune cell function regulation, though its primary role is to assist in protein folding, with immune-related effects being auxiliary.NLRP3: A member of the NOD-like receptor family that forms an inflammasome, activating CASP1 and promoting the maturation and release of IL-1β and IL-18.Among the 34 DEGs, the majority are associated with immune activation, such as IL1B, IL6, IL17A/IL17RA, IFNG/IFNGR1, etc.

(4) I may be missing something, but I cannot work out what was done in the paragraph reporting Figure 2I. Where is the ICB data from? How has this been analysed? What is the cohort? Where are the methods?

The samples used in the analysis corresponding to Figure 2I were sourced from the TCGA (The Cancer Genome Atlas) and TCIA (The Cancer Immunome Atlas) databases. These databases are widely recognized in the field for their comprehensive and rigorously curated cancer - related data, ensuring the reliability and representativeness of our sample cohort.

Regarding the data analysis, the specific methods employed are fully described in the "Methods" section of our manuscript.

(5) How were the four genes for your risk model selected? It is not clear whether a multivariate model and perhaps LASSO regularisation was used to select these genes, or if they were selected arbitrarily.

As you inquired about how the four genes for our risk model were selected, we'd like to elaborate based on the previous analysis steps. In the Cox univariate analysis, we systematically examined a series of ICD-related genes in relation to the overall survival (OS) of patients. Through this analysis, we successfully identified four ICD-related genes, namely CALR (with a p-value of 0.003), IFNB1 (p = 0.037), IFNG (p = 0.022), and IF1R1 (p = 0.047), that showed a significant association with OS, as illustrated in Figure 3A.

Subsequently, to further refine and optimize the model for better prediction performance, we subjected these four genes to a LASSO regression analysis. In the LASSO regression analysis (as depicted in Figure 3B and C), we aimed to address potential multicollinearity issues among the genes and select the most relevant ones that could contribute effectively to the construction of a reliable predictive model. This process allowed us to confirm the significance of these four genes in predicting patient outcomes and incorporate them into our final predictive model.

(6) How related are the high-risk and ICD-high groups? It is not clear. In the 'ICD-high' group in the 1A heatmap, patients typically have a z-score>0 for CALR, IL1R, IFNg, and some patients do also for IFNB1. However, in 3H, the 'high risk' group has a different expression pattern of these four genes.

Patients were divided into ICD high-expression and low-expression groups based on gene expression levels. However, the relationship between these genes and patient prognosis is complex. As shown in Figure 3A, some genes such as IFNB1 and IFNG have an HR < 1, while CALR and IL1R1 have an HR > 1. Therefore, an algorithm was used to derive high-risk and low-risk groups based on their prognostic associations.

(7) In the four-gene model, CALR is related to ICD, as outlined by the authors briefly in the discussion. IFNg, IL1R1, IFNB1 have a wide range of functions related to immune activity. The data is not convincing that this signature is related to ICD-adjuvancy. This is not discussed as a limitation, nor is it sufficiently argued, speculated, or referenced from the literature, why this is an ICD-signature, and why CALR-high status is related to poor prognosis.

We acknowledge that the functions of these genes are indeed complex and extensive. In the current manuscript, we have included a preliminary discussion of their roles in the "Discussion" section. As demonstrated by the data presented earlier, these genes do exhibit associations with ICD, and we firmly believe in the validity of these findings.

However, we are fully aware that our current discussion is not sufficient to fully elucidate the intricate relationships among these genes, ICD, and other biological processes. In response to your valuable feedback, we will conduct an in - depth review of the latest literature, aiming to gain a more comprehensive understanding of the underlying mechanisms.

(8) Score is spelt incorrectly in Figures 3F-J.

Figures 3F-J have been revised as requested.

(9) The authors 'comprehensive analysis' in lines 165-173, is less convincing than the preceding survival curves associating their risk model with survival. Their 'correlations' have no statistics.

We understand your concern regarding the persuasiveness of the content in this part, especially about the lack of statistical support for the correlations we presented. While we currently have our reasons for presenting the information in this way and are unable to make changes to the core data and descriptions at the moment, we deeply respect your perspective that it could be more convincing with proper statistical analysis.

(10) The authors performed immunofluorescence imaging to "validate the reliability of the aforementioned results". There is no information on the imaging used, the panel (apart from four antibodies), the patient cohort, the number of images, where the 'normal' tissue is from, how the data were analysed etc. This data is not interpretable without this information.

a. Is CD39 in the panel? CD8, LAG3? It's not clear what this analysis is.

The color of each antibody has been marked in Fig 2B. The cohort information and its source have been supplemented. The staining experiment was carried out using a tissue microarray, and the analysis method can be found in the "Methods" section.Formalin-fixed, paraffin-embedded human tissue microarrays (HBlaU079Su01) were purchased from Shanghai Outdo Biotech Co., Ltd. (China), comprising a total of 63 cancer tissues and 16 adjacent normal tissues from bladder cancer patients. Detailed clinical information was downloaded from the company's website.The Remmele and Stegner’s semiquantitative immunoreactive score (IRS) scale was employed to assess the expression levels of each marker,as detailed inMethods2.5.CD39, CD8, and LAG3 were also stained, but the results were not presented.

(11) The single-cell RNA sequencing analysis from their previous dataset is tagged at the end. CALR expression in most identified cells is interesting. Not clear what this adds to the work beyond 'we did scRNA-seq'. How were these data analysed? scRNA-seq analysis is complex and small nuances in pre-processing parameters can lead to divergent results. The details of such analysis are required!

We understand your concern about the contribution of the single-cell RNA sequencing results. The main purpose of this analysis is to observe the expression changes of the four genes at the single-cell level. As you mentioned, single-cell RNA sequencing analysis is indeed complex, and we fully recognize the importance of detailed information. We performed the analysis using common analytical methods for single-cell sequencing.It has been supplemented in the Methods section.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Below is a point-by-point response to reviewers concerns.

Main changes are colored in red in the revised manuscript.

Reviewer #1 (Significance (Required)):

General assessment:

This study provides a valuable computational framework for investigating the dynamic interplay between DNA replication and 3D genome architecture. While the current implementation focuses on Saccharomyces cerevisiae, whose genome organization differs significantly from mammalian systems.

Advance: providing the first in vivo experimental evidence in investigating the role(s) of Cohesin and Ctf4 in the coupling of sister replication forks.

Audience: broad interests; including DNA replication, 3D genome structure, and basic research

Expertise: DNA replication and DNA damage repair within the chromatin environment.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

By developing a new genome-wide 3D polymer simulation framework, D'Asaro et al. investigated the spatiotemporal interplay between DNA replication and chromatin organization in budding yeast: (1) The simulations recapitulate fountain-like chromatin patterns around early replication origins, driven by colocalized sister replication forks. These findings align with Repli-HiC observations in human and mouse cells, yet the authors advance the field by demonstrating that these patterns are independent of Cohesin and Ctf4, underscoring replication itself as the primary driver. (2) Simulations reveal a replication "wave" where forks initially cluster near the spindle pole body (SPB) and redistribute during S-phase. While this spatial reorganization mirrors microscopy-derived replication foci (RFis), discrepancies in cluster sizes compared to super-resolution data suggest unresolved mechanistic nuances. (3) Replication transiently reduces chromatin mobility, attributed to sister chromatid intertwining rather than active forks.

This work bridges replication timing, 3D genome architecture, and chromatin dynamics, offering a quantitative framework to dissect replication-driven structural changes. This work provides additional insights into how replication shapes nuclear organization and vice versa, with implications for genome stability and regulation.

We thank Reviewer 1 for her/his enthusiasm and her/his comments that help us to greatly improve the manuscript.

However, the following revisions could strengthen the manuscript:

Major:

Generalizability to Other Species While the model successfully recapitulates yeast replication, its applicability to larger genomes (e.g., mammals) remains unclear. Testing the model against (Repli-HiC/ in situ HiC, and Repli-seq) data from other eukaryotes (particularly in mammalian cells) could enhance its broader relevance.

We agree with the reviewer that testing the model in higher eukaryotes would be highly informative. The availability of Repli-HiC on one hand and higher resolution microscopy on the other could enable insightful quantitative analyses. With our formalism, it is in principle already possible to capture realistic 1D replication dynamics as the integrated mathematical formalism (by Arbona et al. ref. [63]) was already used to model human genome S-phase. In addition, the formalism developed for chain duplication is generic and can be contextualized to any species. However, when addressing the problem in 3D, we would likely require including other crucial structural features such as TADs or compartments. Such a model would require an extensive characterization worthy of its own publication. These considerations are now mentioned in the Discussion as exciting future perspectives (Page 17).

On the other hand, we would like to highlight that, while very minimal in many aspects, our model includes many layers of complexity (explicit replication, different forks interactions, stochastic 1D replication dynamics, physical constraints at the nuclear level). In addition, addressing this problem in budding yeast offers the great advantage of simultaneously capturing at the same time both the local and global spatio-temporal properties of DNA replication and to focus first only on those aspects and not on the interplay with other mechanisms like A/B compartmentalization (absent in yeast) that may add confusions in the data analysis and comparison with experimental data . Studying such an interplay is a very important and challenging question that, we believe, goes beyond the scope of the present work.

Validation with Repli-HiC or Time-Resolved Techniques

The Hi-C data in early S-phase supports the model, but the intensity of replication-specific chromatin interactions is faint, which could be further validated using Repli-HiC, which captures interactions around replication forks. Alternatively, ChIA-PET or HiChIP targeting core component(s) (eg. PCNA or GINS) of replisomes may also solidify the coupling of sister replication forks.

We thank the reviewer for the suggestion. Unfortunately, corroborating our HiC results using Repli-HiC or HiChIP would require developing and adapting the protocols to budding yeast which is well beyond the scope of this work mainly focused on computational modelling. In addition, we believe that the signature found in our Hi-C data is clear and significant enough to demonstrate the effect.

However, we included in the Discussion (Page 15) a more detailed description on how our work compares with the Repli-HiC study in mammals. In particular, we added a new supplementary figure (new Fig. S23) where we discuss our prediction on how Repli-HiC maps would appear in yeast in both scenarios of sister-forks interaction. Interestingly, we find that:

1) Fountain signals are strongly enhanced when sister forks interact.

2) Only mild replication dependent enrichment is detected when diverging forks do not interact.

These two results imply that disrupting putative sister-forks interaction would have a drastic effect on Repli-HiC if compared to HiC.

Interactions Between Convergent Forks

The study focuses on sister-forks but overlooks convergent forks (forks moving toward each other from adjacent origins), whose coupling has been observed in Repli-HiC. Could the simulation detect the coupling of convergent fork dynamics?

We thank the reviewer for this suggestion. We included in our Hi-C analysis aggregate plots around termination sites. Interestingly, no clear signature of coupling between convergent forks was detected (such as type II fountains in mammals) in vivo and in silico. Similarly, from visual inspection of individual termination sites, no fountains were clearly observed. These results can be found in the new Fig. S24 and possible mechanistic explanations are described more in detail in the Discussion (Page 15).

Unexpected Increase in Fountain Intensity in Cohesin/Ctf4 Knockouts.

In Fig.3A, a schematic illustrating the cell treatment would improve clarity. In Sccl- and Ctf4-depleted cells, fountain signals persist or even intensify (Fig. 3A). This counterintuitive result warrants deeper investigation. Could the authors provide any suggestions or discussions? Potential explanations may include:

Compensatory mechanisms (e.g., other replisome proteins stabilizing sister-forks).

Altered chromatin mobility in mutants, enhancing Hi-C signal resolution.

Artifacts from incomplete depletion (western blots for Sccl/Ctf4 levels should be included).

A scheme illustrating the experimental protocol for degron systems (CDC45-miniAID & SCC1-V5-AID) with the corresponding western blots and cell-cycle progression are shown in Fig. S26. Note that for Ctf4, we are using a KO cell line where the gene was deleted.

We do agree with the reviewer that there exist several possible explanations explaining the differences between WT fountains and those observed in mutants. In the revised manuscript, we discussed some of them in Section 2 II B (Page 8):

(1) As already suggested in the paper, asynchronization of cells may impact the intensity of the fountains due a dilution effect mediated by the cells still in G1. Therefore, possible differences in the fractions of replicating/non-relicating cells between the different experiments (new Fig. S7C) would also result in differences in the signal. Moreover, it is important to highlight that aggregate plots are normalized (Observed/Expected) by the average signal (P(s)). Therefore, as Scc1-depleted cells do not exhibit cohesin-mediated loop-extrusion (see aggregate plots around CARs in new Fig. S7B), we may expect an enhancement of signal at origins due to dividing each pixel by a lower contact frequency with respect to the one found in WT.

(2) In the new Fig. S10, we plotted the relative enrichment of Hi-C reads around origins. While we already used the same approach to compare replicon sizes between simulations and experiments (see Fig S7A and response to comment n°9 of Reviewer 3), this analysis is instructive also when comparing different experimental conditions. While we find that the experiment in WT and Scc1-depleted cells show very similar replicon sizes, we do observe a small increase in the peak height for the cohesin mutant. This may also partially motivate differences in the intensity of the fountain. For ctf4Δ, we observe significantly smaller replicons. We speculate that such a mutant might exhibit slower replication and consequently might be enriched in sister-forks contacts.

(3) Compensatory mechanisms: we now briefly discussed this in the Discussion (Page 15).

Inconsistent Figure References

Several figure citations are mismatched. For instance, Fig. S1A has not been cited in the manuscript. Moreover, there is no Fig.1E in figure 1, while it has been cited in the text. All figure/panel references must be cross-checked and corrected.

We thank the reviewer for this observation. We have now corrected the mismatches.

Minor:

Page2: "While G1 chromosomes lack of structural features such as TADs or loops [3]" However, Micro-C captures chromatin loops, although much smaller than those in mammalian cells, within budding yeast.

Loops of approx 20-40 kb are found in interphase in budding yeast but only after the onset of S-phase ( ref. [52-61]). For this reason, our G1 model of yeast without loops well captures the experimental P(s) curves (Fig. S2). See also answer to point 12 of reviewer 2 .

In figure 2E, chromatin fountain signals can be readily observed in the fork coupling situation and movement can also be observed. However, the authors should indicate the location of DNA replication termination sites and show some examples at certain loci but not only the aggregated analysis.

The initial use of aggregate plots was motivated by the fact that fountains are quite difficult to observe at the single origin level in the experimental Hi-C due to the strong intensity of surrounding contacts (along the diagonal). However, when dividing early-S phase maps by the corresponding G1 map, we can now observe clear correlation between origin and fountain positions on such normalized maps. We now added an example for chromosome 7 in Fig.3 indicating early/late origins.

In Fig. S8 and S9 (where we also included termination sites), we show that fountains are prominently found at origins during S-phase and are lost in G2/M.

Reviewer #2 (Significance (Required)):

The topic is relevant and the problem being addressed is very interesting. While there has been some earlier work in this area, the polymer simulation approach used here is novel. The simulation methodology is technically sound and appropriate for the problem. Results are novel. The authors compare their simulations with experimental data and explore both interacting and non-interacting replication forks. Most conclusions are supported by the data presented. Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The manuscript by D'Asaro et al. investigates the relationship between DNA replication and chromatin organization using polymer simulations. While this is primarily a simulation-based study, the authors also present relevant comparisons with experimental data and explore mechanistic aspects of replication fork interactions.

We thank Reviewer 2 for her/his positive evaluation of our work and her/his suggestions that help us to clarify many aspects in our manuscript.

The primary weakness is that many aspects are not clear from the manuscript. Below is a list of questions that the authors must clarify:

In the Model and Methods section, it is written "Arbitrarily, we choose the backbone to be divided into two equally long arms, in random directions." It is unclear what is meant by "backbone to be divided" and "two equally long arms." Does this refer to replication?

We agree with the reviewer that the term backbone may be ambiguous. In the context of the initialization of the polymer, it refers to the L/4 initial bonds used to recursively build an unknotted polymer chain of final size L using the Hedgehog algorithm (see refs [101,109]). As shown in the Fig S1A, these initial L/4 bonds define the initial backbone of each chromosome before they are recursively grown to their final size. We chose to divide them into two branches (called “arms” in the old version of the manuscript) of equal length (L/8) and with random orientations. To avoid any ambiguity between the term arm used in that context and the chromosome arms in a biological sense (sequences on the left and right with respect to centromeres), we changed it to “linear branches” to improve clarity. We highlighted in Fig. S1A two examples of such a “V-shaped” backbone.

As stated in the text, these initial configurations are artificial and just aim to generate unknotted, random structures. After initiating the structures, we then added the geometrical constraints to the centromeric, telomeric and rDNA beads. This, combined with the tendency of the polymer to explore and fill the spherical volume, determine the relaxed G1-like state (see Fig. S2) obtained after an equilibration stage (corresponding to 10^7 MCS). Only after that initialization protocol, DNA replication is activated.

In chromosome 12, since the length inside the nucleolus (rDNA) is finite, the entry and exit points should be constrained. Have the authors applied any relevant constraint in the model?

Indeed, we did not introduce any specific constraint on the relative distance between rDNA boundary monomers in our model. They can therefore freely diffuse, independently from each other, on the nucleolus surface. This point is now clarified in the text. Note that, in this paper, we did not aim to finely describe the rDNA organization and its interactions with the rest of the genome, that is why we did not explicitly model rDNA. Moreover, to the best of our knowledge, there is not available experimental data to potentially tune such additional restraints.

Previous models such as Tjong et al. (ref. [66]) and Di Stefano et al. (ref [67]) have used very similar approximations than us. In the works of Wong et al. (ref.[61]) and Arbona et al. (ref.[63]), rDNA is explicitly modelled via larger/thicker beads/segments, and thus accounts for some generic polymer-based constraints between rDNA boundary elements.

However, note that all these different models, including ours, still correctly predict the strong depletion of contacts between rDNA boundaries, indicating that there exists a spatial separation between the two boundary elements that is qualitatively well captured by our model (See Fig. S1 D and Fig. 1B).

What is the rationale for normalizing the experimental and simulation results by dividing by the respective P_intra(s = 10 kb)?

This normalization was used in Fig. 1 to obtain a rescaling between experiments and simulations. This approach assumes that simulated and experimental Hi-C maps are proportional by a factor that, in Fig 1B, was set to P_exp(s=16kb)/P_sim(s=16kb). Similar strategies are used in a number of modeling studies (for example ref. [103,106]).

We use the average contact frequency (P_intra) at this genomic scale (s in the order of 10s of kb) because our polymer simulations well capture the experimental P(s) decay above this scale. This method allows to plot the two signals with the same color scale and to give a qualitative, visual intuition on the quality of the modeling. Note that normalization has no impact on the Pearson correlation given in text. More generally, it allows to semi-quantitatively compare predicted and experimental Hi-C data.

In Fig 1D, we instead normalize the average signal between pairs of centromeres (inter-chromosomal aggregate plot off-diagonal) by the average P_intra(s=10kb). This method allows estimating how frequently centromeres of different chromosomes are in contact relative to intra-chromosomal contacts at the chosen scale (10 kb). In the new paragraph “Comparison with in vivo HiC maps in G1” (Page 22) , we describe more in detail the quantitative insights that can be recovered from such analysis.

As a comparison, such normalization is not required when computing Observed/Expected maps (Fig. 1C or aggregate plots in Fig. 2 and Fig. 3) as simulation and experimental maps are normalized by their own P(s) curves. We now clarify this aspect in the Materials in Methods under the paragraph “Comparison between on diagonal aggregate plots” (Page 22).

In the sentence "For instance, chromosomes are strictly bound by the strong potential to localize between 250 and 320 nm from the SPB," is it 320 or 325 nm? Is there a typo?

We confirm that the upper bound is indeed 325 nm as stated in Eq.2 and not 320 nm.

Please list the number of beads in each chromosome and the location of the centromere beads.

A new table (Table S2) was included to highlight beads number and centromere positions.

In Eq. 7, when the Euclidean distance between the sister forks d_ij > 50 nm, the energy becomes more and more negative. This implies that the preferred state of sister forks is at distances much greater than 50 nm. Then how is "co-localization of sister forks" maintained?

We corrected the typo sign in Eq.7. The corrected equation without the minus sign - consistently with what simulated - implies that sister forks tend to minimize their 3D distance. The term goes to zero when their distance is within 40 nm (2 nearest-neighbouring sites).

The section on "non-specific fork interactions" is unclear. You state that the interaction is between "all the replication forks in the system," but f_ij is non-zero only for second nearest-neighbors. The whole subsection needs clarification.

We corrected the text, specifying that the energy is non-zero for both first and second neighbours. In practice, two given forks do not experience any attractive energy unless their 3D distance is less than 2 nearest-neighbours. To clarify this aspect, we articulated more in the methods how non-specific fork interactions are implemented in the lattice during the KMC algorithm. We also included a new supplementary image (Fig. S15), where we schematize how forks move in 3D and how changes in their position update the table that tracks the number of forks around each lattice site.

Eq. 6 has no H_{sister-forks}. Is this a typo?

We confirm that it is a typo and the formula was corrected to H_{sister-forks}.

While discussing the published work, the authors may cite the recent paper [https://doi.org/10.1103/PhysRevE.111.054413].

The reference is now included when discussing previous polymer models of DNA replication.

It is not clear how the authors actually increase the length of new DNA in a time-dependent manner. For example, when a new monomer is added near the replication origin (green bead in Fig. 3C), what happens to the red and blue polymer segments? Do they get shifted? How do the authors take into account self-avoidance while adding a new monomer? These details are not clear.

The detailed description of the chain duplication algorithm and its systematic analysis was performed in our previous study (ref. [25]).

However, we agree with the reviewer that to improve self-consistency more details must be included in the present manuscript (see also answer to comment 1 of Reviewer 3). In particular, we now highlight in Materials and Methods that self-avoidance is indeed temporarily broken when we add a newly replicated monomer on top of the site where the fork is. Such double occupancy in the lattice rapidly vanishes due to 3D local moves. We refer to our PRX work (ref [25] and in particular to the following figure (extracted from FIG. S1 in ref.[25]) which illustrates how the bonds/segments of the two sister chromatids are consistently maintained.

How do the authors ensure that monomers get added at a rate corresponding to velocity v? The manuscript mentions "1 MCS = 0.075 msec," but in how many MC steps is a new monomer added? How is it decided?

Similarly to origin firing, replication by fork movement along the genome occurs stochastically, with a rate which we derive by converting the physiological fork speed in yeast 2.2 kb/min (ref. [41]) into a rate in (number of monomer/MCS) units. In practice, we generate a random number that, if smaller than such a rate, leads to forks duplication. We clarify this aspect in the Materials and Methods, also referring to our previous work for a more detailed summary.

The authors stress the relevance of loop extrusion. However, in their polymer simulation, the newly replicated chromatin does not form any loops. Is this consistent with what is known?

Indeed, our simulations do not have any concurrent extrusion mechanism such as cohesin-mediated loops. This choice was purposely made to isolate and characterize replication-dependent effects.

That is why we compare our predictions on chromatin fountain patterns (Fig. 3) with data obtained for the Scc1 mutant strain where cohesin is absent in order to disentangle the possible interference with loop-extruding cohesin. For subsection C where microscopy data are available only in WT condition, we cannot rule out that the observed discrepancies between experiments and predictions cannot be due to missing mechanisms including loop extrusion. It was already mentioned in the Discussion (Page 16). It is however unclear whether sparse and small loops between CARs (see Fig. S7B) in S-phase, could be sufficient to recapitulate the microscopy estimates on the sizes of replication foci and no clear signature of inter-origin loops (possibly mediated by loop extrusion) are observed in Hi-C data in WT and Scc1 deficient conditions.

Moreover, as mentioned in the Discussion, the poorly characterized mechanisms behind forks/extruding-cohesin encounters does not allow for a straightforward modelling of such processes whose accurate description/simulation would require its own study.

Please add a color bar to Fig. 4B.

The color bar was included.

In the MSD plot (Fig. 6), even though it appears to be a log-log plot, the exponents are not computed. Typically, exponents define the dynamics.

We plot the expected 0.5 exponent at smaller time-scales as mentioned in the main text in Fig. 6, previously included only in new Fig. S19A.

The dynamics will depend on the precise nature of interactions, such as the presence or absence of loop extrusion. If the authors present dynamics without extrusion, is it likely to be correct?

The reviewer is correct in highlighting how our model does not capture the potential decrease in dynamics due to cohesin mediated loop extrusion. However, our model does capture the expected Rouse regime (see Fig. 6A, S19A and ref [83]), which justify our timemapping strategy. In comment 16 of reviewer 3, we discuss more in detail the robustness of our results with respect to variation in such a mapping. In the specific context of Fig. 6A, we predict the gradual decrease in dynamics due to sister chromatids intertwining independently of any cohesin-associated activity (both loop-extruding and cohesive). As loop extrusion is also decreasing chromatin mobility overall (ref. [87]), if such a decrease in mobility is observed in WT in vivo, it may be indeed difficult to assign such a decrease to replication rather than loop extrusion. That is why in the Discussion (Page 16), we propose to compare our prediction to experiments in cohesin-depleted cells. In the context of Fig.6B&C, we don’t expect loop extrusion to be a confounding effect as the predicted decrease in dynamics is specific to forks.

Reviewer #3 (Significance (Required)):

The work has been conducted thoroughly, and in general the paper is well written with good attention to detail. As far as I am aware, this is the first study where replication is simulated in a whole nucleus context, and the scale of the simulations is impressive. This allows the authors to address questions on replication foci and the spatiotemporal organisation of replication which would not be possible with more limited simulations, and to compare the model with previous experimental work. This, together with the new HiC data, I think this makes this a strong paper which will be of interest to biophysics and molecular biology researchers; the manuscript is written such that it would suit an interdisciplinary basic research audience.

We thank Reviewer 3 for her/his enthusiasm and her/his comments that help us to greatly improve the manuscript.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

The paper "Genome-wide modelling of DNA replication in space and time confirms the emergence of replication specific patterns in vivo in eukaryotes" by D'Asaro et. al presents new computational and experimental results on the dynamics of genome replication in yeast. The authors present whole-nucleus scale simulations using a kinetic Monte Carlo polymer physics model. New HiC data for synchronised yeast samples with different protein knock-downs are also presented.

The main questions which the paper addresses are whether sister forks remain associated during replication, whether there is more general clustering of replication forks, and whether replication occurs in a 'spatial wave' through the nucleus. While the authors' model data are not able to conclusively show whether sister forks remain co-localised, the work provides some important insights which will be of high interest to the field.

I have no major issues with the paper, only some minor comments and suggestions to improve the readability of the manuscript or provide additional detail which will be of interest to readers. I list these here in the order in which they appear in the paper. There are also a number of typos and grammatical issues through the text, so I recommend thorough proofreading.

The paper seems to be aimed at a broad interdisciplinary audience of biophysicists and molecular biologists. For this reason, the introduction could be expanded slightly to include some more background on DNA replication, the key players and terminology. Also, it seems that this work builds on previous modelling work (Ref. 19), so a bit more detail of what was done there, and what is new here would be helpful. The final paragraph the introduction mentions chromosome features such as TADs and loops, which should be explained in more detail.

We now have expanded the introduction to address some of these aspects. In particular, also as a response to comment 1 of Reviewer 4, we included additional background on the eukaryotic replication time program. We address in more detail its known interplay and correlation with crucial 3D structural features such as compartments and TADs. Finally, we add a sentence to clarify how the current work is distinct from the prior implementation and the novelty introduced here.

In the first results section, end of p2, the "typical brush-like architecture" is mentioned. This is not well explained, some additional detail or a diagram might help.

As very briefly summarized in the mentioned paragraph, the yeast genome is organized in the so-called Rabl organization where chromosome arms are all connected via the centromeres at the Spindle Pole Body (SPB). This is analogous to the definition of a polymer brush where several branches (the arms in this case), are grafted to a surface or to another polymer (see new Inset panel in Fig S1B). We refer in the main text to the scheme in Fig. S1B where we also include the snapshot of a single chromosome and the physical constraints that characterize this large-scale organization and extend the caption to clarify the analogy. A typical emerging feature at the single chromosome level is described in Fig. 1 B and C.

On p3-4, some previous work is described, with Pearson correlations of 0.86 and 0.94 are mentioned. What cases these two different values correspond to is not clear.

These Pearson correlations are obtained for our own modeling. We correct the values in the main text and more clearly indicate the specific correspondence with the maps used. We describe now in the Materials and Methods (new paragraph “Comparison with in vivo HiC maps in G1” and Table S2) how these values were obtained.

In section II-A-2, on the modelling details, it should be made clearer that the nucleus volume is kept constant, and that this is an approximation since typically the nucleus grows during S-phase. This is discussed in the Methods section, but it would be useful to also mention it here (and give some justification why it will not likely change the results).

We now state more clearly in the main text the limitation of our model regarding the doubling of DNA content without any increase of nuclear size. As mentioned in the Discussion, we do not expect this approximation to strongly impact our results, which mainly focus on early S-phase.

We now also included in the Discussion how the detection of the “replication wave” should be qualitatively independent of the density regime. In fact, even in the case of growing nuclei and constant density, the polarity induced by the Rabl organization and replication timing are the main drivers of such fork redistribution.

Regarding the slowdowning in diffusion due to sister chromatids intertwinings (see response to comment 13), we instead verified that the effect is indeed density independent (new Fig S21).

Fig 2. The text in Fig 2B is much smaller than other panels and difficult to read. Also Fig 3B, Fig 6.

This is now corrected.

In 2E, are the times given above each map the range which is averaged over? This could be clearer in the caption. In the caption it stated that these are 'observed over expected'; what the 'expected' is could be clearer.

We reformulate the description in the caption to make clearer that the time indicated above the plots indicate the time window used for the computation. As mentioned more in detail in the response to comment 17 below (and comment 3 of Reviewer 2), we included in the Material and Methods a more precise description on the normalization used in the case of on-diagonal aggregate plots (observed-over-expected).

In section II-B-2, the authors state that the cells are fixed 20 mins after release from S-phase. Can they comment on the rationale behind this choice, since from Fig 2 their simulations predict that the fountain pattern will no-longer be visible by that time.

In the experimental setup, cells are arrested in G1 with alpha-factor and then released in S-phase (see Fig S26 with corresponding scheme). The release from G1 synchronisation is not immediate, and staging of cells by flow-cytometry every 5 minutes for 30 minutes after release (data not shown in the main text but provided below) proved 20 minutes to be an adequate early S-phase timepoint (Page 17 in the Materials and Methods). As a consequence, the times indicated when describing the in vivo experiment, do not correspond to the ones indicated in our in silico system, for which the onset of replication is well defined. For these reasons, we have to determine which time window among the ones used in Fig 2E, is the most appropriate to compare with the experiment (see response to comment 9 for more details).

Fig.R1: Cell cycle progression monitored by flow cytometry after the release. For the first 15 minutes, cells are still mainly in G1 and only start replicating ~20 minutes after the release.

Section II-B-2(b) could be clearer. I don't understand what the conclusion the authors take from the metaphase arrest maps is. I'm not sure why they discuss again the Cdc45-depleted cells here, since this was already covered in the previous section.

Taken together, the G1, Cdc20 (metaphase-arrested cells), and Cdc45-depleted (early S cells but not replicated) conditions suggest that fountains reflect ongoing replication. Namely, G1-arrest shows that fountains require S-phase entry; Cdc45-depletion shows that fountains require origin firing and is not due to another S-phase event; and metaphase-arrested cells show that fountains are not permanent structures established by replication, but a transient replication-dependent structure.

This demonstrates that the emerging signal is not trivially dependent on (1) the presence of the second sister chromatids; or on (2) potential overlaps between origin positions and barriers (CARs) to loop extrusion (see also comment 12 of Reviewer 2). A sentence at the end of II-a was added to clarify the different information gained with the two strains.

We discuss again the cdc20 and cdc45 mutants in II-b to highlight how the results in II-a do not exclude potential interplay between cohesin-mediated loop-extrusion in presence forks progression. These considerations motivated our experiment in Scc1-depleted cells during early S-phase.

At the start of p8 (II-B-3) there is a discussion of the mapping to times to the early-S stage experiments. This could have more explanation. I don't follow what the issue is, or the process which has been used to do the mapping. From Fig 2B, it seems that the simulation time is already mapped well to real time.

As mentioned above in comment 7, we cannot clearly define a “t=0” when replication starts in vivo as the release from the G1-arrest is not immediate and perfectly synchronous. On the other hand, the times indicated within the text are those following the onset of polymer self-duplication in our simulations. Note that the mean replication time (MRT) shown in Fig.2B does not represent an absolute time, but rather an average relative timing along S-phase (signal rescaled between 0 and 1).

For all these considerations, we think that the most reliable strategy to compare fountains in vivo and in silico is to look at the replicon size via the enrichment in raw contacts around early origins, as illustrated in Fig S7A. In practice, looking at the relative counts of contacts around early origins we have a proxy for the average replicon size that we can match by computing the same analysis on simulated signals (Fig S7A). As a result, we find that the best simulated time window is between 5 and 7.5 minutes, compatible with early-S phase and with an approximate duration of G1 after release of 15 minutes as observed in other studies (ref. [61]).

Note that our conclusions are robust with respect to modulating this mapping method. In particular in Fig. S7, we thoroughly investigated how several confounding factors (such as time window used or partial synchronization) may impact the quantitative nature of our prediction without affecting the qualitative insights.

We included a more precise reference to the Supplementary Materials, where the approach is described and clarified.

In Fig 4A above each plot there is a cartoon showing the fork scenario. The left-hand cartoon is rendered properly, but the right-hand one has overlapping black boxes which I don't think should be there. These black boxes are present in many other figures (4B, 3B, 2E etc).

This issue seems to appear using the default PDF viewer on Mac OS. We have corrected the problem and no more black boxes should appear in the main text and in the Supplementary Material.

In II-C-2(b) it is mentioned that the number of forks within RFis is always assumed to be even. This discussion could be clearer. In particular, the authors state that under both fork scenarios, in the simulations they can detect odd numbers of forks within RFis - how can this happen in the case where sister forks are held together?

We included a more accurate description in the main text about why Saner et al. (ref [20]) make these assumptions in their estimates. We highlight possible inconsistencies such as the presence of termination events which, in our formalism, break sister forks interactions and lead to single forks to be detected. We also clarify the latter point when describing Fig 5B and describe in more detail replication bubbles merging events in the Materials and Methods.

Fig 6B and C, it would be useful if the same scale was used on both plots.

We now use the same scale when plotting Fig 6B and C.

Section II-D-1. There is a discussion on the presence of catenated chains; I did not understand how the replicated DNA becomes catenated, and what this actually means in this context. The way the process is described and the snapshots in Fig2C do not suggest that the chains are catenated. Some further discussion or a diagram would be useful here.

We included a small paragraph to better explain how intertwining of sister chromatids occurs, and more clearly refer to a snapshot in supplementary figure S19D (Page 14). As correctly mentioned by the reviewer, replication bubbles by construction are always unknotted during their growth (see example in Fig. 2C). As we thoroughly characterize in our previous work (ref. [25]), when several replication bubbles merge, the random orientation of sister chromatids potentially lead to catenation points and intertwined structures. We show below a scheme from our previous work (ref [25]). While in this past work, we demonstrated that the center of mass of the two sister chromatids show subdiffusive behaviour due to the additional topological constraints of their intertwining, this new analysis in the present work suggests that possible effects may also be observed when tracking the MSD (mean square displacement at the locus level) in a more realistic scenario where we included correct replication timing, chromosome sizes and Rabl-organization.

On p14 (section III) there is a section discussing possible mechanisms for sister fork interactions, and that result that Ctf4 might not play a role in this, as previously suggested. Are there any other candidate proteins which could be tested in the future?

To the best of our knowledge, there is no other candidate protein of the replisome that has been directly associated to sister-fork pairing in previous studies (as Ctf4). However, components of the replisome such as Cdt1, that have the capacity to oligomerize/self-interact, could be good candidates. We now mention this possibility in the Discussion (Page 15).

As on p14, second paragraph: there is a sentence "replication wave [51] cannot be easily visualised at the single cell level.", which seems to contradict the discussion on p9 "such a "wave" can also be observed at the level of an individual trajectory (Video S3,4) even if much more stochastic." I think more explanation is needed here.

We rephrased the mentioned passages to clarify the differences in detecting such “replication wave” at the population vs single cell level. In video S3 and S4, we can still observe an enrichment of forks at the SPB and later in S-phase a shift towards the equatorial plane. However, the stochasticity of polymer dynamics and 1D replication strongly hinder the ability to clearly visualize such redistribution.

In the methods section, p18, it is mentioned that the volume fraction is 3%. I assume this is before replication, and so after replication is complete this will increase to 6%. This should be stated more explicitly, with also a comment on the 5% volume fraction used in the time-scale mapping discussed on p17.

Indeed, we choose to map the experimental MSD measured in ref [83] by simulating a homopolymer 5% volume fraction and in periodic boundary conditions for consistency to previous work in the group (ref. [102-106]) and our previous replication model (ref.[25]). Moreover, this intermediate density regime also lies in between the minimal (3%) and maximal (6%) densities present in our system. When redoing the time mapping with the G1 MSD plotted in Fig 6A and new Fig S19A, we obtain a very similar value of approx. 1MC=0.6ms. Note that the time mapping aims to obtain a rough estimation of real times as several factors, such as active processes, non-constant density, cell-cycle progression may all contribute to chromatin diffusion in vivo (see also comment 15 to Reviewer 2). In the context of our formalism, differences in time mapping do not affect the 1D replication dynamics as all the parameters to model the 1D process are rescaled by the same factor. Moreover, as we characterized in more depth in our previous work (ref [25]), a crucial aspect that defines self-replicating polymers is the relationship between fork progression and the polymer relaxation dynamics. In physiological conditions, we remain in the regime where forks progress almost quasi-statically to allow the bubbles to re-equilibrate. Therefore, small discrepancies in the time mapping will not modify this regime and our results should remain robust.

On p20, processing of simulated HiC using cooltools is discussed. For readers unfamiliar with this software, a bit more detail should be given. Specifically, how does the normalisation account for having some segments which have been replicated and some which have not. Later on the same page (IV-C-2) two different strategies for comparing HiC maps are given; why are two different methods required, and what is the reasoning in each case?

In the raw - unbalanced - data, we observe an artificial increase in contacts around origins in S-phase for both simulation and experiments. This is simply due to the presence of the second Sister chromatids and the fact that contacts between distinct DNA segments are mapped to a single bin.

In the new Fig. S25, we illustrate this effect by computing aggregate plots around early origins using single-chromosome simulations. We demonstrate that the ICE normalization corrects for the variations in copy number due to replication and thus for such artificial increases in contacts during S-phase. We show that such a normalization is equivalent to explicitly divide each bin by the average copy-number of the corresponding segments.

We have now included a sentence in the Materials and Methods to clarify this. Moreover, a detailed description of the other alternative strategies used to compare experiments and simulations were presented in response to comment 3 to Reviewer 2 and two new paragraphs were added in the Materials and Methods.

The references section has an unusual formatting with journal names underlined.

We updated the formatting.

Reviewer #4 (Significance (Required)):

D’Asaro et al focus on the problem of how genome structure is altered by the progression of replisomes through S-phase in the budding yeast S. cerevisiae. The authors employ computational polymer modeling of G1 chromosomes, then implement a hierarchical model of replication origin firing along these polymers to examine how the G1 chromosome structural state is perturbed by replisome progression. Their results indicate that replication origins create 'fountains' - Hi-C map features that other groups have demonstrated are likely to originate from symmetric extrusion by condensin / cohesin complexes originating at a fixed point. These 'fountains' appear to be cohesin-independent, as revealed by depletion Hi-C experiments. Finally, the authors provide evidence from their model of a 'replication wave' that emanates from the spindle pole body. This is an interesting manuscript that raises some exciting questions for the field to follow up on.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

In their manuscript, "Genome-wide modeling of DNA replication in space and time confirms the emergence of replication specific patterns in vivo in eukaryotes," authors Asaro et al perform computational modeling analyses to address an important open question in the chromatin field: how is DNA replication timing coupled to 3D genome architecture? Over the past ten years, the convergence of high-resolution replication timing (RT) analysis with high-resolution 3D genome mapping (e.g. 'Hi-C' technology) has resulted in the discovery that replication timing domains overlap considerably with 3D genomic domains such as topologically associating domains (TADs). How and why this happens both remain unknown, and advances in 3D genome mapping technology have provided even more data to model the problem of both 1) scheduling replication from distinct series of origins / initiation zones, and 2) modeling how 3D genome architecture is altered by the progression of replication forks, which inherently destroy chromatin structure before faithfully reforming G1 structures on daughter chromatids. As such, the problem being tackled by this computational manuscript is interesting.

We thank Reviewer 4 for her/his positive evaluation of our work and her/his comments that help us to greatly improve the manuscript.

Reviewer Comments / Significance

In their manuscript, "Genome-wide modeling of DNA replication in space and time confirms the emergence of replication specific patterns in vivo in eukaryotes," authors D’Asaro et al perform computational modeling analyses to address an important open question in the chromatin field: how is DNA replication timing coupled to 3D genome architecture? Over the past ten years, the convergence of high-resolution replication timing (RT) analysis with high-resolution 3D genome mapping (e.g. 'Hi-C' technology) has resulted in the discovery that replication timing domains overlap considerably with 3D genomic domains such as topologically associating domains (TADs). How and why this happens both remain unknown, and advances in 3D genome mapping technology have provided even more data to model the problem of both 1) scheduling replication from distinct series of origins / initiation zones, and 2) modeling how 3D genome architecture is altered by the progression of replication forks, which inherently destroy chromatin structure before faithfully reforming G1 structures on daughter chromatids. As such, the problem being tackled by this computational manuscript is interesting.

D’Asaro et al focus on the problem of how genome structure is altered by the progression of replisomes through S-phase in the budding yeast S. cerevisiae. The authors employ computational polymer modeling of G1 chromosomes, then implement a hierarchical model of replication origin firing along these polymers to examine how the G1 chromosome structural state is perturbed by replisome progression. Their results indicate that replication origins create 'fountains' - Hi-C map features that other groups have demonstrated are likely to originate from symmetric extrusion by condesin / cohesin complexes originating at a fixed point. These 'fountains' appear to be cohesin-independent, as revealed by depletion Hi-C experiments. Finally, the authors provide evidence from their model of a 'replication wave' that emanates from the spindle pole body. This is an interesting manuscript that raises some exciting questions for the field to follow up on.

Major Comments

There is a tremendous amount of work coupling RT domains to 3D genome architecture, especially deriving from the ENCODE and 4D Nucleome consortia. These studies are not adequately highlighted in the introduction and discussion of this manuscript, and this treatment of the literature would ideally be amended in any revised manuscript.

We include new sentences in the introduction to discuss more in detail the correlation between 3D genome architecture and replication timing program, and advancement in this field in the last decades. We also included additional citations to reviews and publications (ref [8-16]). These references were also included at the end of the Discussion where we address the exciting perspective of employing our model in higher eukaryotes and potentially tackle the complex interplay between 3D nuclear compartmentalization and replication dynamics (see also response 1 to Reviewer 1).

S. cerevisiae origins of replication differ from metazoan origins of replication in that they are sequence-defined and are known to fire in a largely deterministic pattern (see classic study PMID11588253). From the methods of the authors it is not clear that the known deterministic firing pattern is being used here, but instead a stochastic sampling method? Please clarify in the manuscript. Specifically, it would be good to understand how the Initiation Probability Landscape Signal correlates with what is already known about origin firing timing.

In our model, the positions of origins are stochastically sampled proportionally to the IPLS which was inferred directly from experimental MRT (ref. [63]) and RFD (ref. [44]). This modeling approach allows reproducing with a very high accuracy the known replication timing data (correlation of 0.96) and Fork directionality data (correlation of 0.91) (see ref. [71]). Origins were defined as the peaks in the IPLS signal. In Fig S3, we extensively compare these origins and the known ARS positions from the Oridb database. For example, most of our early origins (96%) are located close to known, confirmed ARS. Moreover, even if our algorithm is stochastic for origin firing, we remark that each early origin will fire in 90 % of the simulations, coherent with the quasi-deterministic pattern of origin firing and experimental MRT and RFD data. We now have added such statistics of firing in the revised manuscript (Page 4).

It seems possible that experimental sister chromatid Hi-C data (PMID32968250) and nanopore replicon data (PMID35240057) could be used to further ascertain the validity of some of the findings of this paper. Specifically, could the authors demonstrate evidence in sister chromatid Hi-C data that the replisome is in fact extruding sister chromatids? Moreover, are the interactions being measured specifically in cis (as opposed to trans sister contacts)? For the nanopore replicon data, how do replicon length, replication timing, and position along the replication 'wave' correlate?

We thank the reviewer for the suggestions.

Hopelessly there is currently no Sister-C data available during S-phase. In the seminal study (PMID32968250), cells were arrested in G2/M via nocodazole treatment. For a different unpublished work, we already analysed in detail the SisterC dataset and we did not observe clear fountain-like signature, consistent with our own G2/M Hi-C maps (cdc20) where fountains were absent. Note that, in the present work, in order to compare our predictions with standard HiC data, we included all contacts (cis and trans chromatids), mapping pairwise contacts from distinct replicated sequences/monomers to a single bin (see also response to comment 17 to Reviewer 3 and new Fig. S25).

We now mention in the Discussion that Sister-C data during S-phase could help monitoring the role of replisomes on relative sister-chromatids organization (Page 15).

Main results from the nanopore replicon data study include the observed high symmetry between sister forks and their linear progression, as the density of replicons appears to be uniform with respect to their length. Since these two specific constraints are already present in the framework of Arbona et al. (ref. [63]), our model is able to reproduce these features of DNA replication captured by the nanopore data.

Moreover, as we model with very high accuracy replication timing data (see response to comment 2) and forks positioning, we can assume that our formalism well captures replicon positioning and lengths observed in vivo.

As this study does not include any additional exploration or variation of the parameters inferred by Arbona et al. (ref. [63]), we consider a quantitative comparison with the nanopore replicon data to be beyond the scope of this paper.

Minor Comments:

The paper is in most places easy to follow. However, Section C bucked this trend and in general was quite difficult to follow. We would recommend that the authors try to revise this section to make clearer the actual physical parameters that govern a 'replication wave' and the formation of replication foci - how many forks, the extent to which the sisters are coordinated, etc for early vs. late replicating regions.

We now state more clearly with a sentence in the main text the driving forces behind the formation of such a “replication wave”. We believe that the several additions and clarifications following the various comments, improved the clarity of the manuscri

Reviewer #1 (Public review):

Munday, Rosello, and colleagues compared predictions from a group of experts in epidemiology with predictions from two mathematical models on the question of how many Ebola cases would be reported in different geographical zones over the next month. Their study ran from November 2019 to March 2020 during the Ebola virus outbreak in Democratic Republic of the Congo. Their key result concerned predicted numbers of cases in a defined set of zones. They found that neither the ensemble of models nor the group of experts produced consistently better predictions. Similarly, neither model performed consistently better than the other, and no expert's predictions were consistently better than the others'. Experts were also able to specify other zones in which they expected to see cases in the next month. For this part of the analysis, experts consistently outperformed the models. In March, the final month of the analysis, the models' accuracy was lower than in other months, and consistently poorer than the experts' predictions.

A strength of the analysis is use of consistent methodology to elicit predictions from experts during an outbreak that can be compared to observations, and that are comparable to predictions from the models. Results were elicited for a specified group of zones, and experts were also able to suggest other zones that were expected to have diagnosed cases. This likely replicates the type of advice being sought by policymakers during an outbreak.

A potential weakness is that the authors included only two models in their ensemble. Ensembles of greater numbers of models might tend to produce better predictions. The authors do not address whether a greater number of models could outperform the experts.

The elicitation was performed in four months near the end of the outbreak. The authors address some of the implications of this. A potential challenge for the transferability of this result is that the experts' understanding of local idiosyncrasies in transmission may have improved over the course of the outbreak. The model did not have this improvement over time. The comparison of models to experts may therefore not be applicable to early stages of an outbreak when expert opinions may be less well-tuned.

This research has important implications for both researchers and policy-makers. Mathematical models produce clearly-described predictions that will later be compared to observed outcomes. When model predictions differ greatly from observations, this harms trust in the models, but alternative forms of prediction are seldom so clearly articulated or accurately assessed. If models are discredited without proper assessment of alternatives then we risk losing a valuable source of information that can help guide public health responses. From an academic perspective, this research can help to guide methods for combining expert opinion with model outputs, such as considering how experts can inform models' prior distributions and how model outputs can inform experts' opinions.

Comments on revisions:

I am grateful to the authors for their responses to my previous comments. I think their updates have made the paper much clearer. I do not think the updates change the opinions already given in the public review so I have not modified it.

Author response:

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

Reviewer #1 (Public review):

Munday, Rosello, and colleagues compared predictions from a group of experts in epidemiology with predictions from two mathematical models on the question of how many Ebola cases would be reported in different geographical zones over the next month. Their study ran from November 2019 to March 2020 during the Ebola virus outbreak in the Democratic Republic of the Congo. Their key result concerned predicted numbers of cases in a defined set of zones. They found that neither the ensemble of models nor the group of experts produced consistently better predictions. Similarly, neither model performed consistently better than the other, and no expert's predictions were consistently better than the others. Experts were also able to specify other zones in which they expected to see cases in the next month. For this part of the analysis, experts consistently outperformed the models. In March, the final month of the analysis, the models' accuracy was lower than in other months and consistently poorer than the experts' predictions. 

A strength of the analysis is the use of consistent methodology to elicit predictions from experts during an outbreak that can be compared to observations, and that are comparable to predictions from the models. Results were elicited for a specified group of zones, and experts were also able to suggest other zones that were expected to have diagnosed cases. This likely replicates the type of advice being sought by policymakers during an outbreak. 

A potential weakness is that the authors included only two models in their ensemble. Ensembles of greater numbers of models might tend to produce better predictions. The authors do not address whether a greater number of models could outperform the experts. 

The elicitation was performed in four months near the end of the outbreak. The authors address some of the implications of this. A potential challenge to the transferability of this result is that the experts' understanding of local idiosyncrasies in transmission may have improved over the course of the outbreak. The model did not have this improvement over time. The comparison of models to experts may therefore not be applicable to the early stages of an outbreak when expert opinions may be less welltuned. 

This research has important implications for both researchers and policy-makers. Mathematical models produce clearly-described predictions that will later be compared to observed outcomes. When model predictions differ greatly from observations, this harms trust in the models, but alternative forms of prediction are seldom so clearly articulated or accurately assessed. If models are discredited without proper assessment of alternatives then we risk losing a valuable source of information that can help guide public health responses. From an academic perspective, this research can help to guide methods for combining expert opinion with model outputs, such as considering how experts can inform models' prior distributions and how model outputs can inform experts' opinions. 

Reviewer #2 (Public review):

Summary: 

The manuscript by Munday et al. presents real-time predictions of geographic spread during an Ebola epidemic in north-eastern DRC. Predictions were elicited from individual experts engaged in outbreak response and from two mathematical models. The authors found comparable performance between experts and models overall, although the models outperformed experts in a few dimensions. 

Strengths: 

Both individual experts and mathematical models are commonly used to support outbreak response but rarely used together. The manuscript presents an in-depth analysis of the accuracy and decision-relevance of the information provided by each source individually and in combination. 

Weaknesses: 

A few minor methodological details are currently missing.

We thank the reviewers for taking the time to consider our paper and for their positive reflections and suggestions for our study. We recognise and endorse their characterisation of the study in the public reviews and are greatful for their interest and support for this work. 

Reviewer #1 (Recommendations For The Authors): 

I initially found Table 1 difficult to interpret. In the final two columns, the rows relate to each other but in the other columns, rows within months don't relate to each other. Could this be made clearer? 

Thank you for your helpful suggestion. We agree that this is a little confusing and have now added vertical dividers to the table to indicate which parts of the table relate to each other.

In Figure 1A, the colours are the same as in the colour-bar for Figure 1B but don't have the same meaning. Could different colours be used or could Figure 1A have its own colour-bar to aid clarity? 

Thank you for your query. The colours are not the same pallette, but we appreciate that they look very similar. To help the reader we have changed the colour palette of panel A and added a legend to the left.  

In Figure 3, can labels for each expert be aligned horizontally, rather than moving above and below the timeline each month? 

Thank you for your perspective on this. We made the concious dicision to desplay the experts in this way as it allows the timeline to be presented in a shorter horizontal space. We appreciate that others may prefer a different design, but we are happy with this one. 

On lines 292 and 293, the authors state that experts were less confident that case numbers would cross higher thresholds. It seems that this would be inevitable given the number of cases is cumulative. Could this be clarified, please? 

Thank you for raising this point. We agree that this wording is confusing. We have now reworked the entire section in response to another reviewer. The equivalent section now reads: 

Experts correctly identified Mabalako as the highest-risk HZ in December. They attributed an average 82% probability of exceeding 2 cases; Mabalako reported 38 cases that month, exceeding all thresholds, although the probability assigned to exceeding the higher thresholds was similar to that of Beni (3 cases)

Reviewer #2 (Recommendations For The Authors): 

(1) Some methodological details seem to be missing. Most importantly, the results present multiple ensembles (experts, models, and both), but I can't seem to find anywhere in the Methods that details how these ensembles are calculated. Also, I think it would be useful to define the variables in each equation. It would have been easier to connect the equations to the description if the variables were cited explicitly in the text. 

Thank you for pointing out these omissions. We have included the following paragraph to detail how ensemble forecasts were calculated. 

“Enslemble forecasts

Ensemble forecasts were calculated as an average of the probabilities attributed by the members of the ensemble. For the expert ensemble the arithmetic mean was calculated across all experts with equal weighting. Similarly the model ensemble used the unweighted mean of the model forecasts. For the mixed (model and expert) ensemble, the mean was weighted such that the combined weight of the experts forecasts and the combined weight of the models forecasts were equal.”

(2) Overall, I think the results provide a strong analysis of model vs. expert performance. However, some sections were highly detailed (e.g., the text usually discusses results for every month and all health zones), which clouded my ability to see the salient points. For example, I found it difficult to follow all the details about expert/model predictions vs. observations in the "Expert panel and health zones..." subsection; instead, the graphical illustration of predictions vs. observations in Figure 4 was much easier to interpret. Perhaps some of these details could be trimmed or moved to the supplementary material. 

Thank you for your honest feedback on this point. We have shortened this section to highlight the key points that we feel are the most important. We have also simplified the text where we discuss the health zones nominated by experts. 

(3) Figure 5C is a nice visualization of the fallibility of relying on a single individual expert (or model). I wonder if it would be useful to summarize these results into the probability that a randomly selected expert outperforms a single model. Is it the case that a single expert is more unreliable than a single model? The discussion emphasizes the importance of ensembles and compares a single model to an ensemble of experts, but eliciting predictions from multiple experts may not always be possible. 

Thank you for raising this. We agree that this is an important point that eliciting expert opinions is not a trivial task and should not be taken for granted. We agree with the principle of your suggestion that it would be useful to understand how the models compare to indevidual experts. We don’t however believe that an additional analysis would add sufficiently more information than already shown in Figure 5, which already displays the full distribution of indevidual experts for each month and threshold. If you would like to try this analysis yourself, the relevant data (the indevidual score for each combination of expert, threshold, heal zone and month) is included in the github repo (https://github.com/epiforecasts/Ebola-Expert-Elicitation/blob/main/outputs/indevidual_results_with_scores.csv).

Minor comments: 

(1) Figure 2: the color scales in each panel are meant to represent different places, correct? The figure might be easier to interpret if the colors used were different.  

Thank you for bringing this to our attention. We have now changed the palette of panel A to differ from panel B.  

(2) Equation 7: is o(c>c_thresh) meant to be the indicator function (i.e. 1 if c>c_thresh) and 0 otherwise)? 

Thanks for raising this. The function o is the same as in the previous equation – an observation count function. We appreciate that this is not immediately clear so have added a sentence to explain the notation after the equation.

(3) Table 1: a brief description of the column headers would be useful.  

Thank you for the suggestion. We have now extended the table caption to include more description of the columns. 

“Table 1: Experts and health zones included in each round of the survey. The left part of the table details the experts interviewed (highlighted in green) the health zones included in the main survey in each month. In addition, the right part of the table details the health zones nominated by experts and the number of experts that nominated each one.”

Author response:

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

Reviewer #1 (Public review):

This study investigates how ant group demographics influence nest structures and group behaviors of Camponotus fellah ants, a ground-dwelling carpenter ant species (found locally in Israel) that build subterranean nest structures. Using a quasi-2D cell filled with artificial sand, the authors perform two complementary sets of experiments to try to link group behavior and nest structure: first, the authors place a mated queen and several pupae into their cell and observe the structures that emerge both before and after the pupae eclose (i.e., "colony maturation" experiments); second, the authors create small groups (of 5,10, or 15 ants, each including a queen) within a narrow age range (i.e., "fixed demographic" experiments) to explore the dependence of age on construction. Some of the fixed demographic instantiations included a manually induced catastrophic collapse event; the authors then compared emergency repair behavior to natural nest creation. Finally, the authors introduce a modified logistic growth model to describe the time-dependent nest area. The modification introduces parameters that allow for age-dependent behavior, and the authors use their fixed demographic experiments to set these parameters, and then apply the model to interpret the behavior of the colony maturation experiments. The main results of this paper are that for natural nest construction, nest areas, and morphologies depend on the age demographics of ants in the experiments: younger ants create larger nests and angled tunnels, while older ants tend to dig less and build predominantly vertical tunnels; in contrast, emergency response seems to elicit digging in ants of all ages to repair the nest.

We sincerely thank Reviewer #1 for the time and effort dedicated to our manuscript's detailed review and assessment. The revision suggestions were constructive, and we have provided a point-by-point response to address them.

Reviewer #2 (Public review):

I enjoyed this paper and the approach to examining an accepted wisdom of ants determining overall density by employing age polyethism that would reduce the computational complexity required to match nest size with population (although I have some questions about the requirement that growth is infinite in such a solution). Moreover, the realization that models of collective behaviour may be inappropriate in many systems in which agents (or individuals) differ in the behavioural rules they employ, according to age, location, or information state. This is especially important in a system like social insects, typically held as a classic example of individual-as-subservient to whole, and therefore most likely to employ universal rules of behaviour. The current paper demonstrates a potentially continuous age-related change in target behaviour (excavation), and suggests an elegant and minimal solution to the requirement for building according to need in ants, avoiding the invocation of potentially complex cognitive mechanisms, or information states that all individuals must have access to in order to have an adaptive excavation output.

We sincerely thank reviewer #2 for the time and effort dedicated to our manuscript's detailed review and assessment. We have provided a point-by-point response to the reviewer's comments, which we have incorporated into the revised version of the manuscript.

The only real reservation I have is in the question of how this relationship could hold in properly mature colonies in which there is (presumably) a balance between the birth and death of older workers. Would the prediction be that the young ants still dig, or would there be a cessation of digging by young ants because the area is already sufficient? Another way of asking this is to ask whether the innate amount of digging that young ants do is in any way affected by the overall spatial size of the colony. If it is, then we are back to a problem of perfect information - how do the young ants know how big the overall colony is? Perhaps using density as a proxy? Alternatively, if the young ants do not modify their digging, wouldn't the colony become continuously larger? As a non-expert in social insects, I may be misunderstanding and it may be already addressed in the citations used.

We thank the reviewer for this interesting question. We find that the nest excavation is predominantly performed by the younger ants in the nest, and the nest area increase is followed by an increase in the population. However, if the young ants dig unrestricted, this could result in unnecessary nest growth as suggested by reviewer #2. Therefore, we believe that the innate digging behavior of ants could potentially be regulated by various cues such as;

(a) Density-based: If the colony becomes less dense as its area expands, this could serve as a feedback signal for young ants to reduce or stop digging, as described in references (25, 29, 30).

(b) Pheromone depositions: If the colony reaches a certain population density, pheromone signals could inhibit further digging by young ants, references (25, 29), or space usage as a proxy for the nest area. 

Thus, rather than perfect information, decentralized control, and digging-based local cues probably regulate the level of age-dependent digging, without the ants needing to estimate the overall colony size or nest area.

In any case, this is an excellent paper. The modelling approach is excellent and compelling, also allowing extrapolation to other group sizes and even other species. This to me is the main strength of the paper, as the answer to the question of whether it is younger or older ants that primarily excavate nests could have been answered by an individual tracking approach (albeit there are practical limitations to this, especially in the observation nest setup, as the authors point out). The analysis of the tunnel structure is also an important piece of the puzzle, and I really like the overall study.

We thank the reviewer for the comments. We completely agree that individual tracking of ants within our experimental setup would have been the ideal approach, but we were limited by technical and practical limitations of the setup, as pointed out by the reviewer, such as; 

(a) Continuous tracking of ants in our nests would have required a camera to be positioned at all times in front of the nest, which necessitates a light background. Since Camponotus fellah ants are subterranean, we aimed to allow them to perform nest excavation in conditions as close to their natural dark environment as possible. Additionally, implementing such a system in front of each nest would have reduced the sample sizes for our treatments.

(b) The experimental duration of our colony maturation and fixed demographics experiments extended for up to six months (unprecedented durations in these kinds of measurements). These naturally limited our ability to conduct individual tracking while maintaining the identity of each ant based on the current design.

These details are described in detail within the revised version of the manuscript.

Reviewer #3 (Public review):

Summary:

In this study, Harikrishnan Rajendran, Roi Weinberger, Ehud Fonio, and Ofer Feinerman measured the digging behaviours of queens and workers for the first 6 months of colony development, as well as groups of young or old ants. They also provide a quantitative model describing the digging behaviours and allowing predictions. They found that young ants dig more slanted tunnels, while older ants dig more vertically (straight down). This finding is important, as it describes a new form of age polyethism (a division of labour based on age). Age polyethism is described as a "yes or no" mechanism, where individuals perform or not a task according to their age (usually young individuals perform in-nest tasks, and older ones foraging). Here, the way of performing the task is modified, not only the propensity to carry it or not. This data therefore adds in an interesting way to the field of collective behaviours and division of labour.

The conclusions of the paper are well supported by the data. Measurements of the same individuals over time would have strengthened the claims.

We sincerely thank reviewer #3 for the time and effort dedicated to our manuscript's detailed review and assessment. We completely agree with the reviewer’s comments on the measurements of the same individuals over time, however, we were limited by the technical and experimental limitations as described above and pointed out by reviewer #2.

Strengths:

I find that the measure of behaviour through development is of great value, as those studies are usually done at a specific time point with mature colonies. The description of a behaviour that is modified with age is a notable finding in the world of social insects. The sample sizes are adequate and all the information clearly provided either in the methods or supplementary.

We thank reviewer #3  for this assessment.

Weaknesses:

I think the paper is failing to take into consideration or at least discuss the role of inter-individual variabilities. Tasks have been known to be undertaken by only a few hyper-active individuals for example. Comments on the choice to use averages and the potential roles of variations between individuals are in my opinion lacking. Throughout the paper wording should be modified to refer to the group and not the individuals, as it was the collective digging that was measured. Another issue I had was the use of "mature colony" for colonies with very few individuals and only 6 months of age. Comments on the low number of workers used compared to natural mature colonies would be welcome.

Regarding the main comment 1

We completely agree with the reviewer’s comment on considering inter-individual variability based on activity levels. We have discussed how individual morphological variability could influence digging behavior (references: 28, 31), and we will elaborate further on this aspect in future revisions.

Regarding the main comment 2:

The term ‘colony maturation’ in our study refers to the progressive development of colonies from a single queen, distinguishing it from experiments that begin with pre-established, demographically stable colonies. We provide a detailed explanation for this terminology in the revised version of the manuscript. We were practically limited by the continuation of the experiments for more than 6 months of age, predominantly due to the stability of nests, as they were made with a sand-soil mix. We also acknowledge that the colony sizes attained in our maturation experiments may be smaller than those of naturally matured colonies. This trend was observed generally in lab-reared colonies and could be attributed to differences in microclimatic conditions, foraging opportunities, space availability, and other factors. We have explicitly described these details in the revised version of the manuscript.

Reviewer #1 (Recommendations for the authors):

The experimental design is fantastic. The large quasi-2D should allow for the direct visualization of the movements of individuals and the creation of the nest, and the inclusion of non-workers (specifically, a mated queen and pupae) is new and important. However, I have some questions and concerns about the results, as outlined below. Also, I found the paper difficult to read, and the connections between the various experiments and the model were not always clear. 

We thank the reviewer for the time and effort dedicated to reviewing our manuscript. We have modified the manuscript substantially to address the comments and readability. 

The assumption that the digging rate is constant across ants may be a strong one. Previous work (see, for instance, Aguilar, et al, Science 2018) has demonstrated a very heterogeneous workload distribution among ants. I am not sure what implications that may have for the results here, but the authors should comment on this choice. Related to the point above, given a constant digging rate, the variation in digging is attributed to an age-dependent "desired target area". Can the authors comment on the implications of this, specifically in contrast to a variable digging rate? The distinction between digging rate differences and target area differences seems to be important for the authors. However, the way this is presented, it is difficult to fully understand or appreciate this importance and its implications. What is the consequence of this difference, and why is this important?

We apologize to the reviewer for the confusion.

Our model does not assume that the digging rate (da/dt, Equation 1) remains constant throughout the experiment. Instead, we only treat the basal digging rate (r) as a constant.

The variable digging rate (da/dt, Equation 1) is derived by multiplying the basal rate constant (r) by the term (1 - a/a_age), which accounts for deviations from the age-dependent target area that the ants aim to achieve. This makes the actual digging rate dynamic, as it responds to changes in excavated area (e.g., expansion or rapid collapse)

For example, according to our model (Equation 1), two ants with the same basal digging rate (r) may exhibit markedly different actual digging rates at a given time if they differ in age. This occurs because the variable digging rate (da/dt) depends not only on ‘r’ but also on the age-dependent term (1 - a/a_age). Also, we emphasize that the use of a basal digging rate constant aligns with prior studies (refs. 24, 29, 30).

In our work, we demonstrate that after a collapse event, ants of all ages dig at rates comparable to those observed in the initial (pre-collapse) phase of the experiment. This occurs because the ants are far from their age-dependent target area, effectively resetting their digging behavior. By comparing maximum digging rates pre- and post-collapse, we provide strong empirical evidence that this rate is age-independent (SI Fig. 6A, 6B), supporting the conclusion that the basal digging rate constant (r) is a fundamental property of the ants' behavior, unaffected by age.

We agree with the reviewer that individual tracking of ants within our experimental setup would have been the ideal approach. Then, we could have taken the inter-individual variability of the digging activity into account. However, we were limited to doing so by the technical and practical limitations of the setup, such as; 

(a) Continuous tracking of ants in our nests would have required a camera to be positioned at all times in front of the nest, which necessitates a light background. Since Camponotus fellah ants are subterranean, we aimed to allow them to perform nest excavation in conditions as close to their natural dark environment as possible. Additionally, implementing such a system in front of each nest would have reduced the sample sizes for our treatments.

(b) The experimental duration of our colony maturation experiments extended for up to six months (unprecedented durations in these kinds of measurements). These naturally limited our ability to conduct individual tracking while maintaining the identity of each ant based on the current design.

In light of these points, the following lines are added to the discussion (line numbers: 283-295), signifying the above points:

“Our age-dependent model demonstrates that the digging behavior in Camponotus fellah is governed by a basal digging rate constant (r) modulated by the age-dependent feedback (1 − a/aage). Crucially, we show that after a collapse, the maximum digging rates return to their pre-collapse levels, suggesting that this basal rate ’r’ represents an age-independent ceiling on how fast ants can dig, regardless of age or context (SI Fig. 6 A, B). Previous studies have demonstrated both homogeneous and heterogeneous workload distribution, with varying digging rates among ants (24, 29, 30, 35). Studies showing heterogeneous workload distribution relied on continuous individual tracking of ants to quantify digging rates (35). However, this approach was not feasible in our current design due to the experimental durations of both our colony maturation and fixed demographics experiments. Additionally, sample size requirements naturally limited our ability to conduct continuous individual tracking during nest construction in our study. Thus, based on empirical measurements from our fixed-demographics experiments and supported by the age-independent post-collapse digging rates, we adopted a constant basal digging rate for simulating our age-dependent model—an assumption aligned with both prior literature and the collective dynamics observed in our system (24,29,30)”.

Model: as presented, the model seems to lack independent validation. The model seems to have built-in that there is an age-dependent target area, and this is what is recovered from the model. I am failing to see what is learned from the model that the experiments do not already show. Also, the model has no ant interactions, though ants are eusocial and group size is known to have a large effect on behavior (this is acknowledged by the authors at the beginning of the discussion). Can the authors comment on this?My recommendation would be to remove the model from this paper or improve the text to address the above comments.

We did not draw the conclusion of the age-dependent target area from our model. We used the fixed demographics experiments to quantify the age-dependent area target as a function of the age of individuals. We then used this age-dependent area target in our model to quantify the excavation dynamics of the colony maturation experiments, where ants span a variety of ages, as the nest population changes over time, resulting in natural variation in the ages of individuals within the nest.  These results could not have been obtained by performing any of the individual experiments, whether colony maturation or the fixed demographics, young or old, on their own. The need for different age demographics was crucial to quantify the age-dependent effects in nest excavation, which were lacking in previous studies. 

First, the age-dependent model provides a very good estimate for the natural growth of the nest.  More importantly, after fixing an age threshold of 56 days (mean + standard deviation of the young ant age), the model provides an estimate of which ants are doing the majority of the digging during natural nest expansion. This teaches us that during natural expansion, the older ants are far from their density target and therefore do not engage in any substantial digging, which is shown in Figure 4. C. 

On the other hand, the younger ants are close to their area targets and induced to dig. Indeed, the target area fitted for the age-independent model closely approximates the empirically measured age-dependent target when extrapolated to very young ants. This provides further support for the idea that, in the colony maturation experiments, the youngest ants are responsible for most of the digging.

Our model is a simple analytical model, inspired by earlier models that used a fixed area target (such as density models) for nest construction. However, because we knew the precise age of workers in our experiments, we were able to obtain age-dependent area targets, thereby challenging the use of a constant area target (as employed in prior studies) in light of our findings from the fixed demographics of young and old colonies.

Empirically Quantifiable Parameters: We wanted our model to have empirically quantifiable parameters. Since we did not continuously record the experiment, we could not quantify agent-agent interactions, pheromonal depositions, or similar factors.

Minimal Model Design: We aimed to keep the model as minimal as possible, which is why we did not include complex interactions such as those found in continuous tracking experiments.

However, the model does set up some interesting hypotheses that could easily be tested with the experimental setup (e.g., marking the ants / tracking individual activity levels). For instance, it is hypothesized that older ants dig less often, but when they do dig, they do so at the same rate. Given the 2D setup, the authors could track individual ants and test this hypothesis. Also, if the desired target area does decrease with age, the authors could verify this hypothesis by placing older ants into arenas with different-sized pre-formed nests to observe how structure is changed to achieve the desired area/ant.

We thank the reviewer for this comment.

We believe that the confusion with the usage of a constant basal digging rate is resolved now. To briefly reiterate, ants dig at variable rates that can be decomposed to a (constant on short time scales but age-dependent) basal rate times the (variable) distance from the density target. The suggested experiments are beyond the scope of our current study, and further studies could utilize the suggested experimental design with better time-resolved imaging for individual ant tracking that could verify the predictions from our model. 

Specific comments:

Title:

The title suggests a broad result, yet the study focuses on one ant species. Please modify the title to more accurately reflect the scope of the work.

We thank the reviewer for the comment.

The title is modified as “Colony demographics shape nest construction in Camponotus fellah ants.”

Introduction:

Important information and context are missing about this ant species. For instance, please add the following about this species in the introduction:

What is their natural habitat and substrate? How does the artificial soil compare?

What is their (rough) colony size? [later, discuss experiment group size choice and potential insights/limitations of results when applied to the natural system].

The details have been added to the introduction (line numbers : 49-55) and the materials and methods section (Study species).

“Camponotus fellah ants are native to the Near East and North Africa, particularly found in countries like Israel, Egypt, and surrounding arid and semi-arid regions, where they prefer to nest in moist, decaying wood, including tree trunks, branches, or stumps (49,50). The species lives in monogynous colonies with tens to thousands of individuals. Nests are commonly found in a sand-loamy mix, which is a combination of sand, soil, clay, or gravel, providing structural stability and moisture retention (51). They are typically found under rocks, in the crevices of dried vegetation, or dry, sandy soils, sometimes in areas with loose gravel, with a colony size ranging from tens to thousands of workers”.

What is the natural life expectancy of a worker? A queen? [later, discuss fixed demographic age choices in this context and/or why were age ranges chosen for experiments?].

The lifespan of ants, including both queens and workers, varies significantly based on caste, species, and environmental conditions.

(1) Queen Longevity: From the literature, Camponotus fellah queens can live up to 20 years, with one documented case reaching 26 years (50). 

(2) Worker Longevity: In contrast to queens, the lifespan of workers is much shorter. Lab studies on Camponotus fellah (82) and other Camponotus species (83) suggest that workers can live for several months depending on environmental conditions, colony health, and caste-specific roles (e.g., minor vs. major workers)

(3) Laboratory vs. Natural Conditions: Worker longevity is highly variable between laboratory and natural conditions

Therefore, in the context of the old worker lifespan in our experiments, ~200 days (roughly 6–7 months), we strongly believe that the worker lifespan used in our experiments represents a substantial portion of a worker's expected life. While exact figures for C. fellah workers are unavailable, inferences from related species suggest that workers nearing 200 days are approaching the latter stages of their lifespan, making them meaningfully "old". 

The details are added to the main text (line numbers: 124-127) and discussion (line numbers: 278-282).

Why was this species chosen? Convenience, or is there something special about this species that the readers should know? Specifically, is there something that might make the results more general or of broader interest?

Camponotus fellah was chosen for this study because it is native to Israel, making it convenient to collect and maintain in the lab. Additionally, its nuptial flights occur close to the study location, ensuring a steady supply of colonies. We were able to provide them with a nesting substrate similar to what they naturally use, as their nests are typically found in a sand-loamy mix, similar to the sand-soil mix in our artificial nests. This was possible because we had the opportunity to observe their habitat and nesting behavior in the wild, allowing us to gather preliminary information on their natural nesting conditions.

Results:

Line 60: "several brood items" - how many exactly? Was this consistent across experiments? Do mated queens ever produce more pupae during the experiments?

Yes, the number of brood items (5) was added consistently across the experiments. Additionally, the mated queen did produce pupae during the course of the experiments, which was evident from the noticeable increase in the number of workers in the nest. This was significantly higher than the number of brood items present at the start of the study.

The above points are added to the section (line numbers : 68-69).

Figure 1: Panel A - The food ports are never mentioned in the text. Are the ants fed during the experiments? If so, what? With what frequency? Is the water column replenished/maintained? If so, how and how often? panel C - how long did this experiment last?

We thank the reviewer for pointing this out. We have now updated the nest maintenance section in the Materials and Methods (line numbers : 349-354) part to include all the necessary details and clarifications.

“We provided food to the ants ad libitum through three separate tubes containing water, 20 % sucrose water, and protein food. The protein mixture included egg powder, tuna, prawns, honey, agar, and vitamins. Each of the three tubes was filled with 5 ml of their respective contents and sealed with a cotton stopper to prevent overflow. The tubes were positioned at a slight angle and connected using a custom-made plexiglass adapter to facilitate the flow of liquids. These tubes were replenished once depleted, and regularly replaced once the nest maintenance was carried out bi-weekly.”

Line 76: "...excavation was commenced by the founding queen". How were the queen and pupae introduced into the system?

We initiated colony maturation experiments by introducing a single mated queen and several brood items (pupae) at random positions on the soil layer of the nest (line numbers : 68-69)

Line 87: Please provide bounds for 11cm2/ant value. Is there any biological or physical justification for this number?

We thank the reviewer for the suggestion. We have now provided the bounds as requested (line numbers : 97-101). 

We were unable to pinpoint a specific biological justification based solely on this treatment. However, on extrapolating the age-dependent area fit we derived from the fixed demographics experiment, we found that at the age of 1 day, an ant has a target area of approximately 11.17 cm², which is the largest age-dependent area target possible within our experimental setup.

From the colony maturation experiment, we obtained the value of  11.6 (±1.15) cm² as the area per ant. The consistency between the area per ant obtained from two completely different treatments across different colonies yielded similar results. We propose that under standardized conditions, a 1-day-old ant has a theoretical maximum target area of 11.17 cm²—the highest value observed in our experimental framework.

Lines 98-99: "one straightforward possibility would be that newborn ants are the ones that dig". This statement contradicts the results presented in Figures 1 and S1 - the population increase seems to occur at least a few days before increased excavation in nearly all cases.

We apologize for any confusion caused by our initial phrasing. To clarify, we proposed that a lag likely exists between population growth and nest area expansion. This lag could arise from two sequential processes: (1) newborn ants require time to mature and become active (first delay), and (2) digging to expand the nest takes additional time (second delay; estimated at ~10 days from the cross-correlation analysis). Thus, our results suggest that it is not the population that lags behind the area, but rather the area that lags behind the population, as demonstrated in Figures 2D and SI. Figure. S1.

The sentence “one straightforward possibility would be that newborn ants are the ones that dig” is modified as below (line numbers : 112-119) to prevent further confusion.

“One possible explanation is that, although all ants are capable of digging, it is primarily the newly emerged ants who perform this task. In this case, nest expansion would lag behind colony growth due to two delays: first, the time needed for young ants to mature enough to begin digging, and second, the physical time required to excavate additional space (e.g., around 10 days). This mechanism could eliminate the need for ants to assess overall colony density, as each new group of active workers simply enlarges the nest as they become ready. An alternative possibility is that all ants, regardless of age, respond to increased density by initiating excavation. In that scenario, nest expansion would follow more immediately after the emergence of new individuals, making delays less prominent (24, 29, 30)”.

Line 105: How do group sizes compare to natural colony size? Line 106: How do "young" and "old" classifications compare to natural life expectancy?

We have already addressed this question in an earlier comment. The details are added to the main text (line numbers: 124-127) and discussion (line numbers: 278-282).

Line 118-119: How are nests artificially collapsed?

We have added a new section in the Materials and Methods section that describes the nest collapsing procedure (Nest artificial collapse - line numbers : 386-399).

Figure 2 Panel A: The white dotted line is nearly impossible to see. Please use a more visible color.

We thank the reviewer for the comment.

We changed the solid circles to violet and the dotted line color to continuous white.

Figure 3: The use of circle markers as post-collapse recovery in young and old as well as old pre-collapse is confusing. Use different symbols for old pre-collapse vs young and old post-collapse.

We thank the reviewer for pointing out the confusion. We have revised the figure markers as suggested and modified the main text accordingly.

• Young; pre-collapse : star

• Young; post-collapse : diamond

• Old; pre-collapse : circle

• Old; post-collapse: triangle.

Figure 3 Panel C: Indicate that fixed demographic values here are pre-collapse. Also, as presented, it appears that there is a large group-size dependence that is not commented on. Previous results (Line 87 and Figure 2C) suggest a constant excavation area per ant of 11cm2/ant. Figure 3, panel C appears to suggest a group-size dependence. If these values are divided by group size, is excavated area per ant nearly constant across groups? How does the numerical value compare to the slope from Figure 2C?

We thank the reviewer for their insightful comments.

First, we would like to clarify that the area target of 11.1 (±1) cm²/ant, as described in Line 87, was obtained from the colony maturation experiments. In these experiments, we were unable to track the age of each individual ant, so the area target was calculated by normalizing the total excavated area by the number of ants.

We normalized the excavated area by the group size for both young and old colonies as suggested, and found that the area per ant was not significantly different across the group sizes (see new SI Fig. 5A). This indicates that the excavated area per ant remains relatively constant within each demographic group. Moreover, this shows that the total excavated area is proportional to group size, in agreement with previous works (24, 29, and 30). 

We have explicitly described the above information in the line numbers: 142-146

Regarding the slope comparisons, the slope of Figure 2C (10.71), from the colony maturation experiments, is the largest, followed by the area per ant from the short-term young (8.79 ± 0.98) cm²/ant, and short-term old experiments (5.16 ± 0.44) cm²/ant.

Lines 128-129: "...younger ants aim to approach a higher target area". Seems hard to know what they "aim" to do... rephrase to report what they are observed to do.

We thank the reviewer for the comment. The sentence is rephrased as suggested (line numbers : 158-161).

“In the previous sections, we showed that in fixed-demographics experiments, younger ants excavated a significantly larger nest area compared to older ants (Fig. 3. C).  This difference emerged despite similar temporal patterns in digging rates across age groups, with excavation activity peaking within the first 7 days before asymptotically decaying as nest expansion approached saturation (SI Fig. 8).”

Lines 133-141: The model description is not clear. Specifically, what parameters are ant-dependent? How does A relate to a?

We appreciate the reviewer's request for clarification. In our model:

(1) Equation 1 describes the change in the excavated area due to the digging activity of a single ant. Here, the variable 'a' represents the area excavated by one ant. This formulation allows us to capture the individual digging behavior and its impact on the excavation process.

(2) Equation 2 extends this concept to the total area excavated in the nest, denoted by 'A'. Specifically, 'A' is the sum of the areas excavated by all ants present in the nest. In other words, it aggregates the individual contributions of each ant, linking the microscopic digging behavior to the macroscopic excavation dynamics.

Therefore, the relationship between 'a' and 'A' is as follows:

●     'a' = Area excavated by a single ant.

●     'A' = ∑ 'a' (Summed over all ants in the nest).

We have explicitly mentioned this in the line numbers “ 161-179”, and describe the model assumptions and parameters in detail.

Figure 4:

Figure 4, Panel A: The equation quoted in the caption does not match the data in the figure. The equation has a positive slope and negative intercept, while the figure has a negative slope and a positive intercept. Please provide the correct equation and bounds on fit parameters.

We thank the reviewer for spotting this typing mistake.

The equation was already updated in the reviewed preprint published online. The correct equation and the fit bound are provided in the figure caption.

“Target areas decrease linearly with the ant age (y = −0.032x + 11.22 , 95 % CI (Intercept : (-0.035,-0.027), Slope : (10.53,11.91)), R2 = 0.96 ).”

Figure 4, Panel A: There seem to be three "fixed target area per ant values" in the paper: around 11cm2/ant (line 87), 11.6 cm2/ant (SI Figure 2), and linearly dependent value from fit to Figure 4A. The distinctions between these values and their significance are hard to keep track of. Can the authors add a discussion somewhere that helps the reader better understand? Is there a way to connect/rationalize/explain these different values in terms of demographics?

We thank the reviewer for the suggestion.We have added a paragraph in the discussion (line numbers : 270-277) describing the area targets.

“In our colony maturation experiments, we found that area per ant was highest when the workers were youngest, with values around 11.1–11.6 (±1–1.15). This aligns with observations from naturally growing nests, where newly eclosed ants dominate the population and nest volumes are relatively large. Supporting this, fixed-demographics experiments showed that the area excavated per ant declines linearly with worker age, indicating that the youngest ants contribute most to excavation. Notably, the target area we fit for the age-independent model (11.6 ± 1.15) closely matches the extrapolated value for very young workers (Fig. 4. A), reinforcing the idea that young ants are the primary excavators during early colony growth. In contrast, during events like collapses or displacement, when space is urgently needed, ants of all ages participate in excavation.”

Figure 4, Panel A: What are various symbols and colors for data with error bars? If consistent with Figure 3, then this panel and subsequent model confound two factors: (1) the age dependence and (2) the behavioral differences pre- and post-collapse (structures are different pre-and post-collapse, according to SI Figure 6; line 120: "...colonies ceased digging when they recovered 93{plus minus}3% of the area lost by the manual collapse..."; lines 201-202: "We find significant quantitative and qualitative differences between nests constructed within this natural context and nests constructed in the context of an emergency") and behavior is different (according to SI Figure 7 and line 119: "...all ants dig after collapse...")). Therefore, without further supporting evidence, it does not seem that these data should be used to fit a single line that defines a model parameter a_age for each ant in equation 2.

The symbols are the area per ant quantified from the fixed demographics of young, and old experiments. The symbols show the following;

A.  Star - Young, pre-collapse

B.  Diamond - Young, post-collapse 

C.  Circle - Old, pre-collapse

D.  Triangle - Old, post-collapse.

The details are clearly described in the figure caption. 

We apologize to the reviewer for the confusion. We argue that the data can be fit by a single line to quantify the parameter ‘a_age’ as follows. 

A. All data presented in Figure 4A were obtained from the same fixed-demographics experiments (containing only young and old ants) under experimental collapse conditions, pre- and post-collapse. These results, therefore, exclusively reflect emergency nest-building behaviors during emergency scenarios and do not include any observations from natural colony maturation processes.

B. Age-dependent excavation differences: As correctly noted by the reviewer, the observed difference in excavated area before versus after collapse reflects the natural aging of ants in our experimental colonies. While colonies recovered >90% of lost area post-collapse, the residual variation was not negligible—instead, it systematically correlated with colony age structure. By tracking colonies across this demographic transition, we obtained additional data points spanning a broader developmental spectrum. This extended range strengthened our ability to detect and quantify the linear relationship between worker age and excavation output.

C.The quoted sentence (lines 201-202, submitted version) refers to comparisons across all three experimental cases: (1) fixed-demographics young ants, (2) fixed-demographics old ants, and (3) the natural scenario (mixed-age colonies). Importantly, these comparisons are based on pre-collapse steady-state excavation areas, ensuring a consistent baseline across treatments. We highlight quantitative and qualitative differences between these distinct experimental groups, not between pre- and post-collapse phases within the same treatment. The pre- and post-collapse data within fixed-demographics groups were analyzed separately to avoid conflating aging effects with emergency responses.

To avoid confusion, the whole paragraph in the discussion (line numbers : 253-260) is rephrased.

In lines 201-202; “We find significant quantitative and qualitative differences between nests constructed within this natural context and nests constructed in the context of an emergency”. 

Here, by natural context, we mean the nests excavated in the colony maturation experiments. We believe that it could have been confusing, and the sentence is modified as answered for the previous question. 

Figure 4, Panel B: This uses the model with a_age determined by from Figure 4A and the life table (as shown in the supplemental), whereas the supplemental Figure SI 8 uses the fixed blue line a_age value for the model, which comes from the colony maturation experiments. The age-independent model in the supplemental fits the data better, yet the authors claim the supplemental model cannot be applied to the data because of their experimentally determined age-dependent target area. Given the age-independent target area model fits better, additional evidence/justification is needed to support the choice of the model.

We agree with the reviewer that the age-independent model fits the data well. However, we believe that the fixed area target cannot be used to explain the excavation dynamics for the following reasons.

We make an important assumption in our model: that the ants rely on local cues and that individual ants can not distinguish between the fixed demographics and colony maturation experiments (line numbers : 161-166). Given this assumption, the ants cannot change their behavior between experiments, meaning the same model should fit all of our results. However, the fixed demographics experiments revealed a significant difference in the areas excavated by young vs. old cohorts, despite having the same group size. If the ants regulated the excavated area based on an age-independent constant density target model, then the excavated area in the fixed demographics of young and old colonies would have been similar. This discrepancy indicates that the target area per ant is not constant, as assumed in the age-independent density model (SI. Fig. 8). We emphasize that while the age-independent model provides a better fit for the excavated area in colony maturation experiments, the age-dependence of excavation is empirically supported by fixed-demographics experiments. Therefore, we implemented this age-dependence through a variable target area within the age-dependent model framework to explain excavation dynamics in the colony maturation experiments.

These details are explicitly mentioned in the main text (line numbers : 187 - 198)

Figure 4, Panel C: Is this plot entirely from the model, or are the data points measured from experiments? Please label this more clearly.

We apologize to the reviewer for the confusion.

The Figure 4C is based on the age-dependent digging model. We applied the model to population data from the long-term experiments (n = 22). By setting an age threshold of 56 days (since ants used in the short-term young experiment had an average age of 40 ± 16 days), we categorized the ants into young and old groups. We then quantified the area dug by the young ants, the queen, and the old ants in terms of the percentage of the total area excavated. We hypothesized that, because young ants have a lower digging threshold, they would perform the majority of the digging. We indeed confirm this in Figure 4C.

This information is added to the main text and described in detail (line numbers: 200 - 208).

Lines 162-165: "...Furthermore, we quantified the area dug by each ant in the normal colony growth experiment as estimated from the age-dependent model and found that all ants excavated more or less the same amount...". Figure 4D shows a distribution with significant values ranges from 1-16 cm2... how is this interpreted as "more or less the same amount" and what is the significance of this?

We apologise to the reviewer for the confusion.

We quantified the percentage contribution to the excavated area of each histogram bin (provided in the new SI table: 4), and found that the area excavated between 5 cm² and 13 cm² accounts for 73.76% of the total excavated area. This indicates that most ants dug within this range rather than exhibiting extreme variations. Additionally, the mean excavation amount is 7.84 cm², with a standard deviation of 3.44 cm², meaning that most values fall between 4.4 cm² and 11.28 cm², which aligns well with the 5–13 cm² range. Since the majority of the excavation is concentrated within this narrow interval, and the mean is well centered within it, this suggests that ants excavated more or less the same amount, rather than forming distinct groups with highly different excavation behaviors.

We have modified the main text (line numbers: 209-216) to include these points.

The biological significance of this finding is that since all ants in the colony maturation experiments are born inside the nest, we hypothesize that they should excavate similar amounts. To test this, we quantified the area contribution of each ant over the entire duration of the experiment using the age-dependent digging model as described above and found that they indeed excavated more or less the same amount. From our analysis of fixed demographics experiments, we showed that the youngest ants excavate the largest area. Since the majority of the youngest ants participated in the colony maturation experiments, this further supports our hypothesis.

Figure 5.

Figure 5, Panels A-C: Please provide a scale bar. 

The scale bar is provided in the figure as suggested. The algorithm for the cutoffs for tunnel vs wide tunnels is described in detail in the section “Nest skeletonization, segmentation, and orientation.”

Figure 5, Panel E: Why does the chamber error bar for 5 ants go to zero?

In Figure 5, E, we plot the standard error, as described in the figure caption. In the experiments, the chamber area contributions were (0,0,39.94,0) respectively. The mean of the 4 numbers is 9.985, the standard deviation is 19.97, and the standard error is 9.985. So, the mean and the standard error are the same, so the lower error bar goes to zero, and the upper error bar goes to 19.97. This implies that in these experiments, the chamber area is often zero.

Figure 5, Panel I: Why are there no chambers for young colonies in I when they are in the histogram in E?

We apologize to the reviewer for the confusion. We initially missed adding the chamber orientation data of the young colonies to Panel I, but it has now been included.

Line 212: "...densities of ants never become too high...". What is too high? Is there some connection to biological or physical constraints?

Under normal growth conditions, nest volume is kept proportional to the number of ants, ensuring that the density remains within a specific range. This prevents overcrowding, which could otherwise lead to excessively high densities.

Yes, we believe there is likely a connection to both biological and physical constraints. The proportional relationship between nest volume and the number of ants is likely driven by factors such as:

(1) Biological Constraints:

Ant Colony Size: Ants typically adjust their behavior and social structure to maintain an optimal population size relative to available resources and space.Overcrowding could lead to potentially a breakdown in colony function.

Colony Health: High densities can lead to faster epidemic spread, leading to negative effects on reproduction, foraging efficiency, and overall colony health. By maintaining density within a specific range, the colony can thrive without these adverse effects.

(2) Physical Constraints:

Spatial Limitations: The physical space within the nest limits how many ants can occupy it before space becomes constrained. The nest’s structure and size must physically accommodate the ants, and the volume must be large enough to prevent overcrowding, and efficient resource distribution.

Lines 272 and 302: How often were photos taken? These two statements seem to suggest different data collection rates.

As stated in line 272, photos were taken every 1 to 3 days. During each photo session, four photos were taken, with each photo separated by 2 seconds, as mentioned in line 302. To avoid confusion, we rephrased the sentence (line numbers: 359-361).

“We photographed the nest development every 1-3 days. During each photography session, four pictures of the nest were taken, with a 2-second interval between each.”

Reviewer #2 (Recommendations for the authors):

Some more minor points/questions/clarifications:

This might be pedantic, but I don't think the nest serves as the skeleton of the superorganism, while it does change and grow, the analogy becomes weak beyond that point. The skeleton serves to protect the internal organs of the organism, facilitates movement and muscle attachment, and creates new blood cells. I would be more comfortable with a statement that the nest can grow or shrink according to need.

We sincerely thank the reviewer for their time and effort in providing a detailed review and assessment of our manuscript. A point-by-point response to the comments is provided below.

The analogy of treating a nest structure to the skeleton of a superorganism was based on the following points;

(a) Protection: A nest protects the colony on a collective scale. This is analogous to protecting "organs" by a skeletal framework.

(b) Organization and Division of Space: The skeletal structure organizes the body's internal layout, just as nest structures are organized into various spatial compartments for various colony functions, with specific regions designated for brood chambers, food storage, and waste disposal.

Thus, we believe that the analogy can still be valid in a metaphorical way.

Does this statement need justification with a citation, or is that information contained in the subsequent clause? "However, for more complex structures where ants congregate in specific chambers, workers are less likely to assess the overall nest density." The idea that workers do (or do not) assess overall density touches on many issues, including that of perfect information and adaptive responses, that it seems it needs to be well founded in previous work to be stated in such unequivocal terms.

We thank the reviewer for this comment. The references for this argument are provided in the next sentence. We have now moved these references to the relevant sentence (reference number: 24, 29,30; line number : 30-31 ) 

Can you give some more information on this statement? "Experiments were terminated either when the queen died or when she became irreversibly trapped after a structural collapse." Why was this collapse irreversible and therefore unlike treatment 2? Did the queen die in these instances? Was this event more likely than in natural colonies? And if so, was there something inherently different about your experiments that limit interpretation under natural conditions (e.g. the narrow nature of the observation setup? The consistency of the sand?)

Our nest excavation experiments were terminated under two primary scenarios: (1) the queen died of natural causes, reflecting the baseline mortality expected when queens are brought into laboratory conditions, or (2) the nest experienced a structural collapse that left the queen irreversibly trapped. The second scenario is further elaborated below:

Irreversible Collapses: These collapses were classified as irreversible because the queen could not be rescued alive. This occurred when the structural stability of the nest failed, burying the queen in a manner that prevented recovery. In some cases, the collapse resulted in the queen's immediate death, while in others, she was trapped beyond reach, and any rescue attempt risked further structural damage.

Collapse and Experimental Context: These collapses were not uniquely associated with natural colonies or fixed-demographic experiments; rather, they occurred across various experimental setups.

The sentence is modified as below to improve clarity (line numbers : 70-72 ).

“In all instances where a collapse resulted in the queen's death or her being irreversibly trapped in the nest, the experiment was excluded from analysis starting from the point of the collapse, as such events did not reflect normal colony dynamics.”

I want to make sure I understand the following statement: "Moreover, the area excavated by the young cohorts was similar to that excavated by naturally maturing colonies at the point in which they reached the same population size (Tukey's HSD; group size: 5; p = 0.61, group size: 10; p = 0.46, group size: 15; p = 0.20)." Do I have it right that this means a group of (e.g. 10) young ants excavates an area similar to that of a group of 10 naturally maturing ants at the same age as the young ants?

Yes, the interpretation provided is correct. We apologize to the reviewer for the confusion. We have rephrased the sentence for better readability (line numbers : 146-148).

“Furthermore, the area excavated by the young cohorts was comparable to that excavated by naturally maturing colonies when they reached the same population size (Tukey's HSD; group size: 5, p = 0.61; group size: 10, p = 0.46; group size: 15, p = 0.20)”

How old do ants get? Is the 'old' demographic (~200 days) meaningfully old in the context of the overall worker lifespan? While the results certainly demonstrate there is an age effect, I would like to understand how rapid this is in terms of overall lifespan.

The lifespan of ants, including both queens and workers, varies significantly based on caste, species, and environmental conditions.

(1) Queen Longevity: From the literature, Camponotus fellah queens can live up to 20 years, with one documented case reaching 26 years. This remarkable longevity underscores the queen's central role in maintaining the colony.

(2) Worker Longevity: In contrast to queens, the lifespan of workers is much shorter.

However, specific data on worker longevity in Camponotus fellah colonies are lacking. Studies on other Camponotus species (50, 82) suggest that workers can live for several months depending on environmental conditions, colony health, and caste-specific roles (e.g., minor vs. major workers).

(3) Laboratory vs. Natural Conditions: Worker longevity is highly variable between laboratory and natural conditions

Therefore, in the context of the old worker lifespan in our experiments of, ~200 days (roughly 6–7 months) we strongly believe that the worker lifespan used in our experiments represents a substantial portion of a worker's expected life. While exact figures for C. fellah workers are unavailable, inferences from related species suggest that workers nearing 200 days are approaching the latter stages of their lifespan, making them meaningfully "old."

These details are added to the main text (line numbers : 124 - 127) and to the discussion (line numbers : 278-282)

Reviewer #3 (Recommendations for the authors):

We sincerely thank the reviewer for their time and effort in providing a detailed review and assessment of our manuscript. A point-by-point response to the comments is provided below.

L10: "fixed demographics": I find this term unclear, what does it mean, it should specify if the groups are with or without a queen.

We thank the reviewer for the comment. The sentence is modified in the abstract, and definitions are later added in detail in the introduction (line numbers : 8-10) and the Materials and Methods section (Fixed demographics colonies). 

“We experimentally compared nest excavation in colonies seeded from a single mated queen and allowed to grow for six months to excavation triggered by a catastrophic event in colonies with fixed demographics, where the age of each individual worker, including the queen, is known”.

The details of the “fixed demographics” treatments were explained in the later portion of the text (line numbers: 58-61).

L36: I think it is documented that younger individuals are the ones who involved in nest construction in many species.

Previous studies on nest construction were predominantly performed on mature colonies of specific age demographics or rather mixed demographics, where age was not considered as a factor influencing nest construction. Some studies have speculated that young ants could be the most probable ones to dig, but this has not been experimentally verified to the best of our knowledge.

L50: I do not think the colony should be called mature after only 6 months, given that colonies reach thousands of workers.

The sentence is changed as suggested (line numbers : 56-57).

“The "Colony-Maturation" experiment observed the development of colonies up to six months, starting from a single fertile queen and progressing to colonies with established worker populations.” 

L60: Where was the queen introduced? It is specified in the Methods but a word here would be helpful.

The detail is added as suggested (line numbers : 68-69).

“We initiated colony maturation experiments by introducing a single mated queen and several brood items (n = 5, across all experiments) at random positions on the soil layer of the nest.”

L106: Young vs Old workers 40 vs 171 days. Maybe cite a reference or provide a reason for the selection of those ages?

Previous studies have shown that the Camponotus fellah queens can live up to 20 years, with one documented case reaching 26 years (50). To the best of our knowledge, specific data on worker longevity in Camponotus fellah colonies in natural conditions are lacking. Lab studies on Camponotus fellah (82) and other Camponotus species (50) suggest that workers can live for several months depending on environmental conditions, colony health, and caste-specific roles (e.g., minor vs. major workers). 

We intentionally selected workers from two distinct age groups: younger ants (40 ± 16 days old) and older ants (171.56 ± 20 days old). These ages represent functionally different life stages - the younger group had completed about 25% of their expected lifespan at the start of the experiment, while the older group had lived through most of theirs (50, 82). This 4-fold age difference allowed us to compare excavation behaviors across fundamentally different phases of adult life.

Our experiments lasted for 60-90 days, during which all participating workers continued to age. To ensure all ants remained alive throughout the experiments, and given the constraints of the experimental timeline, we selected young and old workers within the specified age range. 

These details are added to the main text (line numbers :  124 -127), and the discussion (line numbers  : 278-282)

L122-123: But usually ants can vary highly in their behaviours. Can the authors comment on their choice to consider an average, implying that all ants of the same age had the same digging rates?

We thank the reviewer for the comment.

In our experiments, we could not track each worker's activity over time. As described in the methods, we took snapshots of the nest structure over days and recorded the population size of the nest. Thus, we could not capture the activity of single ants in the nest as described in the response to major comments in the reviewed preprint.

We agree that individual tracking of ants within our experimental setup would have been the ideal approach. Then, we could have taken the inter-individual variability of the digging activity into account. However, we were limited to doing so by the technical and practical limitations of the setup, such as; 

(a) Continuous tracking of ants in our nests would have required a camera to be positioned at all times in front of the nest, which necessitates a light background. Since Camponotus fellah ants are subterranean, we aimed to allow them to perform nest excavation in conditions as close to their natural dark environment as possible. Additionally, implementing such a system in front of each nest would have reduced the sample sizes for our treatments.

(b)The experimental duration of our colony maturation and fixed demographics experiments extended for up to six months (unprecedented durations in these kinds of measurements). These naturally limited our ability to conduct individual tracking while maintaining the identity of each ant based on the current design.

To clarify this, we have added the following to the discussion (line numbers: 286-292).

“Previous studies have demonstrated both homogeneous and heterogeneous workload distribution, with varying digging rates among ants (24,29,30,35). Studies showing heterogeneous workload distribution relied on continuous individual tracking of ants to quantify digging rates (35). However, this approach was not feasible in our current design due to the experimental durations of both our colony maturation and fixed demographics experiments. Additionally, sample size requirements naturally limited our ability to conduct continuous individual tracking during nest construction in our study.”

L171: A line on how the nest structure was acquired and data extracted would be welcome here.

The algorithm for the nest structure segmentation, data extraction, and analysis is added in detail to the SI section: Nest skeletonization, segmentation, and orientation. The line is modified (line numbers : 221-224) in the main text as suggested.

“We compared nest architectures by segmenting raw nest images into chambers and tunnels (see SI Section: Nest Skeletonization, Segmentation, and Orientation). Chambers were identified as flat, horizontal structures, while tunnels were narrower and more vertical in orientation (see SI Fig. 9, SI Section: Nest Skeletonization, Segmentation, and Orientation)”.  

Figure 3: Where does the data of the mean in panel C come from: is it the mean of the first 30 days, before the collapse? How is it comparable with the rest?

We apologize to the reviewer for the confusion.

In panel C, the mean values (solid stars and circles) for fixed-demography colonies (young/old groups) represent pre-collapse excavation areas. For colony maturation experiments (where no collapses were induced), we instead plot the mean saturated excavation area for each group size. This allows direct comparison of mean excavated areas across experimental conditions at equivalent colony sizes.

To improve readability, the following sentences are added to the main text (line numbers : 139 - 146 ) 

“We compared the saturated excavation areas (pre-collapse) from fixed-demographics experiments (young and old groups) with those from colony maturation experiments of the same colony sizes (Fig. 3C). We find that, for a given age cohort (young or old), the saturation areas increase linearly with the colony size (GLMM, F(35,37); p < 0.0001) (Fig. 3 C, SI. Fig 7 A). The observed proportional scaling between excavated area and group size aligns with previous studies, even though those studies did not explicitly account for age demographics (24, 29, 30). After normalizing the pre-collapse excavated area by group size for both young and old colonies, we found no significant difference in area per ant across group sizes (SI Fig. 5. A). This indicates that the excavated area per ant remains relatively constant within each demographic group”.

L209-210: I would be more parsimonious in saying that the results presented prove that the target area decreases with age, as the individual behaviour of the ants was not monitored. Suggestion: rephrase to "the target of the group decreases with age".

The sentence is rephrased as suggested (line numbers : 265-266).

“Our results reveal that this target area of the group decreases linearly with age, such that young ants are more sensitive to shortages in space.”

L246: Are C.fellah colonies really found with such few workers?

Previous studies have speculated that mature Camponotus fellah colonies are a monogynous species typically founded by a single queen following nuptial flights (50,51,82), and can range from tens to thousands of workers. However, during the founding stage (as in our experiments), colonies naturally pass through smaller developmental sizes comparable to the matured colonies.

Author response:

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

Reviewer #1 (Public review):

This work addresses an important question in the field of Drosophila aggression and mating- prior social isolation is known to increase aggression in males by increased lunging, which is suppressed by group housing (GH). However, it is also known that single-housed (SH) males, despite their higher attempts to court females, are less successful. Here, Gao et al., developed a modified aggression assay, to address this issue by recording aggression in Drosophila males for 2 hours, over a virgin female which is immobilized by burying its head in the food. They found that while SH males frequently lunge in this assay, GH males switch to higher intensity but very low-frequency tussling. Constitutive neuronal silencing and activation experiments implicate cVA sensing Or67d neurons promoting high-frequency lunging, similar to earlier studies, whereas Or47b neurons promote low-frequency but higher intensity tussling. Using optogenetic activation they found that three pairs of pC1 neurons- pC1SS2 increase tussling. While P1a neurons, previously implicated in promoting aggression and courtship, did not increase tussling in optogenetic activation (in the dark), they could promote aggressive tussling in thermogenetic activation carried out in the presence of visible light. It was further suggested, using a further modified aggression assay that GH males use increased tussling and are able to maintain territorial control, providing them mating advantage over SI males and this may partially overcome the effect of aging in GH males.

Strengths

Using a series of clever neurogenetic and behavioral approaches, subsets of ORNs and pC1 neurons were implicated in promoting tussling behaviors. The authors devised a new paradigm to assay for territory control which appears better than earlier paradigms that used a food cup (Chen et al, 2002), as this new assay is relatively clutter-free, and can be eventually automated using computer vision approaches. The manuscript is generally well-written, and the claims made are largely supported by the data.

Thank you for your precise summary of our study, and being very positive on the novelty and significance of the study.

Weaknesses

I have a few concerns regarding some of the evidence presented and claims made as well as a description of the methodology, which needs to be clarified and extended further.

(1) Typical paradigms for assaying aggression in Drosophila males last for 20-30 minutes in the presence of nutritious food/yeast paste/females or all of these (Chen et al. 2002, Nilsen et al., 2004, Dierick et al. 2007, Dankert et al., 2009, Certel & Kravitz 2012). The paradigm described in Figure 1 A, while important and more amenable for video recording and computational analysis, seems a modification of the assay from Kravitz lab (Chen et al., 2002), which involved using a female over which males fight on a food cup. The modifications include a flat surface with a central food patch and a female with its head buried in the food, (fixed female) and much longer adaptation and recording times respectively (30 minutes, 2 hours), so in that sense, this is not a 'new' paradigm but a modification of an existing paradigm and its description as new should be appropriately toned down. It would also be important to cite these earlier studies appropriately while describing the assay.

We now toned down the description of the paradigm and cited more related references.

(2) Lunging is described as a 'low intensity' aggression (line 111 and associated text), however, it is considered a mid to high-intensity aggressive behavior, as compared to other lower-intensity behaviors such as wing flicks, chase, and fencing. Lunging therefore is lower in intensity 'relative' to higher intensity tussling but not in absolute terms and it should be mentioned clearly.

We have modified the description as suggested.

(3) It is often difficult to distinguish faithfully between boxing and tussling and therefore, these behaviors are often clubbed together as box, tussle by Nielsen et al., 2004 in their Markov chain analysis as well as a more detailed recent study of male aggression (Simon & Heberlein, 2020). Therefore, authors can either reconsider the description of behavior as 'box, tussle' or consider providing a video representation/computational classifier to distinguish between box and tussle behaviors.

Indeed, we could not faithfully distinguish boxing and tussling. To address this concern, we now made textual changes in the result section we occasionally observed the high-intensity boxing and tussling behavior in male flies, which are difficult to distinguish and hereafter simply referred to as tussling.

We also added this information in the Materials and Methods section Tussling is often mixed with boxing, in which both flies rear up and strike the opponent with forelegs. Since boxing is often transient and difficult to distinguish from tussling, we referred to the mixed boxing and tussling behavior simply as tussling.

(4) Simon & Heberlein, 2020 showed that increased boxing & tussling precede the formation of a dominance hierarchy in males, and lunges are used subsequently to maintain this dominant status. This study should be cited and discussed appropriately while introducing the paradigm.

We now cited this important study in both the Introduction and Discussion sections.

(5) It would be helpful to provide more methodological details about the assay, for instance, a video can be helpful showing how the males are introduced in the assay chamber, are they simply dropped to the floor when the film is removed after 30 minutes (Figures 1-2)?

We now provided more detailed description about behavioral assays and how we analyze them. For example All testers were loaded by cold anesthesia. After a 30-minute adaptation, the film was gently removed to allow the two males to fell into the behavioral chamber, and the aggressive behavior was recorded for 2 hours.

(6) The strain of Canton-S (CS) flies used should be mentioned as different strains of CS can have varying levels of aggression, for instance, CS from Martin Heisenberg lab shows very high levels of aggressive lunges. Are the CS lines used in this study isogenized? Are various genetic lines outcrossed into this CS background? In the methods, it is not clear how the white gene levels were controlled for various aggression experiments as it is known to affect aggression (Hoyer et al. 2008).

We used the wtcs flies from Baker lab in Janelia Research Campus, and are not sure where they are originated. We appreciate your concern on the use of wild-type strains as they may show different fighting levels, but this study mainly used wild-type strains to compare behavioral differences between SH and GH males. All flies tested in this study are in w+ background, based on w+ balancers flies but are not backcrossed. We have listed detailed genotypes of all tested flies in Table S1 in the revised manuscript.

(7) How important it is to use a fixed female for the assay to induce tussling? Do these females remain active throughout the assay period of 2.5 hours? Is it possible to use decapitated virgin females for the assay? How will that affect male behaviors?

We used a fixed female to restrict it in the center of food. These females remain active throughout the assay as their legs and abdomens can still move. Such design intends to combine the attractive effects from both female and food. One can also use decapitated females, but in this case, males can push the decapitated female into anywhere in the behavioral chamber. The logic to use fixed females has now been added in the Materials and Methods section of the revised manuscript.

(8) Raster plots in Figure 2 suggest a complete lack of tussling in SH males in the first 60 minutes of the encounter, which is surprising given the longer duration of the assay as compared to earlier studies (Nielsen et al. 2004, Simon & Heberlein, 2020 and others), which are able to pick up tussling in a shorter duration of recording time. Also, the duration for tussling is much longer in this study as compared to shorter tussles shown by earlier studies. Is this due to differences in the paradigm used, strain of flies, or some other factor? While the bar plots in Figure 2D show some tussling in SH males, maybe an analysis of raster plots of various videos can be provided in the main text and included as a supplementary figure to address this.

Indeed, tussling is very low in SH males in our paradigm, which may be due to different genetic backgrounds and behavioral assays. Since tussling behavior is a rare fighting form, it is not surprising to see variation between studies from different labs. Nevertheless, this study compared tussling behaviors in SH and GH males, and our finding that GH males show much more tussling behaviors is convincing. The longer duration of tussling in our paradigm may also be due to the modified behavioral paradigm, which also supports that tussling is a high-level fighting form.

(9) Neuronal activation experiments suggesting the involvement of pC1SS2 neurons are quite interesting. Further, the role of P1a neurons was demonstrated to be involved in increasing tussling in thermogenetic activation in the presence of light (Figure 4, Supplement 1), which is quite important as the role of vision in optogenetic activation experiments, which required to be carried out in dark, is often not mentioned. However, in the discussion (lines 309-310) it is mentioned that PC1SS2 neurons are 'necessary and sufficient' for inducing tussling. Given that P1a neurons were shown to be involved in promoting tussling, this statement should be toned down.

Thank you for this important comment. We now toned down the statement on pC1SS2 function.

(10) Are Or47b neurons connected to pC1SS2 or P1a neurons?

We conducted pathway analysis in the FlyWire electron microscopy database to investigate the connection between Or47b neurons and pC1 neurons. The results indicate that at least three levels of interneurons are required to establish a connection from Or47b neurons to pC1 neurons. Although the FlyWire database currently only contains neuronal data from female brains, they provide a reference for circuit connect in males.

(11) The paradigm for territory control is quite interesting and subsequent mating advantage experiments are an important addition to the eventual outcome of the aggressive strategy deployed by the males as per their prior housing conditions. It would be important to comment on the 'fitness outcome' of these encounters. For instance, is there any fitness advantage of using tussling by GH males as compared to lunging by SH males? The authors may consider analyzing the number of eggs laid and eclosed progenies from these encounters to address this.

Thank you for this suggestion. We agree with you and other reviewers that increased tussling behaviors correlate with better mating competition, but it is difficult for us to make a direct link between them. Thus, in the revised manuscript, we prefer to tone down this statement but not expanding on this part.

Reviewer #2 (Public review):

Summary

Gao et al. investigated the change of aggression strategies by the social experience and its biological significance by using Drosophila. Two modes of inter-male aggression in Drosophila are known lunging, high-frequency but weak mode, and tussling, low-frequency but more vigorous mode. Previous studies have mainly focused on the lunging. In this paper, the authors developed a new behavioral experiment system for observing tussling behavior and found that tussling is enhanced by group rearing while lunging is suppressed. They then searched for neurons involved in the generation of tussling. Although olfactory receptors named Or67d and Or65a have previously been reported to function in the control of lunging, the authors found that these neurons do not function in the execution of tussling, and another olfactory receptor, Or47b, is required for tussling, as shown by the inhibition of neuronal activity and the gene knockdown experiments. Further optogenetic experiments identified a small number of central neurons pC1[SS2] that induce the tussling specifically. In order to further explore the ecological significance of the aggression mode change in group rearing, a new behavioral experiment was performed to examine territorial control and mating competition. Finally, the authors found that differences in the social experience (group vs. solitary rearing) are important in these biologically significant competitions. These results add a new perspective to the study of aggressive behavior in Drosophila. Furthermore, this study proposes an interesting general model in which the social experience-modified behavioral changes play a role in reproductive success.

Strengths

A behavioral experiment system that allows stable observation of tussling, which could not be easily analyzed due to its low frequency, would be very useful. The experimental setup itself is relatively simple, just the addition of a female to the platform, so it should be applicable to future research. The finding about the relationship between the social experience and the aggression mode change is quite novel. Although the intensity of aggression changes with the social experience was already reported in several papers (Liu et al., 2011, etc), the fact that the behavioral mode itself changes significantly has rarely been addressed and is extremely interesting. The identification of sensory and central neurons required for the tussling makes appropriate use of the genetic tools and the results are clear. A major strength of the neurobiology in this study is the finding that another group of neurons (Or47b-expressing olfactory neurons and pC1[SS2] neurons), distinct from the group of neurons previously thought to be involved in low-intensity aggression (i.e. lunging), function in the tussling behavior. Further investigation of the detailed circuit analysis is expected to elucidate the neural substrate of the conflict between the two aggression modes.

Thank you for the acknowledgment of the novelty and significance of the study, and your suggestions for improving the manuscript.

Weaknesses

The experimental systems examining the territory control and the reproductive competition in Figure 5 are novel and have advantages in exploring their biological significance. However, at this stage, the authors' claim is weak since they only show the effects of age and social experience on territorial and mating behaviors, but do not experimentally demonstrate the influence of aggression mode change itself. In the Abstract, the authors state that these findings reveal how social experience shapes fighting strategies to optimize reproductive success. This is the most important perspective of the present study, and it would be necessary to show directly that the change of aggression mode by social experience contributes to reproductive success.

We agree that our data did not directly show that it is the change of aggression mode that results in territory and reproductive advantages in GH males. To address the concern, we have toned down the statement throughout the manuscript. For example, we made textual changes in the abstract as following

Moreover, shifting from lunging to tussling in socially enriched males is accompanied with better territory control and mating success, mitigating the disadvantages associated with aging. Our findings identify distinct sensory and central neurons for two fighting forms and suggest how social experience shapes fighting strategies to optimize reproductive success.

In addition, a detailed description of the tussling is lacking. For example, the authors state that the tussling is less frequent but more vigorous than lunging, but while experimental data are presented on the frequency, the intensity seems to be subjective. The intensity is certainly clear from the supplementary video, but it would be necessary to evaluate the intensity itself using some index. Another problem is that there is no clear explanation of how to determine the tussling. A detailed method is required for the reproducibility of the experiment.

Thank you for this important suggestion. We now analyzed duration of tussling and lunging, and found that a lunging event is often very short (less than 0.2s), while a tussling event may last from seconds to minutes. This new data is added as Figure 2G. In addition, we also provided more detailed methods regarding to tussling behavior

.<br /> Reviewer #3 (Public review):

In this manuscript, Gao et al. presented a series of intriguing data that collectively suggest that tussling, a form of high-intensity fighting among male fruit flies (Drosophila melanogaster) has a unique function and is controlled by a dedicated neural circuit. Based on the results of behavioral assays, they argue that increased tussling among socially experienced males promotes access to resources. They also concluded that tussling is controlled by a class of olfactory sensory neurons and sexually dimorphic central neurons that are distinct from pathways known to control lunges, a common male-type attack behavior.

A major strength of this work is that it is the first attempt to characterize the behavioral function and neural circuit associated with Drosophila tussling. Many animal species use both low-intensity and high-intensity tactics to resolve conflicts. High-intensity tactics are mostly reserved for escalated fights, which are relatively rare. Because of this, tussling in the flies, like high-intensity fights in other animal species, has not been systematically investigated. Previous studies on fly aggressive behavior have often used socially isolated, relatively young flies within a short observation duration. Their discovery that 1) older (14-days-old) flies tend to tussle more often than younger (2-days-old) flies, 2) group-reared flies tend to tussle more often than socially isolated flies, and 3) flies tend to tussle at a later stage (mostly ~15 minutes after the onset of fighting), are the result of their creativity to look outside of conventional experimental settings. These new findings are keys for quantitatively characterizing this interesting yet under-studied behavior.

Precisely because their initial approach was creative, it is regrettable that the authors missed the opportunity to effectively integrate preceding studies in their rationale or conclusions, which sometimes led to premature claims. Also, while each experiment contains an intriguing finding, these are poorly related to each other. This obscures the central conclusion of this work. The perceived weaknesses are discussed in detail below.

Thank you for the precise summary of the key findings and novelty of the study, and your insightful suggestions.

Most importantly, the authors' definition of "tussling" is unclear because they did not explain how they quantified lunges and tussling, even though the central focus of the manuscript is behavior. Supplemental movies S1 and S2 appear to include "tussling" bouts in which 2 flies lunge at each other in rapid succession, and supplemental movie S3 appears to include bouts of "holding", in which one fly holds the opponent's wings and shakes vigorously. These cases raise a concern that their behavior classification is arbitrary. Specifically, lunges and tussling should be objectively distinguished because one of their conclusions is that these two actions are controlled by separate neural circuits. It is impossible to evaluate the credibility of their behavioral data without clearly describing a criterion of each behavior.

Thank you for this very important suggestion. We now provided more detailed description of the two fighting forms in the Materials and Methods section. See below

Lunging is characterized by a male raising its forelegs and quickly striking the opponent, and each lunge typically lasts less than 0.2 seconds through detailed analysis. Tussling is characterized by both males using their forelegs and bodies to tumble over each other, and this behavior may last from seconds to minutes. Tussling is often mixed with boxing, in which both flies rear up and strike the opponent with forelegs. Since boxing is often transient and difficult to distinguish from tussling, we referred to the mixed boxing and tussling behavior simply as tussling. As we manually analyze tussling for 2 hours for each pair of males, it is possible that we may miss some tussling events, especially those quick ones.

It is also confusing that the authors completely skipped the characterization of the tussling-controlling neurons they claimed to have identified. These neurons (a subset of so-called pC1 neurons labeled by previously described split-GAL4 line pC1SS2) are central to this manuscript, but the only information the authors have provided is its gross morphology in a low-resolution image (Figure 4D, E) and a statement that "only 3 pairs of pC1SS2 neurons whose function is both necessary and sufficient for inducing tussling in males" (lines 310-311). The evidence that supports this claim isn't provided. The expression pattern of pC1SS2 neurons in males has been only briefly described in reference 46. It is possible that these neurons overlap with previously characterized dsx+ and/or fru+ neurons that are important for male aggressions (measured by lunges), such as in Koganezawa et al., Curr. Biol. 2016 and Chiu et al., Cell 2020. This adds to the concern that lunge and tussling are not as clearly separated as the authors claim.

Thank you very much for this important question. Indeed, there are many experiments that could do to better understand the function of pC1SS2 neurons, and we only provide the initial characterization of them due to the limited scope of this study. My lab has been focused on studying P1/pC1 function in both male and female flies and will continue to do so.

To partially address your concern, we made the following revisions

(1) We provided higher-resolution images of P1a and pC1SS2 (Figure 4C-4E). While their cell bodies are very close, they project to distinct brain regions, in addition to some shared ones.

(2) By staining these neurons with GFP and co-staining with anti-FruM or anti-DsxM antibodies, we showed that P1a neurons are partially FruM-positive and partially DsxM-positive, while pC1SS2 neurons are DsxM-positive and FruM-negative (Figure 5A-5D).

(3) As pC1SS2 neurons are DsxM-positive and FruM-negative, we also examined how DsxM regulates the development of these neurons. We found that knocking down DsxM expression in pC1SS2 neurons using RNAi significantly affected pC1 development regarding to both cell numbers (Figure 5G) and their projections (Figure 5H).

(4) We further found that DsxM in pC1SS2 neurons is crucial for executing their tussling-promoting function, as optogenetic activation of these neurons with DsxM knockdown failed to induce tussling behavior in the initial activation period, and a much lower level of tussling in the second activation period compared to control males (Figure 5I-5K).

(5) While it is very difficult to identify the upstream and downstream neurons of P1a and pC1SS2 neurons, we made an initial step by utilizing trans-tango and retro-Tango to visualize potential downstream and upstream neurons of P1a and pC1SS2 (Figure 4-figure supplement 2), which certainly needs future investigation.  

While their characterizations of tussling behaviors in wild-type males (Figures 1 and 2) are intriguing, the remaining data have little link with each other, making it difficult to understand what their main conclusion is. Figure 3 suggests that one class of olfactory sensory neurons (OSN) that express Or47b is necessary for tussling behavior. While the authors acknowledged that Or47b-expressing OSNs promote male courtship toward females presumably by detecting cuticular compounds, they provided little discussion on how a class of OSN can promote two different types of innate behavior. No evidence of a functional or circuitry relationship between the Or47b pathway and the pC1SS2 neurons was provided. It is unclear how these two components are relevant to each other.

It has been previously found that Or47b-expressing ORNs respond to fly pheromones common to both sexes, and group-housing enhances their sensitivity. Regarding to how Or47b ORNs promotes two different types of innate behaviors, a simple explanation is that they act on multiple second-order and further downstream neurons to regulate both courtship and aggression, not mentioning that neural circuitries for courtship and aggression are partially shared. We did not include this in the discussion as we would like to focus on aggression modes, and how different ORNs (Or47b and Or67d) mediate distinct aggression modes.

Regarding to the relationship between Or47b ORNs and pC1_SS2 neurons, or in general ORNs to P1/pC1, it is interesting and important to explore, but probably in a separate study. We tried to conduct pathway connection analyses from Or47b to pC1 using the FlyWire database, and found that Or47b neurons can act on pC1 neurons via three layers of interneurons. Although the FlyWire database currently only contains neuronal data from female brains, they can provide a certain degree of reference. We hope the editor and reviewers would agree with us that identifying these intermediate neurons involved in their connection is beyond this study.

Lastly, the rationale of the experiment in Figure 5 and the interpretation of the results is confusing. The authors attributed a higher mating success rate of older, socially experienced males over younger, socially isolated males to their tendency to tussle, but tussling cannot happen when one of the two flies is not engaged. If, for instance, a socially isolated 14-day-old male does not engage in tussling as indicated in Figure 2, how can they tussle with a group-housed 14-day-old male? Because aggressive interactions in Figure 5 were not quantified, it is impossible to conclude that tussling plays a role in copulation advantage among pairs as authors argue (lines 282-288).

Indeed, we do not have direct evidence to show it is tussling that makes socially experienced males to dominate over socially isolated males. To address your concern, we have made following revisions

(1) We toned down the statements about the relationship between fighting strategies and reproductive success throughout the manuscript. For example, in the abstract Moreover, shifting from lunging to tussling in socially enriched males is accompanied with better territory control and mating success.

(2)  Regarding to whether a SH male can engage in tussling with a GH male, we found that while two SH males rarely perform tussling, paired SH and GH males displayed similar levels of tussling like two GH males, although tussling duration from paired SH and GH males is significantly lower compared to that in two GH males (Figure 6-figure supplement 2).

(3) To support the potential role of tussling in territory control and mating competition, we performed additional experiments to silence Or47b or pC1SS2 neurons that almost abolished tussling, and paired these males with control males. We found that males with Or47b or pC1SS2 neurons silenced cannot compete over control males, further suggesting the involvement of tussling in territory control and mating competition.  

Despite these weaknesses, it is important to acknowledge the authors' courage to initiate an investigation into a less characterized, high-intensity fighting behavior. Tussling requires the simultaneous engagement of two flies. Even if there is confusion over the distinction between lunges and tussling, the authors' conclusion that socially experienced flies and socially isolated flies employ distinct fighting strategies is convincing. Questions that require more rigorous studies are 1) whether such differences are encoded by separate circuits, and 2) whether the different fighting strategies are causally responsible for gaining ethologically relevant resources among socially experienced flies. Enhanced transparency of behavioral data will help readers understand the impact of this study. Lastly, the manuscript often mentions previous works and results without citing relevant references. For readers to grasp the context of this work, it is important to provide information about methods, reagents, and other key resources.

Thank you very much for this comment and we almost totally agree.

(1) Our results suggest the involvement of distinct sensory neurons and central neurons for lunging and tussling, but do not exclude the possibility that they may also utilize shared neurons. For example, activation of P1a neurons promotes both lunging and tussling in the presence of light.

(2) We have now toned down the statements about the relationship between fighting strategies and reproductive success throughout the manuscript.

(3) We provided more detailed methods, genotypes of flies to improve transparency of the manuscript.

Reviewer #1 (Recommendations for the authors):

(1) Figure 1 Supplement 1 shows that increased aging has a linear and inverse relationship with the number of lunges, this is in contrast to a previous study from Dierick lab (Chowdhury, 2021), where using Divider assays they showed that aggressive lunges increased up to day 10 and subsequently decreased in 30-day old flies. Given that this study did not use 14-day-old flies, it might be useful to comment on this.

Thank you for this comment. Indeed, Chowdhury et al., suggested a decline of lunging after 10 days, which is not contradictory to our findings that lunging in 14d-old males is lower than that in 7d-old males. It is ideally to perform a time-series experiments to reveal the detailed relationship between ages and aggression (lunging or tussling) levels, but given our initial findings that 14d-old males showed stable tussling behavior, we prefer to use this time point for the rest of this study.

(2) For Figure 3, do various manipulations also affect the duration of tussling and boxing besides frequency and latency?

Thank you for this comment. We only analyzed latency and frequency, but not duration, as data analysis was performed manually rather than automatically on every fly pair for about 2 hours, which is very labor-consuming. We hope you could agree with us that the two parameters (frequency and latency) for tussling are representative for assaying this behavior.

(3) For Figure 3 A-F, the housing status of the males is not clearly mentioned either in the main text or the figure. What is the status of the tussling and lunging status when this housing condition is reversed when Or47b neurons are silenced, or the gene is knocked down? Do these manipulations overcome the effect of housing conditions similar to what is seen in NaChBac-mediated activation experiments?

Figure 3A-F used group-housed males and we have now added such information in the figure legends as well as Table S1.

We appreciate your suggestion on using different housing conditions. As silencing Or47b neurons or knocking down Or47b reduced tussling, it is reasonable to use GH males (as we did in Figure 3A-F) that performed stable tussling behavior, but not SH males that rarely tussle.

(4) The connections between Or47b neurons and pC1SS2 or P1a neurons can be addressed by available connectomic datasets or TransTango/GRASP approaches.

Thank you for this important suggestion. We used the FlyWire electron microscope database to analyze the pathway connections between these two types of neurons. The results indicated that there are at least three levels of interneurons for connecting Or47b and pC1 neurons. Although the FlyWire database currently only contains neuronal data from female brains, they can provide a certain degree of reference for males.

The lack of direct synaptic connection also suggests that it is challenging to resolve the connection between these two neuronal types using methods like trans-Tango/GRASP. To partially address this question, we utilized trans-Tango and retro-Tango techniques to visualize potential downstream and upstream neurons of P1a and pC1SS2 (Figure 4-figure supplement 2). Future investigations are certainly needed for clarifying functional connections between Or47b/Or67d and P1a/pC1SS2 neurons.

(5) Figure 5, 'Winning index' and 'Copulation advance index' while described in Material and Methods, should be referred to in the main text.

We now described these two indices briefly in the main manuscript, and in the Discussion section with more details.

(6) Figure 6 shows comparisons for territorial control and mating outcomes where four different housing and aging conditions are organized in a hierarchical sequence. It is not clear from the data in Figure 5, how this conclusion was arrived at. A supplementary table with various outcomes with statistical analysis would help with this.

We now added a supplementary table (Table S2) with various outcomes with statistical analysis.

Minor Comments

(1) Line 26 says that the courtship levels in SH and GH males are not different, however, unilateral wing extension is higher in SH males as compared to GH males (Pan & Baker, 2014; Inagaki et al., 2014), also it was shown that courtship attempts are higher in D. paulsitorium (Kim & Ehrman, 1998). It would be better to clarify this statement.

Indeed, it is found in some cases that SH males court more vigorously than GH males. We have added more references on this matter in the introduction.

(2) Figure 4, correct 'Tussing' to 'Tussling' or 'Box, Tussling' as appropriate.

Corrected.

(3) Duistermars, 2018 should be cited while discussing the role of vision in aggression (Figure 4). [A Brain Module for Scalable Control of Complex, Multi-motor Threat Displays]

We now cited this reference and added more discussion in the revised manuscript.

(4) Reviews on Drosophila aggression and social isolation can be cited in the introduction/discussion to incorporate recent literature e.g., Palavicino-Maggio, 2022 [The Neuromodulatory Basis of Aggression Lessons From the Humble Fruit Fly]; Yadav et al., 2024[Lessons from lonely flies Molecular and neuronal mechanisms underlying social isolation], etc.

We now cited these references in both the introduction and discussion sections.

(5) The concentration of apple juice agar should be mentioned in the methods.

We added this and other necessary information for materials in the Materials and Methods section of the study.

(6) Source of the LifeSongX software and, if available, a Github link would be helpful to include in the materials and methods section.

We now provided the source of the LifesongY software (website https//sourceforge.net/projects/lifesongy/), which is a Windows version of LifesongX (Bernstein, Adam S.et al., 1992).

Reviewer #2 (Recommendations for the authors):

(1) Major comment 1

As pointed out in the public review, the weakness of this study is that the relationship between the aggression strategy and reproductive success is an inference that is not based on experimental facts; I understand that the frequency of tussling is not so high, but at least tussling-like behavior can be observed in the territory control experiment shown in Video 3. Wouldn't it be possible to re-analyse data and examine the correlation between aggressive behavior and territory control? Even if the analysis of tussling itself in this setup is difficult, for example, additional experiments using Or47b knock-out fly or pC1[SS2]-inactivated fly could provide stronger support.

Indeed, we can only make a correlation between the type of aggressive behavior and territory control. We now toned down this statement throughout the manuscript. For example, in the abstract, we changed our conclusions as following

Moreover, shifting from lunging to tussling in socially enriched males is accompanied with better territory control and mating success. Our findings identify distinct sensory and central neurons for two fighting forms and suggest how social experience shapes fighting strategies to optimize reproductive success.

To further address the concern, we now performed additional experiments to silence Or47b or pC1SS2 neurons that almost abolished tussling, and paired these males with control males. We found that males with Or47b or pC1SS2 neurons silenced cannot compete over control males (Figure 6-figure supplement 3), further suggesting the involvement of tussling in territory control and mating competition.

In relation to the above, some of the text in the Abstract should be changed.Line 28 These findings "reveal" how social experience shapes fighting strategies to optimise reproductive success.

"suggest" is more accurate at this stage.

Changed as suggested.

(2) Major comment 2

The tussling is the central subject of this paper. However, neither the main text nor Materials and Methods section provides a clear explanation of how this aggression mode was detected. Did the authors determine this behavior manually? Or was it automatically detected by some kind of image analysis? In either case, the criteria and method for detecting the tussling should be clearly described.

The behavioral data analysis in this study was performed manually. We now provided more detailed description of the two fighting forms in the Materials and Methods section. See below

Lunging is characterized by a male raising its forelegs and quickly striking the opponent, and each lunge typically lasts less than 0.2 seconds through detailed analysis. Tussling is characterized by both males using their forelegs and bodies to tumble over each other, and this behavior may last from seconds to minutes. Tussling is often mixed with boxing, in which both flies rear up and strike the opponent with forelegs. Since boxing is often transient and difficult to distinguish from tussling, we referred to the mixed boxing and tussling behavior simply as tussling. As we manually analyze tussling for 2 hours for each pair of males, it is possible that we may miss some tussling events, especially those quick ones.

For the experimental groups where tussling cannot be observed, the latency is regarded as 120 min, but this is a value depending on the observation time. While it is reasonable to use the latency to evaluate the behavior such as the lunging that is observed at relatively early times, care should be taken when using it to evaluate the tussling. Since similar trends to those obtained for the latency are observed for Number of tussles and % of males performing tussling, it may be better to focus on these two indices.

We initially intended to provide all three statistical metrics. However, we found that using the "% of males performing tussling" would require a significantly larger sample size for subsequent statistical analysis (using chi-square tests), greatly increasing the workload. At the same time, we believe that the trend observed with "% of males performing tussling" is consistent with the other two indices, and the percentage information can also be derived from the individual sample scatter data of the other two metrics. Therefore, we opted to use "latency" and "numbers" as the statistical metrics, despite the caveat as you mentioned.

The authors repeatedly mention that tussling is less frequent but more vigorous. The low frequency can be understood from the data in Fig. 1 and Fig. 2, but there are no measured data on the intensity. As the authors mention in line 125, each tussling event appears to be sustained for a relatively long period, as can be seen from the ethogram in Fig. 2. For example, it would be possible to evaluate the intensity by measuring the duration of the tussling event.

Thank you for your valuable suggestion. We now analyzed duration of tussling and lunging, and found that a lunging event is often very short (less than 0.2s), while a tussling event may last from seconds to minutes, further supporting their relative intensities. This new data is added as Figure 2G.

(3) Minor comments

a) Line 117 How many flies were placed in one vial for group-rearing (GH)? Were males and females grouped together? Please specify in the Materials and Methods section.

We have added this information in the Materials and Methods section. In brief, 30-40 virgin males were collected after eclosion and group-housed in each food vial.

b) Line 174 The trans-Tango is basically a postsynaptic cell labeling technique. It is unlikely that the labeling intensity changes depending on neuronal activity. Do the authors want to say in this text the high activity of Or47b-expressing neurons under GH conditions? Or are they trying to show that the expression level of the Or47b gene, which is supposedly monitored by the expression of GAL4, is increased by GH conditions? The authors should clarify which is the case.

Although the primary function of the trans-Tango technique is to label downstream neurons, the original literature indicates that the signal strength in downstream neurons depends on the use of upstream neurons evidenced by age-dependent trans-Tango signals. Therefore, the trans-Tango technique can indirectly reflect the usage of upstream neurons. Our findings that GH males showed broader Or47b trans-Tango signals than SH males can indirectly suggest that group-housing experience acts on Or47b neurons. We made textually changes to clarify this.

c) Line 178 Which fly line labels the mushroom body; R19B03-GAL4?

Yes, we now provided the detailed genotypes for all tested flies in the Table S1.

d) Line 184 It was reported in Koganezawa et al., 2016 that some dsx-expressing pC1 neurons are involved in aggressive behavior. The authors should also refer to this paper as they include tussling in the observed aggressive behavior.

Thank you for this comment, and we now cited this reference in the revised manuscript.

e) Line 339 I think you misspelled fruM RNAi.

Thank you for pointing this out. fruMi refers to microRNAi targeting fruM, and we have now clearly stated this information in the main text.

f) Line 681 Is tussling time (%) the total duration of tussling occurrences during the observation time? Or is it the percentage of individuals observed tussling during the observation time? This needs to be clarified.

It is the former one. We now clearly stated this definition in the Materials and Methods section

Reviewer #3 (Recommendations for the authors):

For authors to support their conclusion that enhanced tussling among socially experienced flies allows them to better retain resources, it is necessary to quantify aggressive behaviors (mainly tussling and lunging) in Figure 5.

We agree that we can only make a correlation between enhanced tussling behavior and mating competition. We now toned down this statement throughout the manuscript. For example, in the abstract, we changed our conclusions as following Moreover, shifting from lunging to tussling in socially enriched males is accompanied with better territory control and mating success. Our findings identify distinct sensory and central neurons for two fighting forms and suggest how social experience shapes fighting strategies to optimize reproductive success.

To further address the concern, we now performed additional experiments to silence Or47b or pC1SS2 neurons that almost abolished tussling, and paired these males with control males. We found that males with Or47b or pC1SS2 neurons silenced cannot compete over control males (Figure 6-figure supplement 3), further suggesting the involvement of tussling in territory control and mating competition.

In contrast to the authors' data in Figure 4, movies in ref 36 clearly show instances of 2 flies exchanging lunges after the optogenetic activation of P1a neurons, like the examples shown in supplementary movies S1-S3. It is a clear discrepancy that requires discussion (and raises a concern about the lack of transparency about behavioral quantification).

In our study, optogenetic activation of P1^a neurons failed to induce obvious tussling behavior, and temperature-dependent activation of P1^a neurons can only induce tussling in the presence of light. These data are different from Hoopfer et al., (2015), but are generally consistent with a new study (Sten et al., Cell, 2025), in which pC1SS2 neurons but not P1a neurons promote aggression. Such discrepancy has now been discussed in the revised manuscript.

The authors often fail to cite relevant references while discussing previous results, which compromises the scholarship of the manuscript. Examples include (but are not limited to)

(1) Line 85-86 Simon and Heberlein, J. Exp. Biol. 223 jeb232439 (2020) suggested that tussling is an important factor for flies to establish a dominance hierarchy.

Reference added.

(2) Line 142-143 Cuticular compounds such as palmitoleic acid are characterized to be the ligands of Or47b by ref #18.

Reference added.

(3) Line 185-187 pC1SS1 and pC1SS2 are first characterized by ref #46. Expression data of this paper also implies that pC1SS1 and pC1SS2 label different neurons in the male brain.

We have now added this reference at the appropriate place in the revised manuscript. In addition, we have clarified that these two drivers exhibit sexually dimorphic expression patterns in the brain.

(4) Line 196-199 Cite ref #36, which describes the behavior induced by the optogenetic activation of P1a neurons.

Reference added.

(5) Line 233-235 The authors' observation that control males do not form a clear dominance directly contradicts previous observations by others (Nilsen et al., PNAS 10112342 (2002); Yurkovic et al., PNAS 10317519 (2006); also see Trannoy et al., PNAS 1134818 (2016) and Simon and Heberlein above). The authors must at least discuss why their results are different.

There is a misunderstanding here. We clearly state that there is a ‘winner takes all’ phenomenon. However, for wild-type males of the same age and housing condition, we calculated the winning index as (num. of wins by unmarked males – num. of wins by marked males)/10 encounters * 100%, which is roughly zero due to the randomness of marking.

(6) Line 251-254 The authors' observation that aged males are less competitive than younger males contradicts the conclusion in ref #18. Discussion is required.

We have now added a discussion on this matter. In brief, Lin et al., showed that 7d-old males are more competitive than 2d-old males, which is probably due to different levels of sexual maturity of males, but not a matter of age like our study that used up to 21d-old males.

(7) Line 274-275 It is unclear which "previous studies" "have found that social isolation generally enhances aggression but decreases mating competition in animal models". Cite relevant references.

Reference added.

(8) Line 309-310 The evidence supporting the statement that "there are only three pairs of pC1SS2 neurons". If there is a reference, cite it. If it is based on the authors' observation, data is required.

We have now provided additional data on the number of pC1SS2 neurons in Figure 5G of the revised manuscript.

Author response:

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

Reviewer #1 (Public Review): 

The manuscript by Feng et al. reported that the Endothelin B receptor (ETBR) expressed by the satellite glial cells (SGCs) in the dorsal root ganglions (DRG) acted to inhibit sensory axon regeneration in both adult and aged mice. Thus, pharmacological inhibition of ETBR with specific inhibitors resulted in enhanced sensory axon regeneration in vitro and in vivo. In addition, sensory axon regeneration significantly reduces in aged mice and inhibition of ETBR could restore such defect in aged mice. Moreover, the study provided some evidence that the reduced level of gap junction protein connexin 43 might act downstream of ETBR to suppress axon regeneration in aged mice. Overall, the study revealed an interesting SGC-derived signal in the DRG microenvironment to regulate sensory axon regeneration. It provided additional evidence that non-neuronal cell types in the microenvironment function to regulate axon regeneration via cell-cell interaction. 

However, the molecular mechanisms by which ETBR regulates axon regeneration are unclear, and the manuscript's structure is not well organized, especially in the last section. Some discussion and explanation about the data interpretation are needed to improve the manuscript. 

We thank the reviewer for the positive comments. We agree that the mechanisms by which ETBR signaling functions as a brake on axon growth and regeneration remain to be elucidated. We believe that unraveling the detailed molecular pathways downstream of ETBR signaling in SGCs that promote axon regeneration is beyond the scope of this manuscript. Answering these questions would first require cell specific KO of ETBR and Cx43 to confirm that this pathway is operating in SGCs to control axon regeneration. We would also need to identify how SGCs communicate with neurons to regulate axon regeneration, which is a large area of ongoing research that remains poorly understood. Our data showing that pharmacological inhibition of ETBR with specific FDA-approved inhibitors enhances sensory axon regeneration provide not only new evidence for non-neuronal mechanisms in nerve repair, but also a new potential clinical avenue for therapeutic intervention.

As suggested by the reviewer, we have extensively revised the organization of the manuscript, especially the last section of results. We have performed additional snRNAseq experiments to establish the impact of aging in DRG. We have also performed additional experiments to determine if blocking ETBR improves target tissue reinnervation. Following the reviewer’s suggestion, we have also expanded the Discussion section to discuss alternative mechanisms and o]er additional interpretation of our data. Below we describe how we address each point in detail.

(1) The result showed that the level of ETBR did not change after the peripheral nerve injury. Does this mean that its endogenous function is to limit spontaneous sensory axon regeneration? In other words, the results suggest that SGCs expressing ETBR or vascular endothelial cells expressing its ligand ET-1 act to suppress sensory axon regeneration. Some explanation or discussion about this is necessary. Moreover, does the protein level of ETBR or its ligand change during aging?  

We thank the reviewer for this point. Our results indeed indicate that one endogenous function of ETBR is to limit the extent of sensory axon regeneration. This may be a part of a mechanism to limit spontaneous sensory axon growth or plasticity and maladaptive neural rewiring after nerve injury. While the increased growth capacity of damaged peripheral axons can lead to reconnection with their targets and functional recovery, the increased growth capacity can also lead to axonal sprouting of the central axon terminals of injured neurons in the spinal cord, and to pain (see for example Costigan et al 2010, PMID: 19400724).  In the context of aging that we describe here, this protective mechanism may hinder beneficial recovery. Other mechanisms that slow axon regeneration have been reported, and include, for example, axonally synthesized proteins, which typically support nerve regeneration through retrograde signaling and local growth mechanisms. RNA binding proteins (RBP) are needed for this process. One such RBP, the RNA binding protein KHSRP is locally translated following nerve injury. Rather than promoting axon regeneration, KHSRP promotes decay of other axonal mRNAs and slows axon regeneration.  Another example includes the Rho signaling pathway, which was shown to function as an inhibitory mechanism that slows the growth of spiral ganglion neurites in culture. We have now included these examples in the Discussion section.

To address the reviewer’s second question, we have checked protein levels of ETBR and ET-1 in adult and aged DRG tissue. We observed a robust increase in ET-1 in aged DRG, while the levels of ETBR did not appear to change significantly. These results are now presented in Figure 4- Figure Supplement 1, and further support the notion that in aging, activation of the ETBR signaling hinders axon regeneration.

(2) In ex vivo experiments, NGF was added to the culture medium. Previous studies have shown that adult sensory neurons could initiate fast axon growth in response to NGF within 24 hours. In addition, dissociated sensory neurons could also initiate spontaneous regenerative axon growth without NGF after 48 hours. Some discussion or rationale is needed to explain the di]erence between NGF-induced or spontaneous axon growth of culture adult sensory neurons and the roles of ETBR and SGCs. 

We appreciate the reviewer’s suggestion. In adult DRG explant or dissociated cultures, NGF is not typically required for survival or axon outgrowth. However, in dissociated culture, the addition of NGF to the medium stimulates growth from more neurons compared to controls (Smith and Skene 1997). In the DRG explant, NGF does not promote significant e]ects on axon growth, but stimulates glial cell migration (Klimovich et al 2020). We opted to included NGF in our explant assay to increase the potential of stimulating axon regeneration with pharmacological manipulations of ETBR. We have now clarified these considerations in the Method section.

(3) In cultured dissociated sensory neurons, inhibiting ETBR also enhanced axon growth, which meant the presence of SGCs surrounding the sensory neurons. Some direct evidence is needed to show the cellular relationship between them in culture.  

We thank the reviewer for raising this point and have added new data, now presented in Figure 2B, to show that in mixed DRG cultures, SGCs labeled with Fabp7 are present in the culture in proximity to neurons labeled with TUJ1, but they do not fully wrap the neuronal soma. These results are consistent with prior findings reporting that as time in culture progresses, SGCs lose their adhesive contacts with neuronal soma and adhere to the coverslip (PMID: 22032231, PMID: 27606776).  While in some cases SGCs can maintain their association with neuronal soma in the first day in culture after plating, in our hands, most SGCs have left the soma at the 24h time point we examined. 

(4) In Figure 3, the in vivo regeneration experiments first showed enhanced axon regeneration either 1 day or 3 days after the nerve injury. The study then showed that inhibiting ETBR could enhance sensory axon growth in vitro from uninjured naïve neurons or conditioning lesioned neurons. To my knowledge, in vivo sensory axon regeneration is relatively slow during the first 2 days after the nerve injury and then enters the fast regeneration mode on the 3rd day, representing the conditioning lesion e]ect in vivo. Some discussion is needed to compare the in vitro and the in vivo model of axon regeneration. 

We agree that axon growth is relatively slow the first 2 days and enters a fast growth mode on day 3. This has been elegantly demonstrated in Shin et al Neuron 2012 (PMID: 22726832), where an in vivo conditioning injury 3 days prior increases axon growth one day after injury. In vitro, similar e]ects have been described: a prior in vivo injury accelerates growth capacity within the first day in culture, but a similar growth mode occurs in naive adult neurons after 2-3 days in vitro (Smith and Skene 1996). We also know that the neurite growth in culture is stimulated by higher cell density, likely because non-neuronal cells can secrete trophic factors (Smith and Skene 1996). Our in vitro results thus suggest that blocking ETBR in SGCs in these mixed cultures may alter the media towards a more growth promoting state. In vivo, our data show that Bosentan treatment for 3 days partially mimics the conditioning injury and potentiate the e]ect of the conditioning injury. One possible interpretation is that inhibition of ETBR alters the release of trophic factors from SGCs. Future studies will be required to unravel how ETBR signaling influence the SGCs secretome and its influence on axon growth. We have now included these discussions points in the Results and Discussion Section.

(5) In Figure 5, the study showed that the level of connexin 43 increased after ETBR inhibition in either adult or aged mice, proposing an important role of connexin 43 in mediating the enhancing e]ect of ETBR inhibition on axon regeneration. However, in the study, there was no direct evidence supporting that ETBR directly regulates connexin 43 expression in SGCs. Moreover, there was no functional evidence that connexin 43 acted downstream of ETBR to regulate axon regeneration.  

We thank the reviewer for this point and agree that we do not provide direct evidence that connexin 43 acts downstream of ETBR to regulate axon regeneration. To obtain such functional evidence would require selective KO of ETBR and Cx43 in SGCs, which we believe is beyond the scope of the current study. We have revised the Results and Discussion sections to emphasize that while we observe that ETBR inhibition increases Cx43 levels and Cx43 levels correlates with axon regeneration, whether Cx43 directly mediates the e]ect on axon regeneration remains to be established.  We also discuss potential alternative mechanisms downstream of ETBR in SGCs that could contribute to the observed e]ects on axon regeneration. Specifically, we discuss the possibility that  ETBR signaling may limit axon regeneration via regulating SGCs glutamate reuptake functions, because of the following reasons: 1) Similarly to astrocytes, glutamate uptake by SGCs is important to regulate neuronal function, 2) exposure of cultured cortical astrocytes to endothelin results in a decrease in glutamate uptake that correlates with a major loss of basal glutamate transporter expression (GLT-1 and1), 3) Both glutamate transporters are expressed in SGCs in sensory ganglia 4) GLAST and glutamate reuptake function is important for lesion-induced plasticity in the developing somatosensory cortex. 

Reviewer #2 (Public Review): 

Summary: 

In this interesting and original study, Feng and colleagues set out to address the e]ect of manipulating endothelin signaling on nerve regeneration, focusing on the crosstalk between endothelial cells (ECs) in dorsal root ganglia (DRG), which secrete ET-1 and satellite glial cells (SGCs) expressing ETBR receptor. The main finding is that ETBR signaling is a default brake on axon growth, and inhibiting this pathway promotes axon regeneration after nerve injury and counters the decline in regenerative capacity that occurs during aging. ET-1 and ETBR are mapped in ECs and SGCs, respectively, using scRNA-seq of DRGs from adult or aged mice. Although their expression does not change upon injury, it is modulated during aging, with a reported increase in plasma levels of ET-1 (a potent vasoconstrictive signal). Using in vitro explant assays coupled with pharmacological inhibition in mouse models of nerve injury, the authors demonstrate that ET-1/ETBR curbs axonal growth, and the ETAR/ETBR antagonist Bosentan boosts regrowth during the early phase of repair. In addition, Bosentan restores the ability of aged DRG neurons to regrow after nerve lesions. Despite Bosentan inhibiting both endothelin receptors A and B, comparison with an ETAR-specific antagonist indicates that the e]ects can be attributed to the ET-1/ETBR pathway. In the DRGs, ETBR is mostly expressed by SGCs (and a subset of Schwann cells) a cell type that previous studies, including work from this group, have implicated in nerve regeneration. SGCs ensheath and couple with DRG neurons through gap junctions formed by Cx43. Based on their own findings and evidence from the literature, the pro-regenerative e]ects of ETBR inhibition are in part attributed to an increase in Cx43 levels, which are expected to enhance neuron-SGC coupling. Finally, gene expression analysis in adult vs aged DRGs predicts a decrease in fatty acid and cholesterol metabolism, for which previous work by the authors has shown a requirement in SGCs to promote axon regeneration. 

Strengths: 

The study is well-executed and the main conclusion that "ETBR signaling inhibits axon regeneration after nerve injury and plays a role in age-related decline in regenerative capacity" (line 77) is supported by the data. Given that Bosentan is an FDA-approved drug, the findings may have therapeutic value in clinical settings where peripheral nerve regeneration is suboptimal or largely impaired, as it often happens in aged individuals. In addition, the study highlights the importance of vascular signals in nerve regeneration, a topic that has gained traction in recent years. Importantly, these results further emphasize the contribution of longneglected SGCs to nerve tissue homeostasis and repair. Although the study does not reach a complete mechanistic understanding, the results are robust and are expected to attract the interest of a broader readership. 

We thank the reviewer for the positive comments, especially in regard to the rigor and originality of our study.

Weaknesses: 

Despite these positive comments provided above, the following points should be considered: 

(1) This study examines the contribution of the ET-1 pathway in the ganglia, and in vitro assays are consistent with the idea that important signaling events take place there. Nevertheless, it remains to be determined whether the accelerated axon regrowth observed in vivo depends also on cellular crosstalk mediated by ET-1 at the lesion site. Are ECs along the nerve secreting ET-1? What cells are present in the nerve stroma that could respond and participate in the repair process? Would these interactions be sensitive to Bosentan? It may be di]icult to dissect this contribution, but it should at least be discussed.  

We thank the reviewer for this important point and agree that the in vivo e]ects observed cannot rule out the contribution of ECs or SCs at the lesion site in the nerve. Dissecting the contribution of ETBR expressing cells in the nerve would require cell-specific manipulations that go beyond the scope of this manuscript. We have revised the Discussion section to highlight the potential contribution of ECs, fibroblast and SCs in the nerve.  

(2) It is suggested that the permeability of DRG vessels may facilitate the release of "vascularderived signals" (lines 82-84). Is it possible that the ET-1/ETBR pathway modulates vascular permeability, and that this, in turn, contributes to the observed e]ects on regeneration?  

We thank the reviewer for raising this interesting point. ET-1 can have an impact on vascular permeability. It was indeed shown that in high glucose conditions, increased trans-endothelial permeability is associated with increased Edn1, Ednra and Ednrb expression and augmented ET1 immunoreactivity (PMID: 10950122). It is thus possible that part of the e]ects observed results from altered vascular permeability. We have included this point in the Discussion section. Future experiments will be required to test how injury and age a]ects vascular permeability in the DRG.

(3) Is the a]inity of ET-3 for ETBR similar to that of ET-1? Can it be excluded that ET-3 expressed by fibroblasts is relevant for controlling SGC responses upon injury/aging?  

We thank the reviewer for raising this point. ET-1 binds to ETAR and ETBR with the same a]inity, but ET3 shows a higher a]inity to ETBR than to ETAR (Davenport et al. Pharmacol. Rev 2016 PMID: 26956245). We attempted to examine ET-3 level in adult and aged DRG by western blot, but in our hands the antibody did not work well enough, and we could not obtain clear results. We thus cannot exclude the possibility that ET-3 released by fibroblasts contribute to the e]ects we observe on axon regeneration. Indeed, in cultured cortical astrocytes, application of either ET-1 or ET-3 leads to inhibition of Cx43 expression. We have revised the text in the Discussion section to highlight the possibility that both ET-1 and ET-3 could participate on the ETBRdependent e]ect on axon regeneration.

(4) ETBR inhibition in dissociated (mixed) cultures uncovers the restraining activity of endothelin signaling on axon growth (Figure 2C). Since neurons do not express ET-1 receptors, based on scRNA-seq analysis, these results are interpreted as an indication that basal ETBR signaling in SGC curbs the axon growth potential of sensory neurons. For this to occur in dissociated cultures, however, one should assume that SGC-neuron association is present, similar to in vivo, or to whole DRG cultures (Figure 2C). Has this been tested?

We thank the reviewer for this point. In dissociated DRG culture, neurons, SGCs and other nonneuronal cells are present, but SGCs do not retain the surrounding morphology as they do in vivo. Within 24 hours in culture, SGCs lose their adhesive contacts with neuronal soma and adhere to the coverslip (PMID: 22032231, PMID: 27606776).  We have included new data in Figure 2B to show that in our culture conditions, SGCs are present, but do not wrap neurons soma as they do in vivo. We also know from prior studies that the density of the culture a]ects axon growth, an e]ect that was attributed to trophic factors released from non-neuronal cells (Smith and Skene 1997). Therefore, although SGCs do not surround neurons, the signaling pathway downstream of ETBR may be present in culture and contribute to the release of trophic factors that influence axon growth. We have revised the Results section to better explain our in vitro results and their interpretation.

In both in vitro experimental settings (dissociated and whole DRG cultures) how is ETBR stimulated over up to 7 days of culture? In other words, where does endothelin come from in these cultures (which are unlikely to support EC/blood vessel growth)? Is it possible that the relevant ligand here derives from fibroblasts (see point #6)? Or does it suggest that ETBR can be constitutively active (i.e., endothelin-independent signaling)? Is there any chance that endothelin is present in the culture media or Matrigel? 

We thank the reviewer for raising this point.  Our single-cell data indicate that ET-1 is expressed by endothelial cells and ET-3 by fibroblasts. In dissociated DRG culture at 24h time point, all DRGs cells are present, including endothelial cells and fibroblasts, and could represent the source of ET-1 or ET-3. In the explant setting, it is also possible that both ET-1 and ET-3 are released by endothelial cells and fibroblasts during the 7 days in culture. According to information for the suppliers, endothelin is not present neither in the culture media nor in the Matrigel. While mutations can facilitate the constitutive activity of the ETBR receptor, we are not aware of data showing that endogenous ETBR can be constitutively active.  Because the molecular mechanisms governing ETBR -mediated signaling remain incompletely understood (see for example PMID: 39043181, PMID: 39414992) future studies will be required to elucidate the detailed mechanisms activating ETBR in SGCs and its downstream signaling mechanisms.  We have now expanded the Results and discussion sections to clarify these points. 

(5) The discovery that ET-1/ETBR signaling in SGC curtails the growth capacity of axons at baseline raises questions about the physiological role of this pathway. What happens when ETBR signaling is prevented over a longer period of time? This could be addressed with pharmacological inhibitors, or better, with cell-specific knock-out mice. The experiments would certainly be of general interest, although not within the scope of this story. Nevertheless, it could be worth discussing the possibilities. 

We agree that this is an interesting point. As mentioned above in response to point #1 of reviewer 1, the physiological role of this pathway could be to limit plasticity and prevent maladaptive neural rewiring that can happen after injury (Costigan et al 2009, PMID: 19400724), but can also hinder beneficial recovery after injury. Other mechanisms that limit axon regeneration capacity have been described and involve local mRNA translation and Rho signaling. We have revised the Discussion section to include these points. We agree that understanding the consequence of blocking ETBR over longer time periods is beyond the scope of the current study, but we now discuss the possibility that blocking ETBR with a cell specific KO approach could unravel its physiological function on target innervation and behavior. 

(6) Assessing Cx43 levels by measuring the immunofluorescence signal (Figure 5E-F) is acceptable, particularly when the aim is to restrict the analysis to SGCs. The modulation of Cx43 expression by ET-1/ETBR plays an important part in the proposed model. Therefore, a complementary analysis of Cx43 expression by quantitative RT-PCR on sorted SGCs would be a valuable addition to the immunofluorescence data. Is this attainable? 

We agree and have attempted to perform these types of experiments but encountered technical di]iculties. We attempted to sorting SGCs from transgenic mice in which SGCs are fluorescently labeled. However, the cells did not survive the sorting process and died in culture.  We think that increasing the viability of cells after sorting would require capillary- free fluorescent sorting approaches. However, we do not currently have access to such technology. We attempted this experiment with cultured SGCs, following a previously published protocol (Tonello et al. 2023 PMID: 38156033). In these experiments, SGCs are cultured for 8 days to obtain purity. We did not observe any di]erence in Cx43 protein or mRNA level upon treatment with ET-1 with or without BQ788. However, in these SGCs cultures, Cx43 displayed a di]use localization, rather than puncta as observed in vivo. Therefore, despite our multiple attempts, quantifying Cx43 on sorted or purified SGCs was not attainable.

(7) The conclusions "We thus hypothesize that ETBR inhibition in SGCs contributes to axonal regeneration by increasing Cx43 levels, gap junction coupling or hemichannels and facilitating SGC-neuron communication" (lines 303-305) are consistent with the findings but seem in contrast with the e]ect of aging on gap junction coupling reported by others and cited in line 210: "the number of gap junctions and the dye coupling between these cells increases (Huang et al., 2006)". I am confused by what distinguishes a potential, and supposedly beneficial, increase in coupling after ETBR inhibition, from what is observed in aging. 

We agree that the aging impact of Cx43 level and gap junction number appears contradictory. Procacci et al 2008 reported that Cx43 expression in SGCs decreases in the aged mice. Huang et al 2006 report that both the number of gap junctions and the dye coupling between these cells were found to increase with aging. Procacci et al suggested as a possible explanation for this apparent discrepancy that additional connexin types other than Cx43 may contribute to the gap junctions between SGCs in aged mice. Our snRNAseq data did not allow us to verify this hypothesis, because there were less SGCs in aged mice compared to adult, and connexin genes were detected in only 20% or less of SGCs.  Furthermore, our quantification did not look specifically at gap junctions, but just at Cx43 puncta. Cx43 can also form hemichannels in addition to gap junctions, and can also perform non-channel functions, such as protein interaction, cell adhesion, and intracellular signaling. Thus, more research examining the role of Cx43 in SGCs is necessary to address this discrepancy in the literature. We have expanded the Discussion section to include these points. 

(8) I find it di]icult to reconcile the results in Figure 5F with the proposed model since (1) injury increases Cx43 levels in both adult and aged mice, (2) the injured aged/vehicle group has a similar level to the uninjured adult group, (3) upon injury, aged+Bosentan is much lower than adult+Bosentan (significance not tested). It seems hard to explain the e]ect of Bosentan only through the modulation of Cx43 levels. Whether the increase in Cx43 levels following ETBR inhibition actually results in higher SGC-neuron coupling has not been assessed experimentally. 

We thank the reviewer for this point and agree that the e]ect of Bosentan is likely not exclusively through the modulation of Cx43 levels in SGCs, and that Cx43 levels may simply correlate with axon regenerative capacity. We have revised the manuscript to clarify this point.  We have also added the missing significance test in Figure 5F.

Cell specific KO of Cx43 and ETBR would allow to test this hypothesis directly but is beyond the scope of the current study. We have not tested SGCs-neuron coupling, as these experiments are currently beyond our area of expertise. Cx43 has also other functions beyond gap junction coupling, such as protein interaction, cell adhesion, and intracellular signaling. Investigating the precise function of Cx43 would require in depth biochemical and cell specific experiments that are beyond the scope of this study. Furthermore, as we now mentioned in response to reviewer #2 point 5, ETBR signaling may also have other downstream e]ects in SGCs, such as glutamate transporters expression, or a]ect other cells in the nerve during the regeneration process. We have revised the Discussion section to include these alternative mechanisms.

Reviewer #3(Public Review): 

Summary: 

This manuscript suggests that inhibiting ETBR via the FDA-approved compound Bosentan can disrupt ET-1-ETBR signalling that they found detrimental to nerve regeneration, thus promoting repair after nerve injury in adult and aged mice. 

Strengths: 

(1) The clinical need to identify molecular and cellular mechanisms that can be targeted to improve repair after nerve injury. 

(2) The proposed mechanism is interesting. 

(3) The methodology is sound. 

We thank the reviewer for highlighting the strengths of our study

Weaknesses: 

(1) The data appear preliminary and the story appears incomplete. 

We appreciate the reviewer’s point. We would like to emphasize that our results provide compelling evidence that ETBR signaling is a default brake on axon growth, and inhibiting this pathway promotes axon regeneration after nerve injury and counters the decline in regenerative capacity that occurs during aging. We also provide evidence that ETBR signaling regulates the levels of Cx43 in SGCs. Furthermore, our results document the use of an FDA approved compound to increase axon regeneration may be of interest to the broader readership, as there is currently no therapies to improve or accelerate nerve repair after injury. We agree that the detailed mechanisms operating downstream of ETBR will need to be elucidated. Answering these questions would first require cell specific KO of ETBR and Cx43 to confirm that this pathway is operating in SGCs to control axon regeneration. We would also need to identify how SGCs communicate with neurons to regulate axon regeneration, which is a large area of ongoing research that remains poorly understood. This extensive and highly complex set of experiments is beyond the scope of the current study. As we discussed in our response to reviewer #1 and #2 we attempted to perform numerous additional experiments to better define the role of ETBR signaling in SGCs in aging and have included additional results in Fig. 2B, Fig 3G-H,  Fig 5A-E, and Figure 4- Figure Supplement 1and Figure 5- Figure Supplement 1. We have expanded the

Discussion to acknowledge the limitation of our study and to discuss possible mechanisms.  

(2) Lack of causality and clear cellular and molecular mechanism. There are also some loose ends such as the role of connexin 43 in SGCs: how is it related to ET-1- ETBR signalling?  

We thank the reviewer for this point and agree that the molecular mechanisms downstream of ETBR remain to be elucidated. However, we believe that our manuscript reports an interesting potential of an FDA-approved compound in promoting nerve repair. We focused on Cx43 downstream of ETBR signaling because decreased Cx43 expression in SGCs in ageing was previously established, but the mechanisms were not elucidated. Furthermore, it was reported that ET1 signaling in cultured astrocytes, which share functional similarities with SGCs, leads to the closure of gap junctions and reduction in Cx43 expression. Our study thus provides a mechanism by which ETBR signaling in SGCs regulates Cx43 expression. Whether Cx43 directly impact axon regeneration remains to be tested. Cell specific KO of Cx43 and ETBR would be required to answer this question. We have revised the Introduction and Discussion section extensively to provide a link between ETBR and Cx43 and to acknowledge the lack of causality in Cx43 in SGCs, as well as to provide additional potential mechanisms by which ETBR inhibition may promote nerve repair.

Reviewer #2 (Recommendations For The Authors): 

In addition to the points listed in the Public Review section, please consider the following comments: 

(1) ETAR, which is high in mural cells, does not seem to be implicated in the reported proregenerative e]ects. Even so, can vasoconstriction be ruled out as an underlying cause of the age-dependent decline in axon regrowth potential and, more generally, in the e]ects of ET-1 inhibition on regeneration? This could be discussed. 

We agree that we can’t exclude a role in vasoconstriction or e]ect on vascular permeability in the age-dependent decline in axon regrowth potential. However, our in vitro and ex vivo experiments, in which vascular related mechanisms are unlikely, suggest that vasoconstriction may not be a major contributor to the e]ects we observed.

(2) The manuscript (e.g. line 287-288) would benefit from a discussion of the role that blood vessels play in the peripheral nervous system, and possibly CNS, repair. Vessels were shown to accompany regenerating fibers and instruct the reorganization of the nerve tissue to favor repair potentially through the release of pro-regenerative signals acting on stromal cells, glia, and other cellular components. Highlighting these processes will help put the current findings into perspective. 

We agree and have revised the Discussion section to better explain the role of blood vessels in orientating Schwann cells migration and guiding axon regeneration.

(3) The vast majority of the cells that are sequenced and shown in the UMAP in Figure 1C are from adult (3-month-old) mice [16,923 out of 18,098]. It would be useful to include the UMAP split (or color-coded) by timepoint to appreciate changes in cell clustering that may occur with aging.  

We apologize for this misunderstanding, Figure 1C had all cells from all ages. However, the number of cells we obtained from the age group was insu]icient to perform in depth analysis of each cell type. We have thus revised this section and Figure 1, now only presenting the data from adult mice.  

It is not discussed why fewer cells were sequenced at later stages. Additionally, I do not know how to interpret the double asterisks next to the labeling "18,098 samples" in Figure 1C. 

Since our original sequencing of adult and aged mice using 10x yielded so few cells from the aged DRG, we tested and optimized a new technology for single cell preparation of DRG using Illumina Single Cell 3’ RNA Prep. This preparation creates templated emulsions using a vortex mixer to capture and barcode single-cell mRNA instead of a microfluidics system. This method yielded much better results for nuclei recovery from aged DRG, with more nuclei and better quality of nuclei. Thus, we now present in Figure 5 and Figure 5- Figure Supplement 1 the results from snRNA-sequencing of aged and adult DRG using the Illumina single cell kit. The results of the snRNA-sequencing show a decreased abundance of SGCs in aged mice, consistent with the results from our morphology analysis with EM. We were also able to perform SGCs-specific pathway analysis because of the increased number of nuclei captured in the aged SGCs, which we included in the manuscript.

(4) The in vivo studies are designed to examine the e]ects of ETBR inhibition during the first phase of axon regrowth after nerve injury (1-3 days post-injury, dpi). Is there a reason why later stages have not been studied? It would be interesting to understand whether ETBR inhibition improves long-term recovery or is only e]ective at boosting the initial growth of axons through the lesion. It is possible that early inhibition will be enough for long-term recovery. If so, these experiments would define a sensitivity window with therapeutic value. 

We agree that assessing functional recovery requires proper behavioral tests or morphological evaluations of reinnervation. To determine if Bosentan treatment has long-term e]ects on recovery, we administered Bosentan or vehicle for 3 weeks (daily for 1 week, and then once a week for the subsequent 2 weeks) after sciatic nerve crush. At 24 days after SNC, we assessed intraepidermal nerve fiber density (IENFD) in the injured paw and saw a trend towards increased fibers/mm in the treated animals (new Figure 3G,H). Future studies will examine how long-term Bosentan treatment a]ects functional recovery and innervation at later time points. Additionally, behavior assays will be needed to determine if these morphological changes relate to behavioral improvements using IENFD and behavior assays.

(5) I am unsure if the gene expression analysis shown in Figure 6 fits well into this story. It is interesting per se and in line with previous work from this group showing the relevance of fatty acid metabolism in SGCs for axon regeneration. Nevertheless, without a mechanistic link to endothelin signaling and Cx43/gap junction modulation, the observations derived from DEG analysis are not well integrated with the rest and may be more distracting than helpful. One limitation is that there is no cell-type information for the DEGs due to the small number of cells recovered from aged mice. For instance, if ETBR inhibition rescued gene downregulation associated with fatty acid/cholesterol metabolism, then the DGE results would become more relevant for understanding the cellular basis of the pro-regenerative e]ect, which at this point remains quite speculative (lines 264-265; lines 318-319).  

We agree and have added new snRNA sequencing data to replace these findings (see above response to point #4, new Figure 5 and Figure 5- Figure Supplement 1. The new data shows a decreased abundance of SGCs in aged mice, consistent with our TEM results. Pathway analysis revealed that aging triggers extensive transcriptional reprogramming in SGCs, reflecting heightened demands for structural integrity, cell junction remodeling, and glia–neuron interactions within the aged DRG microenvironment.  

(6) It would be interesting to determine whether Bosentan increases SGC coverage of neuronal cell bodies in aged mice (Figures 6A-C). 

We agree that this would be very interesting, but will require extensive EM analysis at di]erent time points and is beyond the scope of the current manuscript.

(7) Finally, adding a summary model would help the readers. 

We agree and have made a summary model, now presented in Figure 6F.

Reviewer #3 (Recommendations For The Authors): 

Longer time points post-injury and assessment of functional recovery after Bosentan would be of great value here. 

We agree that assessing functional recovery requires proper behavioral tests or morphological evaluations of reinnervation. To determine if Bosentan treatment has long-term e]ects on recovery, we administered Bosentan or vehicle for 3 weeks (daily for 1 week, and then once a week for the subsequent 2 weeks) after sciatic nerve crush. At 24 days after SNC, we assessed intraepidermal nerve fiber density in the injured paw and saw a trend towards increased fibers/mm in the treated animals (Fig 3). While the results do not reach significance, we decided to include this new data as it provides evidence that Bosentan treatment may also improves long term recovery. Future studies will be required examine how long-term Bosentan treatment a]ects functional recovery and innervation at later time points. Additionally, behavior assays will be needed to determine if these morphological changes relate to behavioral improvements.

It would be important to know how ET-1- ETBR signalling axis promotes the regeneration of axons:this remains unaddressed. What are the cells that are specifically involved? Endothelial cellsSGC- neurons- SC? There are no experiments addressing the role of any of these? 

We agree that the molecular and cellular mechanisms by which ETBR signaling in SGCs promote axon regeneration remains to be elucidated.  Answering these questions would first require cell specific KO of ETBR and Cx43 to confirm that this pathway is operating in SGCs to control axon regeneration. We would also need to identify how SGCs communicate with neurons to regulate axon regeneration, which is a large area of ongoing research that remains poorly understood. While these are important experiments, because of numerous technical and temporal constrains, we believe they are beyond the scope of the current manuscript. 

How does connexin 43 in SGCs related to ET-1- ETBR signalling? 

The relation between connexin 43 and ETBR signaling stems from observations made in astrocytes. ET1 signaling in cultured astrocytes, which share functional similarities with SGCs, was shown to lead to the closure of gap junctions and the reduction in Cx43 expression. Because Cx43 expression, a major connexin expressed in SGCs as in astrocytes, was previously shown to be reduced at the protein level in SGCs from aged mice, we decided to explore it this ETBR-Cx43 mechanism also operates in SGCs. We have revised the Introduction and Discussion section extensively to acknowledge the lack of causality in Cx43 expression SGCs and to provide additional potential mechanisms by which ETBR inhibition may promote nerve repair.

Author response:

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

Reviewer #1 (Public review):

Summary:

The manuscript proposes that 5mC modifications to DNA, despite being ancient and widespread throughout life, represent a vulnerability, making cells more susceptible to both chemical alkylation and, of more general importance, reactive oxygen species. Sarkies et al take the innovative approach of introducing enzymatic genome-wide cytosine methylation system (DNA methyltransferases, DNMTs) into E. coli, which normally lacks such a system. They provide compelling evidence that the introduction of DNMTs increases the sensitivity of E. coli to chemical alkylation damage. Surprisingly they also show DNMTs increase the sensitivity to reactive oxygen species and propose that the DNMT generated 5mC presents a target for the reactive oxygen species that is especially damaging to cells. Evidence is presented that DNMT activity directly or indirectly produces reactive oxygen species in vivo, which is an important discovery if correct, though the mechanism for this remains obscure.

Strengths:

This work is based on an interesting initial premise, it is well-motivated in the introduction and the manuscript is clearly written. The results themselves are compelling.

We thank the reviewer for their positive response to our study.  We also really appreciate the thoughtful comments raised.  We have addressed the comments raised as detailed below. 

Weaknesses:

I am not currently convinced by the principal interpretations and think that other explanations based on known phenomena could account for key results. Specific points below.

(1) As noted in the manuscript, AlkB repairs alkylation damage by direct reversal (DNA strands are not cut). In the absence of AlkB, repair of alklylation damage/modification is likely through BER or other processes involving strand excision and resulting in single stranded DNA. It has previously been shown that 3mC modification from MMS exposure is highly specific to single stranded DNA (PMID:20663718) occurring at ~20,000 times the rate as double stranded DNA. Consequently, the introduction of DNMTs is expected to introduce many methylation adducts genome-wide that will generate single stranded DNA tracts when repaired in an AlkB deficient background (but not in an AlkB WT background), which are then hyper-susceptible to attack by MMS. Such ssDNA tracts are also vulnerable to generating double strand breaks, especially when they contain DNA polymerase stalling adducts such as 3mC. The generation of ssDNA during repair is similarly expected follow the H2O2 or TET based conversion of 5mC to 5hmC or 5fC neither of which can be directly repaired and depend on single strand excision for their removal. The potential importance of ssDNA generation in the experiments has not been considered.

We thank the reviewer for this interesting and insightful suggestion.  Our interpretation of our findings is that a subset of MMS-induced DNA damage, specifically 3mC, overlaps with the damage introduced by DNMTs and this accounts for increased sensitivity to MMS when DNMTs are expressed.  However, the idea that the introduction of 3mC by DNMT actually makes the DNA more liable to damage by MMS, potentially through increasing the level of ssDNA, is also a potential explanation, which could operate in addition to the mechanism that we propose.

(2) The authors emphasise the non-additivity of the MMS + DNMT + alkB experiment but the interpretation of the result is essentially an additive one: that both MMS and DNMT are introducing similar/same damage and AlkB acts to remove it. The non-additivity noted would seem to be more consistent with the ssDNA model proposed in #1. More generally non-additivity would also be seen if the survival to DNA methylation rate is non-linear over the range of the experiment, for example if there is a threshold effect where some repair process is overwhelmed. The linearity of MMS (and H2O2) exposure to survival could be directly tested with a dilution series of MMS (H2O2).

We thank the reviewer for this point.  As in the response to point #1, the reviewer’s hypothesis of increased potency of MMS, potentially through increased ssDNA, downstream of 3mC induction by DNMT, is a good one.  We have added a dose-response curve for DNMT-expressing cells to MMS to the revised version of the manuscript.  This shows that there is a non-linear response to MMS in the WT background.  Sensitivity is exacerbated by expression of DNMT and alkB mutation individually but there is also a strong non-additive effect that is particularly marked at low MMS concentrations where sensitivity is much higher in the double mutant than predicted from the two single mutants.  This is consistent with induction of DNA damage by DNMT that is repaired by alkB because alkB can be ‘overwhelmed’ even in WT backgrounds as the reviewer suggests.  However, it is also perfectly possible that the effect is due to increased levels of DNA damage induction in DNMT-expressing cells.  Both these results are compatible with our central hypothesis, namely that DNMT expression induces 3mC.  We have included these results along with discussion of them in the revised text in the results section:

In order to investigate the non-additivity between DNMT expression and alkB mutation further, we investigated the effect of MMS over a range of concentrations for the different strains (Supplemental Figure 1A).  We quantified the non-additivity by comparing between the survival of alkB expressing DNMT to the predicted combined effect of either alkB mutation alone or DNMT expression alone(Supplemental Figure 1B).  Significantly reduced survival than expected was observed, most notably at low concentrations of MMS, which could be due to the saturation of the effect at high concentrations of MMS for alkB mutants expressing DNMT, where extremely high levels of sensitivity were observed.  The non-linear shape of the graph observed for WT cells expressing DNMTs further suggests that the ability of AlkB to repair the DNA is overwhelmed at high MMS concentrations even in the WT background.  These results are consistent with the idea that AlkB repairs a form of DNA damage from MMS that is more prevalent when DNMT is expressed.  This could be because DNMT induces 3mC, repaired by AlkB, and further 3mC is induced by MMS leading to much higher 3mC levels in the absence of AlkB activity.  Alternatively, 3mC induction by DNMT may lead to increased levels of ssDNA, particularly in alkB mutants, which could increase the risk of further DNA damage by MMS exposure and heighten sensitivity.  Either of these mechanisms are consistent with induction of 3mC by DNMT, and  indicate that the induction of DNA damage by DNMT expression has a fitness cost for cells when exposed to genotoxic stress in their environment. 

(3) The substantial transcriptional changes induced by DNMT expression (Supplemental Figure 4) are a cause for concern and highlight that the ectopic introduction of methylation into a complex system is potentially more confounded than it may at first seem. Though the expression analysis shows bulk transcription properties, my concern is that the disruptive influence of methylation in a system not evolved with it adds not just consistent transcriptional changes but transcriptional heterogeneity between cells which could influence net survival in a stressed environment. In practice I don't think this can be controlled for, possibly quantified by single-cell RNA-seq but that is beyond the reasonable scope of this paper.

We fully agree with the reviewer and, indeed, we are very interested in what is driving the transcriptional changes that we observed.  Work is currently underway in the lab to investigate this further but, as the reviewer suggests, is beyond the scope of this paper.  Importantly, we have used the transcriptional data to determine that the effect of DNMTs on ROS is unlikely to be due to failure of ROS-induced detoxification mechanisms by investigating the expression of oxyR regulated genes.  Nevertheless we have explicitly mentioned the concern raised by the reviewer in the revised manuscript as follows:

“The substantial transcriptional responses could potentially affect how individual cells respond to genotoxic stress and thus could be contributing to some of the excess sensitivity to MMS and H2O2 in cells expressing DNMTs. However, the induction of oxyR regulated genes such as catalase was unaffected by 5mC (Supplementary Figure 4B).  Thus, the increased sensitivity to H2O2 is unlikely to be caused by failure of detoxification gene induction by DNMT expression.”

(4) Figure 4 represents a striking result. From its current presentation it could be inferred that DNMTs are actively promoting ROS generation from H2O2 and also to a lesser extent in the absence of exogenous H2O2. That would be very surprising and a major finding with far-reaching implications. It would need to be further validated, for example by in vitro reconstitution of the reaction and monitoring ROS production. Rather, I think the authors are proposing that some currently undefined, indirect consequence of DNMT activity promotes ROS generation, especially when exogenous H2O2 is available. It would help if this were clarified.

We thank the reviewer for picking this up.  In the discussion, we raise two possible explanations for why DNMT (even without H2O2) increases the ROS levels.  One idea is direct activity of DNMT, and one is through the product of DNMT activity (5mC) acting as a platform to generate more ROS from endogenous or exogenous sources.  Whilst we attempted to measure ROS from mSSSI activity in vitro, this experiment gave inconsistent results and therefore we cannot distinguish between these two possibilities.  However, we argued that direct activity is less likely, exactly as the reviewer points out.  We have clarified our discussion in the revised version, rewriting the entire section titled

Oxidative stress as a new source of DNA damage induction by DNMT expression to more clearly set out these possibilities. 

Reviewer #2 (Public review):

5-methylcytosine (5mC) is a key epigenetic mark in DNA and plays a crucial role in regulating gene expression in many eukaryotes including humans. The DNA methyltransferases (DNMTs) that establish and maintain 5mC, are conserved in many species across eukaryotes, including animals, plants, and fungi, mainly in a CpG context. Interestingly, 5mC levels and distributions are quite variable across phylogenies with some species even appearing to have no such DNA methylation.

This interesting and well-written paper discusses the continuation of some of the authors' work published several years ago. In that previous paper, the laboratory demonstrated that DNA methylation pathways coevolved with DNA repair mechanisms, specifically with the alkylation repair system. Specifically, they discovered that DNMTs can introduce alkylation damage into DNA, specifically in the form of 3-methylcytosine (3mC). (This appears to be an error in the DNMT enzymatic mechanism where the generation 3mC as opposed to its preferred product 5-methylcytosine (5mC), is caused by the flipped target cytosine binding to the active site pocket of the DNMT in an inverted orientation.) The presence of 3mC is potentially toxic and can cause replication stress, which this paper suggests may explain the loss of DNA methylation in different species. They further showed that the ALKB2 enzyme plays a crucial role in repairing this alkylation damage, further emphasizing the link between DNA methylation and DNA repair.

The co-evolution of DNMTs with DNA repair mechanisms suggests there can be distinct advantages and disadvantages of DNA methylation to different species which might depend on their environmental niche. In environments that expose species to high levels of DNA damage, high levels of 5mC in their genome may be disadvantageous. This present paper sets out to examine the sensitivity of an organism to genotoxic stresses such as alkylation and oxidation agents as the consequence of DNMT activity. Since such a study in eukaryotes would be complicated by DNA methylation controlling gene regulation, these authors cleverly utilize Escherichia coli (E.coli) and incorporate into it the DNMTs from other bacteria that methylate the cytosines of DNA in a CpG context like that observed in eukaryotes; the active sites of these enzymes are very similar to eukaryotic DNMTs and basically utilize the same catalytic mechanism (also this strain of E.coli does not specifically degrade this methylated DNA) .

The experiments in this paper more than adequately show that E. coli expression of these DNMTs (comparing to the same strain without the DNMTS) do indeed show increased sensitivity to alkylating agents and this sensitivity was even greater than expected when a DNA repair mechanism was inactivated. Moreover, they show that this E. coli expressing this DNMT is more sensitive to oxidizing agents such as H2O2 and has exacerbated sensitivity when a DNA repair glycosylase is inactivated. Both propensities suggest that DNMT activity itself may generate additional genotoxic stress. Intrigued that DNMT expression itself might induce sensitivity to oxidative stress, the experimenters used a fluorescent sensor to show that H2O2 induced reactive oxygen species (ROS) are markedly enhanced with DNMT expression. Importantly, they show that DNMT expression alone gave rise to increased ROS amounts and both H2O2 addition and DNMT expression has greater effect that the linear combination of the two separately. They also carefully checked that the increased sensitivity to H2O2 was not potentially caused by some effect on gene expression of detoxification genes by DNMT expression and activity. Finally, by using mass spectroscopy, they show that DNMT expression led to production of the 5mC oxidation derivatives 5-hydroxymethylcytosine (5hmC) and 5-formylcytosine (5fC) in DNA. 5fC is a substrate for base excision repair while 5hmC is not; more 5fC was observed. Introduction of non-bacterial enzymes that produce 5hmC and 5fC into the DNMT expressing bacteria again showed a greater sensitivity than expected. Remarkedly, in their assay with addition of H2O2, bacteria showed no growth with this dual expression of DNMT and these enzymes.

Overall, the authors conduct well thought-out and simple experiments to show that a disadvantageous consequence of DNMT expression leading to 5mC in DNA is increased sensitivity to oxidative stress as well as alkylating agents.

Again, the paper is well-written and organized. The hypotheses are well-examined by simple experiments. The results are interesting and can impact many scientific areas such as our understanding of evolutionary pressures on an organism by environment to impacting our understanding about how environment of a malignant cell in the human body may lead to cancer.

We thank the reviewer for their response to our study, and value the time taken to produce a public review that will aid readers in understanding the key results of our study. 

Reviewer #3 (Public review):

Summary:

Krwawicz et al., present evidence that expression of DNMTs in E. coli results in (1) introduction of alkylation damage that is repaired by AlkB; (2) confers hypersensitivity to alkylating agents such as MMS (and exacerbated by loss of AlkB); (3) confers hypersensitivity to oxidative stress (H2O2 exposure); (4) results in a modest increase in ROS in the absence of exogenous H2O2 exposure; and (5) results in the production of oxidation products of 5mC, namely 5hmC and 5fC, leading to cellular toxicity. The findings reported here have interesting implications for the concept that such genotoxic and potentially mutagenic consequences of DNMT expression (resulting in 5mC) could be selectively disadvantageous for certain organisms. The other aspect of this work which is important for understanding the biological endpoints of genotoxic stress is the notion that DNA damage per se somehow induces elevated levels of ROS.

Strengths:

The manuscript is well-written, and the experiments have been carefully executed providing data that support the authors' proposed model presented in Fig. 7 (Discussion, sources of DNA damage due to DNMT expression).

Weaknesses:

(1) The authors have established an informative system relying on expression of DNMTs to gauge the effects of such expression and subsequent induction of 3mC and 5mC on cell survival and sensitivity to an alkylating agent (MMS) and exogenous oxidative stress (H2O2 exposure). The authors state (p4) that Fig. 2 shows that "Cells expressing either M.SssI or M.MpeI showed increased sensitivity to MMS treatment compared to WT C2523, supporting the conclusion that the expression of DNMTs increased the levels of alkylation damage." This is a confusing statement and requires revision as Fig. 2 does ALL cells shown in Fig. 2 are expressing DNMTs and have been treated with MMS. It is the absence of AlkB and the expression of DNMTs that that causes the MMS sensitivity.

We thank the reviewer for this and agree that this needs to be clarified with regards to the figure presented and will do so in the revised manuscript. The key comparison is between the active and inactive mSSSI which shows increased sensitivity when active methyltransferases are expressed.  We have clarified this in the revised version of the manuscript as follows:

“Cells expressing either M.SssI or M.MpeI showed increased sensitivity to MMS treatment compared to cells expressing inactive M.SssI”

(2) It would be important to know whether the increased sensitivity (toxicity) to DNMT expression and MMS is also accompanied by substantial increases in mutagenicity. The authors should explain in the text why mutation frequencies were not also measured in these experiments.

This is an important point because it is not immediately obvious that increased sensitivity would be associated with increased mutagenicity (if, for example, 3mC was never a cause of innacurate DNA repair even in the absence of AlkB).  We have now added a Rif resistance assay which demonstrates increased mutagenesis in the presence of DNMT, and that this is exacerbated by loss of AlkB. This is now added as supplemental figure 2 and described in the manuscript as follows:

“One potential consequence of DNMT activity in inducing DNA damage might be increased mutagenesis.  To test this we performed a rifampicin resistance mutagenesis assay, in the absence of MMS, to test whether DNMT induced damage was sufficient to lead to mutation rate increase.  Mutation rate was increased by DNMT expression (p=1.6e-12; two way anova; Supplemental Figure 2) and alkB mutation (two way anova) separately (p<1e-16).  Moreover, there was a significant interaction such that combined alkB mutation and DNMT expression led to a further increased mutation rate compared to the expectation from alkB mutation and DNMT expression separately (p = 7.9e-10; Supplemental Figure 2).  Importantly, DNMT induction alone would be expected to lead to increased mutations due to cytosine deamination(Sarkies, 2022a); however, there is a synergistic effect on mutations when this is combined with loss of AlkB function in alkB mutants. This is consistent with 3mC induction by DNMTs which is repaired by AlkB in WT cells but leads to mutations in alkB mutant cells.

(3) Materials and Methods. ROS production monitoring. The "Total Reactive Oxygen Species (ROS) Assay Kit" has not been adequately described. Who is the Vendor? What is the nature of the ROS probes employed in this assay? Which specific ROS correspond to "total ROS"?

The ROS measurement was with a kit from ThermoFisher: https://www.thermofisher.com/order/catalog/product/88-5930-74.  The probe is DCFH-DA.  This is a general ROS sensor that is oxidised by a large number of cellular reactive oxygen species hence we cannot attribute the signal to a single species.  Use of a technique with the potential to more precisely identify the species involved is something we plan to do in future, but is beyond what we can do as part of this study.  We have added a comment as to the specificity of the ROS sensor in the revised version as follows:

“The ROS detection reagent in this system is DCFH-DA, a generalised ROS sensor that is not specific to any particular ROS molecule.”     

(4) The demonstration (Fig. 4) that DNMT expression results in elevated ROS and its further synergistic increase when cells are also exposed to H2O2 is the basis for the authors' discussion of DNA damage-induced increases in cellular ROS. S. cerevisiae does not possess DNMTs/5mC, yet exposure to MMS also results in substantial increases in intracellular ROS (Rowe et al, (2008) Free Rad. Biol. Med. 45:1167-1177. PMC2643028). The authors should be aware of previous studies that have linked DNA damage to intracellular increases in ROS in other organisms and should comment on this in the text.

We thank the reviewer for this point.  We note that the increased ROS that we observed occur in the presence of DNMTs alone and in the presence of H2O2, not in the presence of MMS; however, the point that DNA damage in general can promote increased ROS in some circumstances is well taken.  We have included a comment on this in the revised version as follows:

“We believe this is a plausible mechanism to explain both increased ROS and increased sensitivity to oxidative stress when DNMT is expressed.  However, other explanations are possible, and it is notable that DNA damaging agents such as MMS can lead to ROS generation(Rowe et al., 2008).  A more detailed chemical and kinetic study of the ROS formation in DNMT-expressing cells would be needed to resolve these questions.”

This op-ed addresses the issue with the exponential increase in publications and how this is leading to a lower quality of peer review which, in turn, is resulting in more bad science being published. It is a well-written article that tackles a seemingly eternal topic. This piece focussed more on the positives and potential actions which is nice to see as this is a topic that can become stuck in the problems. There are places throughout that would benefit from more clarity and at times there appears to be a bias towards publishers, almost placing blame on researchers. Very simple word changes or headings could immediately resolve any doubt here as I don't believe this is the intention of the article at all.

Additionally, this article is very focussed on peer review (a positive) but I think that it would benefit from small additions throughout that zoom out from this and place the discussion in the context of the wider issues - for example you cannot change peer review incentives without changing the entire incentives around "service" activities including teaching, admin etc. This occurs to a degree with the discussion on other outputs, including preprints and data. Moreover, when discussing service type activities, there is data that reveals certain demographics deliberately avoid this work. Adding this element into the article would provide a much stronger argument for change (and do some good in the new current political climate).

Overall, I thought this was a great piece when it was first posted online and does exactly what a good op-ed should - provoke thought and discussion. Below are some specific comments, in reading order. I do not believe that there are any substantial or essential changes required, particularly given that this is an op-ed article.

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Quote: "Academia is undergoing a rapid transformation characterized by exponential growth of scholarly outputs."

Comment: There's an excellent paper providing evidence to this: https://direct.mit.edu/qss/article/5/4/823/124269/The-strain-on-scientific-publishing which would be a very positive addition

Quote: "it’s challenging to keep up with the volume at which research publications are produced"

Comment: Might be nice to add that this was a complaint dating back since almost the beginning of sharing research via print media, just to reinforce that this is a very old point.

Quote: "submissions of poor-quality manuscripts"

Comment: The use of "poor quality" here is unnecessary. Just because a submission is not accepted, it has no reflection on "quality". As such this does seem to needlessly diminish work rejected by one journal

Quote: "Maybe there are too many poor quality journals too - responding to an underlying demand to publish low quality papers."

Comment: This misses the flip side - poor quality journals encourage and actively drive low quality & outright fraudulent submissions due to the publisher dominance in the assessment of research and academics.

Quote: "even after accounting for quality,"

Comment: Quality is mentioned here but has yet to be clearly defined. What is "quality"? - how many articles a journal publishes? The "prestige" of a journal? How many people are citing the articles?

Quote: "Researchers can – and do – respond to the availability by slicing up their work (and their data) into minimally publishable units"

Comment: I fully agree that some researchers do exactly this. However, again, this seems to be blaming researchers for creating this firehose problem. I think this point could be reworded to not place so much blame or be substantiated with evidence that this is a widespread practice - my experience has been very mixed in that I've worked for people who do this almost to the extreme (and have very high self-citations) and also worked for people who focus on the science and making it as high quality and robust as possible. I agree many respond to the explosion of journals and varied quality in a negative manner but the journals, not researchers are the drivers here.

Quote: "least important aspect of the expected contributions of scholars."

Comment: I think it may be worth highlighting here that sometimes specific demographics (white males) actively avoid these kinds of service activities - there's a good study on this providing data in support of this. It adds an extra dimension into the argument for appropriate incentives and the importance & challenges of addressing this.

Quote: "high quality peer review"

Comment: Just another comment on the use of "quality'. This is not defined and I think when discussing these topics it is vital to be clear what one means by "high quality". For example, a high quality peer review that is designed as quality control would be detecting gross defects and fraud, preventing such work from being published (peer review does not reliably achieve this). In contrast, a high quality peer review designed to help authors improve their work and avoid hyperbole would be very detailed and collegial, not requesting large numbers of additional experiments.

Quote: "conferring public trust in the oversight of science"

Comment: I'm not convinced of this. Conveying peer review as a stamp of approval or QC leads to reduced trust when regular examples emerge with peer review failures - just look at Hydroxychloroquine and how peer review was used to justify that during COVID or the MMR/autism issues that are still on-going even after the work was retracted. I think this should be much more carefully worded, removed or expanded on to provide this perspective - this occurs slightly in the following sentence but it is very important to be clear on this point.

Quote: "Researchers hold an incredible amount of market power in scholarly publishing"

Comment: I like the next few paragraphs but, again, this seems to be blaming researchers when they in fact hold no/little power. I agree that researchers *could* use market pressure but this is entirely unrealistic when their careers depend on publishing X papers in X journal. An argument as to why science feels increasingly non-collaborative perhaps. Funders can have immediate and significant changes. Institutions adopting reward structures, such as teaching for example, would have significant impacts on researcher behaviour. Researchers are adapting to the demands the publication system creates - more journals, greater quantity and reduced quality whilst maintaining control over the assessment - eLife being removed from Wos/Scopus is a prime example of publishers (via their parent companies) preventing innovation or even rather basic improvements.

Quote: "With preprint review, authors participate in a system that views peer review not as a gatekeeping hurdle to overcome to reach publication but as a participatory exercise to improve scholarship."

Comment: This is framing that I really like; improving scholarship, not quality control.

Quote: "buy"

Comment: typo

Quote: "adoption of preprint review can shift the inaccurate belief that all preprints lack review"

Comment: Is this the right direction for preprints though? If we force all preprints to be reviewed and only value reviewed-preprints, then we effectively dismantle the benefits of preprints and their potential that we've been working so hard to build. A recent op-ed by Alice Fleerackers et al provided an excellent argument to this effect. More a question than a suggestion for anything to change.

Quote: "between all of those stakeholders to work together without polarization"

Comment: I disagree here - publishers have repeatedly shown that their only real interest is money. Working with them risks undermining all of the effort (financial, careers, reputation, time) that advocates for change put in. The OA movement should also highlight perfectly why this is such a bad route to go down (again). Publishers grip on preprint servers is a great example - those servers are hard to use as a reader, lack APIs and access to data, are not innovative or interacting with independent services. The community should make the rules and then publishers abide by and within them. Currently the publishers make all of the rules and dominate. Indeed, this is possibly the biggest ommision from this article - the total dominance of publishers across the entire ecosystem. You can't talk about change without highlighting that the publishers don't just own journals but the reference managers, the assessment systems, the databases etc. I may be an outlier on this point but for all of the people I interact with (often those at the bottom of the ladder) this is a strong feeling. Again, not a suggestion for anything to change and indeed the point of an op-ed is to stimulate thought and discussion so dissent is positive.

Note that these annotations were made in hypothes.is and are available here, linked in-text for ease - comments are duplicated in this review.

Summary of the essay

In this essay, the author seeks to explain the ‘firehose’ problem in academic research, namely the rapid growth in the number of articles but also the seemingly concurrent decline in quality. The explanation, he concludes, lies in the ‘superstructure’ of misaligned incentives and feedback loops that primarily drive publisher and researcher behaviour, with the current publish or perish evaluation system at the core. On the publisher side, these include commercial incentives driving both higher acceptance rates in existing journals and the launch of new journals with higher acceptance rates. At the same time, publishers seek to retain reputational currency by maintaining consistency and therefore brand power of scarcer, legacy-prestige journals. The emergence of journal cascades (automatic referrals from one journal to another journal within the same publisher) and the introduction of APCs (especially for special issues) also contribute to commercial incentives driving article growth. On the researcher side, he argues that there is an apparent demand from researchers for more publishing outlets and simultaneous salami slicing by researchers because authors feel they have to distribute relatively more publications among journals that are perceived to be of lower quality (higher acceptance rates) in order to gain equivalent prestige to that of a higher impact paper. The state of peer review also impacts the firehose. The drain of PhD qualified scientists out of academia, compounded by a lack of recognition for peer review, further contributes to the firehose problem because there are insufficient reviewers in the system, especially for legitimate journals. Moreover, what peer review is done is no guarantee of quality (in highly selective journals as well as ‘predatory’). One of his conclusions is that there is not just a crisis in scholarly publishing but in peer review specifically and it is this crisis that will undermine science the most. Add AI into the mix of this publish or perish culture, and he predicts the firehose will burst.

He suggests that the solution lies in researchers taking back power themselves by writing more but ‘publishing’ less. By writing more he means outputs beyond traditional journal publications such as policy briefs, blogs, preprints, data, code and so on, and that these should count as much as peer-reviewed publications. He places special emphasis on the potential role of preprints and on open and more collegiate preprint review acting as a filter upstream of the publishing firehouse. He ends with a call for more collegiality across all stakeholders to align the incentives and thus alleviate the pressure causing the firehose in the first place.

General Comment

I enjoyed reading the essay and think the author does a good job of exposing multiple incentives and competing interests in the system. Although discussion of perverse incentives has been raised in many articles and blog posts, the author specifically focuses on some of the key commercial drivers impacting publishing and the responses of researchers to those drivers. I found the essay compellingly written and thought provoking although it took me a while to work through the various layers of incentives.  In general, I agree with the incentives and drivers he has identified and especially his call for stakeholders to avoid polarization and work together to repair the system. Although I appreciate the need to have a focused argument I did miss a more in-depth discussion about the equally complex layers of incentives for institutions, funders and other organisations (such as Clarivate) that also feed the firehose.

I note that my perspective comes from a position of being deeply embedded in publishing for most of my career. This will have also impacted what I took away from the essay and the focus of my comments below.

Main comments

1. I especially liked the idea of a ‘superstructure’ of incentives as I think that gives a sense of the size and complexity of the problem. At the same time, by focusing on publisher incentives and researchers’ response to them he has missed out important parts of the superstructure contributing to the firehose, namely the role of institutions and funders in the system. Although this is implicit, I think it would have been worth noting more, in particular:

   • He mentions institutions and the role of tenure and promotion towards the end but not the extent of the immense and immobilizing power this wields across the system (despite initiatives such as DORA and CoARA).

   • Most review panels (researchers) assessing grants for funders are also still using journal publications as a proxy for quality, even if the funder policy states journal name and rank should not be used

   • Many Institutions/Universities still rely on number and venue of publications. Although some notable institutions are moving away from this, the impact factor/journal rank is still largely relied on. This seems especially the case in China and India for example, which has shown a huge growth in research output. Although the author discusses the firehose, it would have been interesting to see a regional breakdown of this.

   • Libraries also often negotiate with publishers based on volume of articles – i.e they want evidence that they are getting more articles as they renegotiate a specific contract (e.g. Transformative agreements), rather than e.g. also considering the quality of service.

   • Institutions are also driven by rankings in a parallel way to researchers being assessed based on journal rank (or impact factor). How University Rankings are calculated is also often opaque (apart from the Leiden rankings) but publications form a core part. This further incentivises institutions to select researchers/faculty based on the number and venue of their publications in order to promote their own position in the rankings (and obtain funding)

2. The essay is also about power dynamics and where power in the system lies. The implication in the essay is that power lies with the publishers and this can be taken back by researchers. Publishers do have power, especially those in possession of high prestige journals and yet publishers are also subject to the power of other parts of the system, such as funder and institutional evaluation policies. Crucially, other infrastructure organisations, such as Clarivate, that provide indexing services and citation metrics also exert a strong controlling force on the system, for example:

   • Only a subset of journals are ever indexed by Clarivate. And funders and Institutions also use the indexing status of a journal as a proxy of quality. A huge number of journals are thus excluded from the evaluation system (primarily in the arts and humanities but also many scholar-led journals from low and middle income countries and also new journals). This further exacerbates the firehose problem because researchers often target only indexed journals. I’d be interested to see if the firehose problem also exists in journals that are not traditionally indexed (although appreciate this is also likely to be skewed by discipline)

   • Indexers also take on the role of arbiters of journal quality and can choose to delist or list journals accordingly. Listing or delisting has a huge impact on the submission rates to journals that can be worth millions of dollars to a publisher, but it is often unclear how quality is assessed and there seems to be a large variance in who gets listed or not.

   • Clarivate are also paid large fees by publishers to use their products, which creates a potential conflict of interest for the indexer as delisting journals from major publishers could potentially cause a substantial loss of revenue if they withdraw their fees. Also Clarivate relies on publishers to create the journals on which their products are based which may also create a conflict if Clarivate wishes to retain the in-principle support of those publishers.

   • The delisting of elife recently, even though it is an innovator and of established quality, shows the precariousness of journal indexing.

3. All the stakeholders in the system seem to be essentially ‘following the money’ in one way or another – it’s just that the currency for researchers, institutions, publishers and others varies. Publishers – both commercial and indeed most not-for profit -  follow the requirements of the majority of their ‘customers’  (and that’s what authors, institutions, subscribers etc are in this system) in order to ensure both sustainability and revenue growth. This may be a legacy of the commercialisation of research in the 20th Century but we should not be surprised that growth is a key objective for any company. It is likely that commercial players will continue to play an important role in science and science communication; what needs to be changed are the requirements of the customers.

4. The root of the problem, as the author notes, is what is valued in the system, which is still largely journal publications. The author’s solution is for researchers to write more – and for value to be placed on this greater range of outputs by all stakeholders. I agree with this sentiment – I am an ardent advocate for Open Science. And yet, I also think the focus on outputs per se and not practice or services is always going to lead to the system being gamed in some way in order to increase the net worth of a specific actor in the system. Preprints and preprint review itself could be subject to such gaming if value is placed on e.g. the preprint server or the preprint-review platform as a proxy of preprint and then researcher quality.

5. I think the only way to start to change the system is to start placing much more value on both the practices of researchers (as well as outputs) and on the services provided by publishers. Of course saying this is much easier than implementing it.

Other comments

1. A key argument is that higher acceptance rates actually create a perverse incentive for researchers to submit as many manuscripts as possible because they are more likely to get accepted in journals with higher acceptance rates. I disagree that higher acceptance rates per se are the main incentive for researchers to publish more. More powerful is the fact that those responsible for grants and promotion continue to use quantity of journal articles as a proxy for research quality.

2. Higher acceptance rates are not necessarily an indicator of low quality or a bad thing if it means that null, negative and inconclusive results are also published

3. The author states that Journal Impact Factors might have been an effective measure of quality in the past.  I take issue with this because the JIF has, as far as I know, always been driven by relatively few outliers (papers with very high citations) and I don’t know of evidence to show that this wasn’t also true in the past. It also makes the assumption that citations = quality.

4. The author asks at one point “Why would field specialization need a lower threshold for publication if the merits of peer review are constant? ” I can see a case for lower thresholds, however, when the purpose of peer review is primarily to select for high impact, rather than rigour, of the science conducted. A similar case might be made for multidisciplinary research, where peer reviewers tend to assess an article from their discipline’s perspective and reject it because the part that is relevant to them is not interesting enough… Of course, this all points to the inherent problems with peer review (with which I agree with the author)

5. The author puts his essay in appropriate context, drawing on a range of sources to support his argument. I particularly like that he tried to find source material that was openly available.

6. He cites 2 papers by Bjoern Brembs to substantiate the claim that there is potentially poorer review in higher prestige journals than in lower ranked journals. These papers were published in 2013 and 2018 and the conclusions relied, in part, on the fact that higher ranked journals had more retractions. Apart from a potential reporting bias, given the flood of retractions across multiple journals in more recent years, I doubt this correlation now exists?

7. The author works out submission rates from the published acceptance rates of journals. The author acknowledges this is only approximate and discusses several factors that could inflate or deflate it. I can add a few more variables that could impact the estimate, including: 1) the number of articles a publisher/journal rejects before articles are assigned to any editor (e.g. because of plagiarism, reporting issues or other research integrity issues), 2) the extent to which articles are triaged and rejected by editors before peer review (e.g. because it is out of scope or not sufficiently interesting to peer review); the number of articles rejected after peer review;  and 4) the extent to which authors independently withdraw an article at any stage of the process. When publishers publish acceptance rates, they don’t make it clear what goes into the numerator or the denominator and there are no community standards around this. The author rightly notes this process is too opaque.

Catriona J. MacCallum

As is my practice, I do not wish to remain anonymous. Please also note that I work for a large commercial publisher and am writing this review in an independent capacity such that this review reflects my own opinion, which are not necessarily those of my employer.

This is a well written and clear enough piece that may be helpful for a reader new to the topic. To people familiar with the field there is not so much which is new here. The final recommendation is not well expressed. As currently put it is, I think, wrong. But it is a provocative idea. I comment section by section below.

The first paragraphs repeat well established facts that there are too many papers. Seppelt et al’s contribution is missing here. It also reproduces the disengenuous claim, by a publisher’s employee, that publishers ‘only’ respond to demand. I do not think that is true. They create demand. They encourage authors to write and submit papers, as anyone who has been emailed by MDPI recently can testify. Why repeat something which is so inaccuate?

The section on ‘upstream of the nozzle’ is rather confusing. I think the author is trying to establish if more work is being submitted. But this cannot be deduced from the data presented. No trends are given. Rejection rates will be a poor guide if the same paper is being rejected by several journals. I was also confused by the sources used to track growth in papers – why not just use Dimensions data? The final paragraph again repeats well known facts about the proliferation of outlets and salami slicing. Thus far the article has not introduced new arguments.

Minor points in this section:

• there are some unsupported claims. Eg ‘This is a practice that is often couched within the seemingly innocuous guise of field specialty journals.’

• I also do not understand the logic of this rather long sentence: ‘The expansion of journals with higher acceptance rates alters the rational calculus for researchers - all things being equal higher acceptance rates create a perverse incentive to submit as many manuscripts as possible since the underlying probability of acceptance is simply higher than if those same publications were submitted to a journal with a lower acceptance rate, and hence higher prestige.’ I suggest it be rephrased

The section on peer review (Who’s testing the water) is mostly a useful review of the issues. But there are some problems which need addressing. Bizarrely, when discussing whether there enough scientists, it fails to mention Hanson et al’s global study, despite linking to it’s preprint in the opening lines. Instead the author adopts a parochial North American approach and refers only to PhDs coming from the US. It is not adequate to take trends in one country to cannot explain an international publishing scene. These are not the ‘good data’ the author claims. Likewise the value of data on doctorates not going onto a post-doc hinges on how many post-docs there are. That trend is not supplied. This statement ‘Almost everyone getting a doctorate goes into a non-university position after graduation’ may be true, but no supporting data are supplied to justify it. Nor do we know what country, or countries, the author is referring to.

The section ‘A Sip from the Spring’ makes the mistaken claim that researchers hold market power. This is not true. Researchers institutions, their libraries and governments are the main source of publisher income. It is here that the key proposal for improvement is made: researcher can write more and publish less. But if the problem is that there is too much poorly reviewed literature then this cannot be the solution. Removing all peer review, would mean there is even more material to read whose appearance is not slowed up by peer review at all. If peer review is becoming inadequate, evading it entirely is hardly a solution.

This does not mean we should not release pre-prints. The author is right to advocate them, but the author is mistaken to think that this will reduce publishing pressures. The clue is in their name ‘pre-print’. Publication is intended.

Missing from the author’s argument is recognition of the important role that communities of researchers form, and the roles that journals play in providing venues for conversation, disagreement and disucssion. They provide a filter. Yes researchers produce other material than publications as the author states: ‘grant proposals, editorials, policy briefs, blog posts, teaching curricula and lectures, software code and documentation, dataset curation, and labnotes and codebooks.’ I would add email and whatsapp messages to that list. But adding all that to our reading lists will not reduce the volume of things to be read. It must increase it. And it would make it harder to marshall and search all those words.

But the idea is provocative nonetheless. Running through this paper, and occasionally made explicit, is the fact that publishers earn billions from their ‘service’ to academia. They have a strong commercial interest in our publishing more, and in competing with each other to produce a larger share of the market. If writing more, and publishing less, means we need to find ways of directing our thoughts so that they earn less money for publishers, then that could bring real change to the system.

A minor point: the fire hose analogy is fully exploited and rather laboured in this paper. But it is a North American term and image, that does not travel so easily.

A few months back, Upstream editor Martin Fenner suggested that I submit my Upstream blog post titled, Drinking from the Firehose? Write More and Publish Less, for peer-review as a sort of experiment for Upstream through MetaROR. MetaROR, a relative newcomer to the scholarly communication community, provides the review and curate steps in the "publish-review-curate" model for meta-research.

While I do not consider myself a meta-researcher (scholars who conduct research on research) many of my positions on science policy have implications on the field (especially, those on transparency, openness, and reproducibility). I think the main call in my blog post for reform in scholarly communication – namely, to stop publishing in traditional journals as much and start rewarding a broader swath of scholarly activities like data sharing – is particularly appealing to meta-researchers who rely on non-publication outputs for their work. So, I submitted. The article was openly reviewed, and MetaROR provided an editorial assessment. Here, I reply to the reviewers and contribute to the curation of the original post.

The reviews are very high-quality - in fact, they are some of the most well-reasoned reviews I've received in the 20 years I've been a scholar. If MetaROR represents the future of peer-review through the publish-review-curate model, scholarly communication is about to get a whole lot better. You can read the open reviews of my blog post here. The revised version of the editorial is here.

Like traditional peer-review, each individual reviewer provided their feedback independently of the others and the handling editor did not curate the reviews. I prefer when editors do such curation since it helps to organize the response in a way that reduces redundancy. This is one of the main benefits of the group-based peer review systems - such as PREreview's Live Review. Also, there was no easy way (or at least not an obvious one) to export the reviews in plaintext from MetaROR so I could respond point-by-point in software of my choice. Below is an attempt to organize my response roughly around the major criticisms and suggestions in the review. Because this was an opinion piece and not research, I'm not going to respond to every point anyway – nearly all of which I would accept and revise accordingly had this been a research article.

Too Easy on the Publishers, Too Hard on Researchers

All three reviewers expressed some dismay over how light my criticism of the publishers was in my blog piece. I do not disagree. The reviewers rightfully point out that the publishers play outsized role in the inequity created in the scholarly communication space. However, I am choosing not to revise here much as the essay was already too long - it would have taken a tome to articulate my criticism of the publishers. That's out of scope. However, I revised the first paragraph in the conclusion to state:

The publishers are incentivized to avoid any other form of reform - this is the rational option that publishers choose in response to the apparent demand from researchers - as Ciavarella rightly pointed out.

Two of the reviewers also thought I was too harsh on researchers. I don't think that I was overly harsh. All three agree with me that researchers have some market role here but disagree with the extent to which they can exert influence. One reviewer claims researchers have no market power (to which I respectfully disagree). I've clarified in the paper that: 'the power any individual researcher has here is small. Collective action is needed.' I reject that researchers are blameless for the status quo - complacency empowers the publishers. Unfortunately, it's also baked into the superstructure of the reward system that is perpetuated by publisher-controlled market forces. I also added the following sentiment along these lines when discussing market-power of researchers:

It's free to share and read research without the need for costly, anticompetitive gatekeeping. Leveraging that freedom is an untapped source of market power.

Focus More on Institutions and Funders and Communities

Two of the three reviewers thought I needed to draw more attention to the roles, demands, and influence that academic institutions, publisher consortia, libraries, indexing services, scholarly societies, and grassroots research organizations have in this ecosystem. I agree with all these points - and had Clarivate's irresponsible delisting of eLife in the Web of Science happened before I wrote the original piece, I would have highlighted that as one reviewer suggested.

No New Arguments or Analysis

The reviewers felt that, while well-articulated, the arguments I was espousing are not novel. First, I think it is worthy to renew the idea that we should be more selective in choosing what to publish in journals. Focusing on quality over quantity and valuing activities beyond journal publications should be repeated often until it's common practice.

One comment called for more data and analysis, and another wanted some additional research cited. I think that's a great idea and I hope the reviewers can do that work or perhaps the open review will inspire others to do so.

In response to the criticism that preprints themselves both presuppose an eventual traditional publication and that they could be gamed, I revised that section accordingly:

There is risk of gaming preprints and preprint review just as there is in traditional publishing, such as by placing value on a paper for where it appears or how it was reviewed without considering its quality or contribution to science.

One reviewer misunderstood my point about preprints altogether:

Removing all peer review, would mean there is even more material to read whose appearance is not slowed up by peer review at all. If peer review is becoming inadequate, evading it entirely is hardly a solution. This does not mean we should not release pre-prints. The author is right to advocate them, but the author is mistaken to think that this will reduce publishing pressures. The clue is in their name ‘pre-print’. Publication is intended.

I am absolutely not arguing for tossing out peer review. I strongly believe peer review is valuable but currently broken. Moreover, I reject that peer review needs to happen behind the gatekeeping of publishers. I revised to clarify here and added a footnote based on this reviewer's latter observation.

Peer-review remains a critical check for pollutants in the waters - but the prevailing model needs significant reform. The traditional opaque, uncompensated system has eroded the quality, transparency, timeliness, and appropriateness of peer review due to competing priorities and a lack of appropriately aligned incentive structures. Novel models of peer review including, publish-review-curate and preprint review, and compensated review - ideally all done transparently and with conflicts of interest declared out in the open. At the same time, not all manuscripts need review to have value and most preprints with value (even those with reviews) should not be published in journals.

New footnote: The term 'preprint' is evolving - what was once a moniker for non-peer reviewed manuscript intended to eventually become reviewed and published (or more likely, rejected) now scopes-in other forms including publish-curate-review and manuscripts with preprint reviews. A new labeling and metadata system is desperately needed to highlight the state of review of a particular manuscript in a record of versions. Version control systems and badging are ubiquitous in the open-source software community and could be easily adopted here.

Volume is Volume is Volume

Probably the most important critique among the set of reviews points out an apparent recursion in the logic of the thesis that I need to clarify: you can't solve the firehose problem by writing more, as that just adds more volume to the flow. My revision to the conclusion clarifies my intent: what I'm proposing is to stop sending so many papers to journals for publication and to choose preprints more often for reading, reviewing, and writing. At the same time the system should, maintain or increase non-publication scholarly outputs and reward those too.

"Write-More" here is a placeholder for all the non-publication writing scholars do and should get credit for from their institutions and fields. Again, I happen to focus on writing because that's what I care about in this editorial and it would take volumes to pontificate on all the other services and activities that happen within the academy that are not properly rewarded.

Summary

Having my blog post peer-reviewed through MetaROR was a positive experience and I recommend the service. However, my post was still just an editorial – my opinions and thoughts – not research. Had this been a research article, however, the reviews as presented would have been a very good roadmap to improving the paper. For MetaROR, I have two suggestions: 1) the editorial assessment could be improved by organizing the key points and 2) create a way to have all reviews downloadable in plaintext for ease of importing into an editor.

Acknowledgments

Special thanks are owed to the reviewers, Catriona MacCallum, Dan Brockington, and Jonny Coates, the MetaROR handling editor Ludo Waltman, and to Upstream Editor and Front Matter founder Martin Fenner for the crazy idea to peer-review a blog post.

Disclosure

The opinions expressed here are my own and may not represent those of my employer, my associates, or the reviewers. I have no conflicts of interest to disclose.

This author response was previously published on Upstream.

Author response:

Evidence reducibility and clarity

Reviewer 1:

In this manuscript, the role of the insulin receptor and the insulin growth factor receptor was investigated in podocytes. Mice, were both receptors were deleted, developed glomerular dysfunction and developed proteinuria and glomerulosclerosis over several months. Because of concerns about incomplete KO, the authors generated podocyte cell lines where both receptors were deleted. Loss of both receptors was highly deleterious with greater than 50% cell death. To elucidate the mechanism, the authors performed global proteomics and find that spliceosome proteins are downregulated. They confirm this by using long-range sequencing. These results suggest a novel role for these pathways in podocytes.

Thank you

This is primarily a descriptive study and no technical concerns are raised. The mechanism of how insulin and IGF1 signaling are linked to the spiceosome is not addresed.

We do not think the paper is descriptive as we used non-biased phospho and total proteomics in the DKO cells to uncover the alterations in the spliceosome (that have not been previously described) that were detrimental. However, we are happy to look further into the underlying mechanism.

We would propose:

(1) Stimulating/inhibiting insulin/IGF signalling pathways in the Wild-type and DKO knockout cells and check expression levels and/or phosphorylation status of splice factors (including those in Figure 3E) and those revealed by phospho-proteomic data; a variety of inhibitors of insulin/IGF1 pathways could also be used along the pathways that are shown in Fig 2.

(2) Looking at the RNaseq data bioinformatically in more detail – the introns/exons that move up or down are targets of the splice factors involved; most splice factors binding sequences are known, so it should be possible to ask bioinformatically – from the sequences around the splice sites of the exons and introns that move in the DKO, which splice factors binding sites are seen most frequently? To uncover splice factors/RNA-binding proteins (RBPs) that are involved in the insulin signaling we will use a software named MATT which was specifically designed to look for RNA-binding motifs (PMID 30010778). In brief, using the long-sequencing data, we will test 250 nt sequences flanking the splice sites of all regulated splicing events (intronic and exonic) against all RNA- binding proteins in the CISBP-RNA database (PMID 23846655) using MATT. This will result in a list of RBPs potentially involved in the insulin signaling. We will validate these by activating insulin signaling (similar to Figures 2 B,C) and probe whether the RBPs are activated (e.g. phosphorylated or change in expression) or we will manipulate expression of the candidate RBPs and measure how they affect the insulin signaling.

(3) Examining the phospho and total proteomic data for IGF1R and Insulin receptor knockout alone podocytes (which we have already generated) and analysing these in more detail and include this data set to elucidate the relative importance of both receptors to spliceosome function.

The phenotype of the mouse is only superficially addressed. The main issues are that the completeness of the mouse KO is never assessed nor is the completeness of the KO in cell lines. The absence of this data is a significant weakness.

We apologise for not making clear but we did assess the level of receptor knockdown in the animal and cell models.  The in vivo model showed variable and non-complete levels of insulin receptor and IGF1 receptor podocyte knock down (shown in supplementary figure 1B). This is why we made the in vitro  floxed podocyte cell lines in which we could robustly knockdown both the insulin receptor and IGF1 receptor (shown in Figure 2A)

The mouse experiments would be improved if the serum creatinines were measured to provide some idea how severe the kidney injury is.

We can address this:

We have further urinary Albumin:creatinine ratio (uACR) data at 12, 16 and 20 weeks. We also have more blood tests of renal function that can be added. There is variability in creatinine levels which is not uncommon in transgenic mouse models (probably partly due to variability in receptor knock down with cre-lox system). This is part of rationale of developing the robust double receptor knockout cell models where we knocked out both receptors by >80%.

An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful. If this didn't work, an explanation in the text would suffice.

We would consider  over express SF3BF4 in the Wild type and DKO cells and assess the effects on spliceosome if deemed necessary.  However, we think it is unlikely to rescue the phenotype as so many other spliceosome components are downregulated in the DKO cells.

As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on.

We have some detail on this and can add to the manuscript. However it is not extensive as not a major driver of this work.

Lastly, the authors should caveat the cell experiments by discussing the ramifications of studying the 50% of the cells that survive vs the ones that died.

Thank you, we appreciate this and this was the rationale behind cells being studied after 2 days differentiation before significant cell loss in order to avoid the issue of studying the 50% of cells that survive.

Reviewer 2:

In this manuscript, submitted to Review Commons (journal agnostic), Coward and colleagues report on the role of insulin/IGF axis in podocyte gene transcription. They knocked out both the insulin and IGFR1 mice. Dual KO mice manifested a severe phenotype, with albuminuria, glomerulosclerosis, renal failure and death at 4-24 weeks.

Long read RNA sequencing was used to assess splicing events. Podocyte transcripts manifesting intron retention were identified. Dual knock-out podocytes manifested more transcripts with intron retention (18%) compared wild-type controls (18%), with an overlap between experiments of ~30%.

Transcript productivity was also assessed using FLAIR-mark-intron-retention software. Intron retention w seen in 18% of ciDKO podocyte transcripts compared to 14% of wild-type podocyte transcripts (P=0.004), with an overlap between experiments of ~30% (indicating the variability of results with this method). Interestingly, ciDKO podocytes showed downregulation of proteins involved in spliceosome function and RNA processing, as suggested by LC/MS and confirmed by Western blot.

Pladienolide (a spliceosome inhibitor) was cytotoxic to HeLa cells and to mouse podocytes but no toxicity was seen in murine glomerular endothelial cells.<br /> Specific comments.

The manuscript is generally clear and well-written. Mouse work was approved in advance. The six figures are generally well-designed, bars/superimposed dot-plots.

Thank you

Evaluation.

Methods are generally well described. It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity.

We did this and will add this information to the methods/figure legend.

Specific comments.

(1) Data are presented as mean/SEM. In general, mean/SD or median/IQR are preferred to allow the reader to evaluate the spread of the data. There may be exceptions where only SEM is reasonable.

Graphs can be changed to SD rather than SEM.

(2) It would be useful to for the reader to be told the number of over-lapping genes (with similar expression between mouse groups) and the results of a statistical test comparing WT and KO mice. The overlap of intron retention events between experimental repeats was about 30% in both knock-out podocytes. This seems low and I am curious to know whether this is typical for typical for this method; a reference could be helpful.

This is an excellent question. We had 30% overlap as the parameters used for analysis were very stringent. We suspect we could get more than 30% by being less stringent, which still be considered as similar events if requested. Our methods were based on FLAIR analysis (PMID: 32188845)

(3) Please explain "adjusted p value of 0.01." It is not clear how was it adjusted. The number of differentially-expressed proteins between the two cell types was 4842.

We used the Benjamini-Hochberg method to adjust our data. We think the reviewer is referring to the transcriptomic data and not the proteomic data.

Minor comments

Page numbers in the text would help the reviewer communicate more effectively with the author.

We will do this

Reviewer 3:

These investigators have previously shown important roles for either insulin receptor (IR) or insulin-like growth factor receptor (IGF1R) in glomerular podocyte function. They now have studied mice with deletion of both receptors and find significant podocyte dysfunction. They then made a podocyte cell line with inducible deletion of both receptors and find abnormalities in transcriptional efficiency with decreased expression of spliceosome proteins and increased transcripts with impaired splicing or premature termination.

The studies appear to be performed well and the manuscript is clearly written.

Thank you

Referees cross-commenting

I am in agreement with Reviewer 1 that the studies are overly descriptive and do not provide sufficient mechanism and the lack of more investigation of the in vivo model is a significant weakness.

Please see our responses to reviewer 1 above.

Significance

Reviewer 1:

With the GLP1 agonists providing renal protection, there is great interest in understanding the role of insulin and other incretins in kidney cell biology. It is already known that Insulin and IGFR signaling play important roles in other cells of the kidney. So, there is great interest in understanding these pathways in podocytes. The major advance is that these two pathways appear to have a role in RNA metabolism, the major limitations are the lack of information regarding the completeness of the KO's. If, for example, they can determine that in the mice, the KO is complete, that the GFR is relatively normal, then the phenotype they describe is relatively mild.

Thank you. The receptor  KO in the mice is unlikely to be complete (Please see comments above and Supplementary Figure 1b). There are many examples of KO models targeting other tissues showing that complete KO of these receptors seems difficult to achieve , particularly in reference to the IGF1 receptor. In the brain (which is also terminally differentiated cells PMID:28595357 (barely 50% iof IGF1R knockdown was achieved in the target cells). Ovarian granulosa cells PMID:28407051 -several tissue specific drivers tried but couldn't achieve any better than 80%. The paper states that 10% of IGF1R is sufficient for function in these cells so they conclude that their knockdown animals are probably still responding to IGF1. Finally, in our recent IGF1R podocyte knockdown model we found Cre levels were important for excision of a single floxed gene (PMID: 38706850) hence we were not surprised that trying to excise two floxed genes (insulin receptor and IGF1 receptor) was challenging. This is the rationale for making the double receptor knockout cell lines to understand process / biology in more detail.

Reviewer 2:

The manuscript is generally clear and well-written. Mouse work was approved in advance. The figures are generally well-designed, bars/superimposed dot-plots.

Evaluation.

Methods are generally well described. It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity.

Thank you we will do this.

Reviewer 3:

There are a number of potential issues and questions with these studies.

(1) For the in vivo studies, the only information given is for mice at 24 weeks of age. There needs to be a full time course of when the albuminuria was first seen and the rate of development. Also, GFR was not measured. Since the podocin-Cre utilized was not inducible, there should be a determination of whether there was a developmental defect in glomeruli or podocytes. Were there any differences in wither prenatal post natal development or number of glomeruli?

Thank you we will add in further phenotyping data. We do not think there was a major developmental phenotype as  albuminuria did not become significantly different until several months of age. We could have used a doxycycline inducible model but we know the excision efficiency is much less than the podocin-cre driven model SUPP FIGURE 1. This would likely give a very mild (if any) phenotype and not reveal the biology adequately.

(2) Although the in vitro studies are of interest, there are no studies to determine if this is the underlying mechanism for the in vivo abnormalities seen in the mice. Cultured podocytes may not necessarily reflect what is occurring in podocytes in vivo.

Thank you for this we are happy to employ Immunohistochemistry (IHC) and immunofluorescence (IF) using spliceosome antibodies on tissue sections from DKO and control mice to examine spliceosome changes. However, as the DKO results in podocyte loss, there may not be that many DKO podocytes still present in the tissue sections. This will be taken into consideration.

(3) Given that both receptors are deleted in the podocyte cell line, it is not clear if the spliceosome defect requires deletion of both receptors or if there is redundancy in the effect. The studies need to be repeated in podocyte cell lines with either IR or IGFR single deletions.

Thank you. We have full total and phospho-proteomic data sets from single insulin receptor and IGF1 receptor knockout cell lines that we will investigate for this point.

(4) There are not studies investigating signaling mechanisms mediating the spliceosome abnormalities.

Thank you as outlined as above to reviewer 1 point 1 we are very happy to investigate insulin / IGF signalling pathways in more detail.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Manuscript number: RC-2025-02946

Corresponding author(s): Margaret, Frame

Roza, Masalmeh

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Reviewer #1

Evidence, reproducibility and clarity

Review of Masalmeh et al. Title: "FAK modulates glioblastoma stem cell energetics..."

Previous studies have implicated FAK and the related tyrosine kinase PYK2 in glioblastoma growth, cell migration, and invasion. Herein, using a murine stem cell model of glioblastoma, the authors used CRISPR to inactivate FAK, FAK-null cells selected and cloned, and lentiviral re-expression of murine FAK in the FAK-null cells (termed FAK Rx) was accomplished. FAK-/- cells were shown to possess epithelial characteristics whereas FAK Rx cells expressed mesenchymal markers and increased cell migration/invasion in vitro. Comparisons between FAK-/- and FAK Rx cells showed that FAK re-expressed increased mitochondrial respiration and amino acid uptake. This was associated with FAK Rx cells exhibiting filamentous mitochondrial morphology (potentially an OXPHOS phenotype) and decreased levels of MTFR1L S235 phosphorylation (implicated in mito morphology fragmentation). Mito and epithelial cell morphology of FAK-/- cells was reversed by treatment with Rho-kinase inhibitors that also increased mito metabolism and cell viability. Last, FAK-dependent glioblastoma tumor growth was shown by comparisons of FAK-/- and FAK Rx implantation studies.

The studies by Masalmeh provide interesting findings associating FAK expression with changes in mitochondrial morphology, energy metabolism, and glutamate uptake. According to the authors model, FAK expression is supporting a glioblastoma stem cell like phenotype in vitro and tumor growth in vivo. What remains unclear is the mechanistic connection to cell changes and whether or not these are be dependent on intrinsic FAK activity or as the Frame group has previously published, potentially FAK nuclear localization. The associations with MTFR1L phosphorylation and effects by Rho kinase inhibition are likely indirect and remind this reviewer of long-ago studies with FAK-null fibroblasts that exhibit epithelial characteristics, still express PYK2, exhibited elevated RhoA GTPase activity. Some of these phenotypes were linked to changes in RhoGEF and RhoGAP signaling with FAK and/or Pyk2. At a minimum, it would be informative to know whether Pyk2 signaling is relevant for observed phenotypes and whether the authors can further support their associations with FAK-targeted or FAK-Pyk2-targeted inhibitors or PROTACs.

Some questions that would enhance potential impact. 1. Cell generation. Please describe the analysis of FAK-/- clones in more detail. The "low viability" phenotype needs further explanation with regard to clonal expansion and growth characteristics?

Response:

• We included a better description and a supplementary figure in our revised manuscript to indicate that we have examined several FAK -/- clones and confirmed that our observations were not due to clonal variation; multiple clones displayed similar morphological changes (Figure S1D). We also show that the elongated mesenchymal-like morphology was observed at 48 h after nucleofecting the cells with the FAK‑expressing vector, before beginning G418 selection to enrich for cells expressing FAK (Figure S1C). We also included experiments to acutely modulate FAK signalling (detaching and seeding cells on fibronectin) (Figure S2D, E, F and Figure S3) to exclude the possibility that the profound effects are due to protocols/selection we used for generating FAK-deleted cells.
• Regarding the term “low viability”, we have clarified in the text that there is no significant difference in cell number (Figure S1A) or ‘cell viability’ when it is assessed by trypan blue exclusion (a non-mitochondria-dependent read-out) (Figure S1B) between FAK-expressing FAK Rx and FAK-/- cells cultured for three days under normal conditions. Therefore, we agree the term ‘cell viability’ in this context could be confusing and have replace "cell viability” with “metabolic activity as measured by Alamar Blue.” in Figure 1D and Figure 5B, and the corresponding text in the original manuscript. This wording more accurately reflects the data.

Figure 1F: need further support of MET change upon FAK KO and EMT reversion.

Response: We have added a heatmap (Figure S1E) illustrating the changes in protein expression of core-enriched EMT/MET genes products (by proteomics) after FAK gene deletion (EMT genes as defined in Howe et al., 2018) ; this strengthens the conclusion that the MET reversion morphological phenotype is accompanied by recognised MET protein changes.

Fig. 2: Need further support if FAK effects impact glycolysis or oxidative phosphorylation in particular as implicated by the stem cell model.

Response: We show that FAK impacts both glycolysis (Figure 2A, 2E, and 2F) and mitochondrial oxidative phosphorylation on the basis of the oxygen consumption rate (OCR) (Figure 2B, and 2D), showing both are contributing pathways to FAK-dependent energy production. We have clarified this in the text.

Is there a combinatorial potential between FAKi and chemotherapies used for glioblastoma. Need to build upon past studies.

Response: Yes, previous studies suggest that inhibiting FAK can sensitize GBM cells to chemotherapy (Golubovskaya et al., 2012; Ortiz-Rivera et al., 2023). We have included a paragraph in the discussion section to make sure this is clearer. Although it is not the subject of this study, we appreciate it is useful context.

The notation of changes in glucose transporter expression should be followed up with regard to the potential that FAK-expressing cells may have different uptake of carbon sources and other amino acids. Altered uptake could be one potential explanation for increase glycolysis and glutamine flux.

Response: We agree with the reviewer that glucose uptake could be contributing and we include data that 2 glucose transporters are indeed FAK-regulated namely Glucose transporter 1 (GLUT1, encoded by Slc2a1 gene) and Glucose transporter 3 (GLUT 3, encoded by Slc2a3 gene) (shown in Figure S2B and C).

It would be helpful to support the confocal microscopy of mitos with EM.

Response:

We are concerned (and in our experience) that Electron microscopy (EM) may introduce artefacts during sample preparation. In contrast, immunofluorescence sample preparation is less susceptible to artefacts. The SORA system we used is not a conventional point-scanning confocal microscope, but is a super-resolution module based on a spinning disk confocal platform (CSU-W1; Yokogawa) using optical pixel reassignment with confocal detection. This method enhances resolution in all dimensions with resolution in our samples measured at 120nm. This has been instructive in defining a new level of changes in mitochondrial morphology upon FAK gene deletion.

Lack of FAK expression with increased MTFR1 phosphorylation is difficult to interpret.

Response: We do not directly show that this phosphorylation event is causal in our experiments; however, we think it important to document this change since it has been published that phosphorylation of MTFR1 has been causally linked to the mitochondrial morphology we observed in other systems (Tilokani et al., 2022).

Need to have better support between loss of FAK and the increase in Rho signaling. Use of Rho kinase inhibitors is very limited and the context to FAK (and or Pyk2) remains unclear. Past studies have linked integrin adhesion to ECM as a linkage between FAK activation and the transient inhibition of RhoA GTP binding. Is integrin signaling and FAK involved in the cell and metabolism phenotypes in this new model?

Response: To better support the antagonistic effect of FAK on Rho-kinase (ROCK) signalling, we included a new experiment in which the integrin-FAK signalling pathway has been disrupted by treating FAK WT cells with an agent that causes detachment from the substratum, Accutase, and growing the cells in suspension in laminin-free medium. We present ROCK activity data, as judged by phosphorylated MLC2 at serine 19 (pMLC2 S19), relating this to induced FAK phosphorylation at Y397 (a surrogate for FAK activity) that is supressed after integrin disengagement. These measurements have been compared with conditions whereby integrin-FAK signalling is activated by growing the cells on laminin coated surfaces. We observed a time-dependent decrease in pFAK(Y397) levels (normalised to total FAK) in suspended cells compared to those spread on laminin, while pMLC2(S19) levels increased in a reciprocal manner over time in detached cells relative to spread cells (S4A and B). There is therefore an inverse relationship between integrin-FAK signalling and ROCK-MLC2 activity, consistent with findings from FAK gene deletion experiments. In the former case, we do not rely on gene deletion cell clones.

Significance

The studies by Masalmeh provide interesting findings associating FAK expression with changes in mitochondrial morphology, energy metabolism, and glutamate uptake. According to the authors model, FAK expression is supporting a glioblastoma stem cell like phenotype in vitro and tumor growth in vivo. What remains unclear is the mechanistic connection to cell changes and whether or not these are be dependent on intrinsic FAK activity or as the Frame group has previously published, potentially FAK nuclear localization. The associations with MTFR1L phosphorylation and effects by Rho kinase inhibition are likely indirect and remind this reviewer of long-ago studies with FAK-null fibroblasts that exhibit epithelial characteristics, still express PYK2, exhibited elevated RhoA GTPase activity. Some of these phenotypes were linked to changes in RhoGEF and RhoGAP signaling with FAK and/or Pyk2. At a minimum, it would be informative to know whether Pyk2 signaling is relevant for observed phenotypes and whether the authors can further support their associations with FAK-targeted or FAK-Pyk2-targeted inhibitors or PROTACs.

__Response: __

Deleting the gene encoding FAK in mouse embryonic fibroblasts leads to elevated Pyk2 expression (Sieg, 2000). However, in the GBM stem cell model we used here, Pyk2 was not expressed (determined by both transcriptomics and proteomics). We have included Figure S1E to show that PYK2 expression was undetectable in FAK -/- and FAK Rx cells at the RNA level (Figure S1F). We conclude that there is no compensatory increase in Pyk2 upon FAK loss in these cells. In the transformed neural stem cell model of GBM, we do not consistently or robustly detect nuclear FAK.

Review #2

Masalmeh and colleagues employ a neural stem/progenitor cell-based glioma model (NPE cells) to investigate the role of Focal Adhesion Kinase (FAK) in GBM, with a focus on potential links between the regulation of morphological/adhesive and metabolic GBM cell properties. For this, the authors employ wt cells alongside newly generated FAK-KO and -reexpressing cells, as well as pharmacological interventions to probe the relevance of specific signaling pathways. The authors´ main claims are that FAK crucially modulates glioma cell morphology, cell-cell and cell-substrate interactions and motility, as well as their metabolism, and that these effects translate to changes to relevant in vivo properties such as invasion and tumor growth.

My main issues are with the model chosen by the authors.

As per the methods section, generation of FAK-KO and -"Rx" NPE cells entailed protracted selection/expansion processes, which may have resulted in inadvertent selection for cellular/molecular properties unrelated to the desired one (loss or gain of FAK expression) and which may have had cascading effects on NPE cells. The authors nonetheless repeatedly claim the parameters they quantify, such as mitochondrial or cytoskeletal properties or metabolic features, to have directly resulted from FAK loss or reintroduction. Examples of such causal inferences are to be found in lines 123, 134/135, 165, 181. Such causal claims are, in my view, unsupported.

Acute perturbation of FAK expression/activity, genetically or pharmacologically, followed by a rapid assessment of the processes under investigation, would be needed to begin to assess causality, even if acute genetic perturbations may be technically challenging as sufficient gene expression reduction or restoration to physiologically relevant levels may be hard to achieve.

Response:

We would like to first comment on the model we used here, which we think will clarify the validity of our approach. The model is a transformed stem cell model of GBM that was published in (Gangoso et al., Cell, 2021) and is now used regularly in the GBM field. As mentioned in the response to Reviewer 1, we have added text (page 4 and 5 in the revised manuscript) and a new supplementary figure (Figure S1D) clarifying that the morphological changes we observed were consistent across multiple FAK -/- clones, showing this was not due to any inter-clonal variability. We also added images showing that the morphological changes were apparent at 48 h after nucleofecting FAK -/- cells with the FAK‑expressing vector specifically (not the empty vector), prior to starting G418 selection to enrich for FAK‑expressing cells (Figure S1C), addressing the worry that clonal variation and selection was the cause of the FAK-dependent phenotypes we observed. We believe that our model provides a type of well controlled, clean genetic cancer cell system of a type that is commonly used in cancer cell biology, allowing us to attribute phenotypes to individual proteins.

We have also carried out a more acute treatment by using the FAK inhibitor VS4718 to perturb FAK kinase activity and assessed the effects on glycolysis and glutamine oxidation after 48h treatment (Figure S2D, E and F). We found that treating the transformed neural stem cells (parental population) with FAK inhibitor (300nM VS4718) decreases glucose incorporation into glycolysis intermediates and glutamine incorporation into TCA cycle intermediates, consistent with a role for FAK’s kinase activity in maintaining glycolysis and glutamine oxidation.

The employed pharmacological modulation of ROCK activity is the only approach that, given the presumably acute nature of the treatment, may have allowed the authors to probe the proposed functional links. The methods section of the manuscript does not however comprise details as to the duration of these treatments, which leaves open the possibility of long-term treatment having been carried out (data shown in Figure 5B refers to 72hr treatment).

__Response: __

We have added the duration of the treatment to the Methods section and Figure Legends, to clarify that cells were treated with ROCK inhibitors for 24h, before assessing the effects on mictochondria (Figure 4C, D, S4C and D) and glutamine oxidation (Figure 5A, and S5). For metabolic activity by AlamarBlue assay, cells were treated with ROCK inhibitors for 72h (Figure 5B).

Even in the case of ROCK inhibitor experiments, it is however unclear if and how the effects on cell morphology and adhesion, mitochondrial organization and metabolic activity may be connected to each other and, if at all, to FAK expression.

Given the above uncertainties due to the nature of the model and experimental approaches, it is hard to assess the reliability and thus the relevance of the findings.

Response:

FAK suppresses ROCK activity (as judged by pMLC2 S19, Figure 4A and B). Treating FAK -/- cells with two different ROCK inhibitors restored mesenchymal-like cell morphology, mitochondrial morphology and glutamine oxidation. As mentioned above, to strengthen our evidence for the antagonistic role of FAK in ROCK-MLC2 signalling, we have now introduced an experiment whereby integrin-FAK signalling was disrupted through treatment with a detachment agent (Accutase), and subsequently maintaining the cells in suspension in laminin-free medium. We assessed pMLC2 S19 levels (a measure of ROCK activity) relating this to FAK phosphorylation that is supressed after integrin disengagement. These results were evaluated relative to spread wild type cells growing on laminin where Integrin-FAK signalling was active (Figure S4A and B). We observed an inverse relationship between Integrin-FAK signalling and ROCK-MLC2 activity in keeping with our conclusions (Figure 4A and B).

Experimental support for the ability of cell-substrate interaction modulation to concomitantly impact cellular metabolism and motility/invasion would be significant both in terms of advancing our understanding of glioma cell biology and of its translational potential, but the evidence being provided is at best compatible with the proposed model.

Response: We carried out a new experiment to support the ability of cell-substrate interaction modulation to impact metabolism; specifically, we inhibited cell-substrate interactions by plating the cells on Poly-2-hydroxyethyl methacrylate (Poly 2-HEMA)-coated dishes. This suppressed FAK phosphorylation at Y397, as expected, with concomitant reduction in glutamine utilisation in the TCA cycle (Figure S3A, B and C).

My background/expertise is in developmental and adult neurogenesis, in vivo modelling of gliomagenesis and cell fate control/reprogramming, with a focus on molecular mechanisms of differentiation and quantitative aspects of lineage dynamics; molecular details of the control of cellular metabolism, cell-cell adhesion and cytoskeletal dynamics are not core expertise of mine.

We appreciate this reviewer’s expertise are not necessarily in the cancer cell biology and genetic intervention aspects of our study. We hope that the explanations we have provided satisfy the reviewer that our conclusions are valid.

Author response:

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

Reviewer #1 (Public review): 

In this study, Ma et al. aimed to determine previously uncharacterized contributions of tissue autofluorescence, detector afterpulse, and background noise on fluorescence lifetime measurement interpretations. They introduce a computational framework they named "Fluorescence Lifetime Simulation for Biological Applications (FLiSimBA)" to model experimental limitations in Fluorescence Lifetime Imaging Microscopy (FLIM) and determine parameters for achieving multiplexed imaging of dynamic biosensors using lifetime and intensity. By quantitatively defining sensor photon effects on signal-to-noise in either fitting or averaging methods of determining lifetime, the authors contradict any claims of FLIM sensor expression insensitivity to fluorescence lifetime and highlight how these artifacts occur differently depending on the analysis method. Finally, the authors quantify how statistically meaningful experiments using multiplexed imaging could be achieved. 

A major strength of the study is the effort to present results in a clear and understandable way given that most researchers do not think about these factors on a day-to-day basis. The model code is available and written in Matlab, which should make it readily accessible, although a version in other common languages such as Python might help with dissemination in the community. One potential weakness is that the model uses parameters that are determined in a

specific way by the authors, and it is not clear how vastly other biological tissue and microscope setups may differ from the values used by the authors. 

Overall, the authors achieved their aims of demonstrating how common factors

(autofluorescence, background, and sensor expression) will affect lifetime measurements and they present a clear strategy for understanding how sensor expression may confound results if not properly considered. This work should bring to awareness an issue that new users of lifetime biosensors may not be aware of and that experts, while aware, have not quantitatively determined the conditions where these issues arise. This work will also point to future directions for improving experiments using fluorescence lifetime biosensors and the development of new sensors with more favorable properties. 

We appreciate the comments and helpful suggestions. We now also include FLiSimBA simulation code in Python in addition to Matlab to make it more accessible to the community.

One advantage of FLiSimBA is that the simulation package is flexible and adaptable, allowing users to input parameters based on the specific sensors, hardware, and autofluorescence measurements for their biological and optical systems. We used parameters based on a FRETbased sensor, measured autofluorescence from mouse tissue, and measured dark count/after pulse of our specific GaAsP PMT in this manuscript as examples. In Discussion and Materials and methods, we now emphasize this advantage and further clarify how these parameters can be adapted to diverse tissues, imaging systems, and sensors based on individual experiments. We further explain that these input parameters will not affect the conclusions of our study, but the specific input parameters would alter the quantitative thresholds.

Reviewer #2 (Public review): 

Summary: 

By using simulations of common signal artefacts introduced by acquisition hardware and the sample itself, the authors are able to demonstrate methods to estimate their influence on the estimated lifetime, and lifetime proportions, when using signal fitting for fluorescence lifetime imaging. 

Strengths: 

They consider a range of effects such as after-pulsing and background signal, and present a range of situations that are relevant to many experimental situations. 

Weaknesses: 

A weakness is that they do not present enough detail on the fitting method that they used to estimate lifetimes and proportions. The method used will influence the results significantly. They seem to only use the "empirical lifetime" which is not a state of the art algorithm. The method used to deconvolve two multiplexed exponential signals is not given. 

We appreciate the comments and constructive feedback. Our revision based on the reviewer’s suggestions has made our manuscript clearer and more user friendly. We originally described the detail of the fitting methods in Materials and methods. Given the importance of these methodological details for evaluating the conclusions of this study, we have moved the description of the fitting method from Materials and methods to Results. In addition, we provide further clarification and more details of the rationale of using these different methods of lifetime estimates in Discussion to aid users in choosing the best metric for evaluating fluorescence lifetime data.

More specifically, we modified our writing to highlight the following.

(1) In Results, we describe that lifetime histograms were fitted to Equation 3 with the GaussNewton nonlinear least-square fitting algorithm and the fitted P<sub1</sub> was used as lifetime estimation.

(2) In Results, we clarify that our simulation of multiplexed imaging was modeled with two sensors, each displaying a single exponential decay, but the two sensors have different decay constants. We also describe that Equation 3 with the Gauss-Newton nonlinear least-square fitting algorithm was used to deconvolve the two multiplexed exponential signals (Fig. 8)

Reviewer #3 (Public review): 

Summary: 

This study presents a useful computational tool, termed FLiSimBA. The MATLAB-based FLiSimBA simulations allow users to examine the effects of various noise factors (such as autofluorescence, afterpulse of the photomultiplier tube detector, and other background signals) and varying sensor expression levels. Under the conditions explored, the simulations unveiled how these factors affect the observed lifetime measurements, thereby providing useful guidelines for experimental designs. Further simulations with two distinct fluorophores uncovered conditions in which two different lifetime signals could be distinguished, indicating multiplexed dynamic imaging may be possible. 

Strengths: 

The simulations and their analyses were done systematically and rigorously. FliSimba can be useful for guiding and validating fluorescence lifetime imaging studies. The simulations could define useful parameters such as the minimum number of photons required to detect a specific lifetime, how sensor protein expression level may affect the lifetime data, the conditions under which the lifetime would be insensitive to the sensor expression levels, and whether certain multiplexing could be feasible. 

Weaknesses: 

The analyses have relied on a key premise that the fluorescence lifetime in the system can be described as two-component discrete exponential decay. This means that the experimenter should ensure that this is the right model for their fluorophores a priori and should keep in mind that the fluorescence lifetime of the fluorophores may not be perfectly described by a twocomponent discrete exponential (for which alternative algorithms have been implemented: e.g., Steinbach, P. J. Anal. Biochem. 427, 102-105, (2012)). In this regard, I also couldn't find how good the fits were for each simulation and experimental data to the given fitting equation (Equation 2, for example, for Figure 2C data). 

We thank the reviewer for the constructive feedback. We agree that the FLiSimBA users should ensure that the right decay equations are used to describe the fluorescent sensors. In this study, we used a FRET-based PKA sensor FLIM-AKAR to provide proof-of-principle demonstration of the capability of FLiSimBA. The donor fluorophore of FLIM-AKAR, truncated monomeric enhanced GFP, displays a single exponential decay. FLIM-AKAR, a FRET-based sensor, displays a double exponential decay. The time constants of the two exponential components were determined and reported previously (Chen, et al, Neuron (2017)).  Thus, a double exponential decay equation with known τ₁ and τ₂ was used for both simulation and fitting. The goodness of fit is now provided in Supplementary Fig. 1 for both simulated and experimental data. In addition to referencing our prior study characterizing the double exponential decay model of FLIM-AKAR in Materials and methods, we have emphasized in Discussion the versality of FLiSimBA to adapt to different sensors, tissues, and analysis methods, and the importance of using the right mathematical models to describe the fluorescence decay of specific sensors. 

Also, in Figure 2C, the 'sensor only' simulation without accounting for autofluorescence (as seen in Sensor + autoF) or afterpulse and background fluorescence (as seen in Final simulated data) seems to recapitulate the experimental data reasonably well. So, at least in this particular case where experimental data is limited by its broad spread with limited data points, being able to incorporate the additional noise factors into the simulation tool didn't seem to matter too much.  

In the original Fig 2C, the sensor fluorescence was much higher than the contributions from autofluorescence, afterpulse, and background signals, resulting in minimal effects of these other factors, as the reviewer noted. This original figure was based on photon counts from single neurons expressing FLIM-AKAR. For the rest of the manuscript, photon counts were based on whole fields of view (FOV). Since the FOV includes cells that do not express fluorescent sensors, the influence of autofluorescence, dark currents, and background is much more pronounced, as shown in Fig. 2B. 

Both approaches – using photon counts from the whole FOV or from individual neurons – have their justifications. Photon counts from the whole FOV simulate data from fluorescence lifetime photometry (FLiP), whereas photon counts from individual neurons simulate data from fluorescence lifetime imaging microscopy (FLIM). However, the choice of approach does not affect the conclusions of the manuscript, as a range of photon count values are simulated. To maintain consistency throughout the manuscript, we have revised the photon counts in this figure (now Supplementary Fig. 1C) to match those from the whole FOV.

Additionally, we have made some modifications in our analyses of Supplementary Fig. 1C and Fig. 2B, detailed in the “FLIM analysis” section of Materials and methods. For instance, to minimize system artifact interference at the histogram edges, we now use a narrower time range (1.8 to 11.5 ns) for fitting and empirical lifetime calculation.

Reviewer #1 (Recommendations for the authors): 

(1) The authors report how autofluorescence was measured from "imaged brain slices from mice at postnatal 15 to 19 days of age without sensor expression." However, it remains unclear how many acute slices and animals were used (for example, were all 15um x 15um FOV from a single slice) and if mouse age affects autofluorescence quantification. Furthermore, would in vivo measurements have different autofluorescence conditions given that blood flow would be active? It would help if the authors more clearly explained how reliable their autofluorescence measurement is by clarifying how they obtained it, whether this would vary across brain areas, and whether in vitro vs in vivo conditions would affect autofluorescence. 

We have added description in Materials and methods that for autofluorescence ‘Fluorescence decay histograms from 19 images of two brain slices from a single mouse were averaged.’ We have added in Discussion that users should carefully ‘measure autofluorescence that matches the age, brain region, and data collection conditions (e.g., ex vivo or in vivo) of their tissue…’, and emphasize that FLiSimBA offers customization of inputs, and it is important for users to adapt the inputs such as autofluorescence to their experimental conditions. We also clarify in Discussion that the change of input parameters such as autofluorescence across age and brain region would not affect the general insights from this study, but will affect quantitative values.

(2) Does sensor expression level issues arise more with in-utero electroporation compared to AAV-based delivery of biosensors? A brief comment on this in the discussion may help as most users in the field today may be using AAV strategies to deliver biosensors.

In our experience, in-utero electroporation results in higher sensor expression than AAV-based delivery, and so pose less concern for expression-level dependence. However, both delivery methods can result in expression level dependence, especially with a sensor that is not bright. We have added in Discussion ‘For a sensor with medium brightness delivered via in utero electroporation, adeno-associated virus, or as a knock-in gene, the brightness may not always fall within the expression level-independent regime.’

(3) Figure 1. Should the x-axis on the top figures be "Time (ns)" instead of "Lifetime (ns)"?

Similarly in Figure 8A&B, wouldn't it make more sense to have the x-axis be Time not Lifetime?

The x-axis labels in Fig. 1 and Fig. 8A-8B have been changed to ‘Time (ns)’.   

(4) Figure 2b: why is the empirical lifetime close to 3.5ns? Shouldn't it be somewhere between

2.14 and 0.69? 

In our empirical lifetime calculation, we did not set the peak channel to have a time of 0.0488 ns (i.e. the laser cycle 12.5 ns divided by 256 time channels). Rather, we set the first time channel within a defined calculation range (i.e. 1.8 ns in Supplementary Fig. 1B) to have a time of 0.0488 ns (i.e.). Thus, the empirical lifetime exceeds 2.14 ns and depends on the time range of the histogram used for calculation. 

For Fig. 2B and Supplementary Fig. 1C, we have now adjusted the range to 1.8-11.5 ns to eliminate FLIM artifacts at the histogram edges in our experimental data, resulting in an empirical lifetime around 2.255 ns. In contrast, the range for calculating the empirical lifetime of simulated data in the rest of the study (e.g. Fig. 4D) is 0.489-11.5 ns, yielding a larger lifetime of ~3.35 ns. 

We have clarified these details and our rationale in Materials and methods.

(5) Figure 2b: how come the afterpulse+background contributes more to the empirical lifetime than the autofluorescence (shorter lifetime). This was unclear in the results text why autofluorescence photons did not alter empirical lifetime as much as did the afterpulse/background.

With a histogram range from 1.8 ns to 11.5 ns used in Fig. 2B, the empirical lifetime for FLIM-AKAR sensor fluorescence, autofluorescence, and background/afterpulse are: 2-2.3 ns, around 1.69 ns, and around 4.90 ns. The larger difference of background/afterpulse from FLIM-AKAR sensor fluorescence leads to larger influence of afterpulse+background than autofluorescence. We have added an explanation of this in Results.

(6) One overall suggestion for an improvement that could help active users of lifetime biosensors understand the consequences would be to show either a real or simulated example of a "typical experiment" conducted using FLIM-AKAR and how an incorrect interpretation could be drawn as a consequence of these artifacts. For example, do these confounds affect experiments involving comparisons across animals more than within-subject experiments such as washing a drug onto the brain slice, and the baseline period is used to normalize the change in signal? I think this type of direct discussion will help biosensor users more deeply grasp how these factors play out in common experiments being conducted.

We have added the following in Discussion, ‘…While this issue is less problematic when the same sample is compared over short periods (e.g. minutes), It can lead to misinterpretation when fluorescence lifetime is compared across prolonged periods or between samples when comparison is made across chronic time periods or between samples with different sensor expression levels. For example, apparent changes in fluorescence lifetime observed over days, across cell types, or subcellular compartments may actually reflect variations in sensor expression levels rather than true differences in biological signals (Fig. 6), Therefore, considering biologically realistic factors in FLiSimBA is essential, as it qualitatively impacts the conclusions.’

Reviewer #2 (Recommendations for the authors): 

The paper would be improved with more detail on the fitting methods, and the use of state-of-theart methods. Consult for example the introduction of this paper where many methods are listed: https://www.mdpi.com/1424-8220/22/19/7293

We have moved the description of the Gauss-Newton nonlinear least-square fitting algorithm from Materials and methods to Results to enhance clarity. We appreciate the reviewer’s suggestion to combine FLiSimBA with various analysis methods. However, the primary focus of our manuscript is to call for attention of how specific contributing factors in biological experiments influence FLIM data, and to provide a tool that rigorously considers these factors to simulate FLIM data, which can then be used for fitting. Therefore, we did not expand the scope of our manuscript. Instead, we have added in the Discussion that ‘‘FLiSimBA can be used to test multiple fitting methods and lifetime metrics as an exciting future direction for identifying the best analysis method for specific experimental conditions’, citing relevant references.

I would also improve the content of the GitHub repository as it is very hard to identify to source code used for simulation and fitting. 

We have reorganized and relabeled our GitHub repository and now have three folders labeled as ‘Simulation_inMatlab’, ‘DataAnalysis_inMatlab’, and ‘SimulationAnalysis_inPython’. We also updated the clarification of the contents of each folder in the README file.

Reviewer #3 (Recommendations for the authors): 

(1) P. 10 "For example, to detect a P1 change of 0.006 or a lifetime change of 5 ps with one sample measurement in each comparison group, approximately 300,000 photons are needed." If I am reading the graphs in Figures 3B and C, this sentence is talking about the red line. However, the intersection of 0.006 in the MDD of P1 in 3B and red is not 3E5 photons. And the intersection of 0.005 ns and red in 3C is not 3E5 photons either. Are you sure you are talking about n=1? Maybe the values are correct for the blue curve with n=5.

Thank you for catching our error. We have corrected the text to ‘with five sample measurements’.

(2) Figure 2 (B) legend: It would be helpful to specify what is being compared in the legend. For example, consider revising "* p < 0.05 vs sensor only; n.s. not significant vs sensor + autoF; # p < 0.05 vs sensor + autoF. Two-way ANOVA with Šídák's multiple comparisons test" to "* p <0.05 for sensor + auto F (cyan) vs sensor only; n.s. not significant for final simulated data (purple) vs sensor + autoF; # p < 0.05 for final simulated data (purple) vs sensor + autoF. Twoway ANOVA with Šídák's multiple comparisons test".

We’ve made the change and thanks for the suggestion to make it clearer.

(3) Figure 2 (c) Can you please show the same Two-way ANOVA test values for Experimental vs. Sensor only and for Experimental vs. Sensor + autoF? Currently, the value (n.s.) is marked only for Experimental vs. Final simulation. Given that the experimental data are sparse (compared to the simulations), it seems likely that there may be no significant difference among the 3 different simulations regarding how well they match the experimental data. Also, can you specify the P1 and P2 of the experimental data  used to generate the simulated data on this panel? Also, what is the reason why P1=0.5 was used for panels A and B, instead of the value matching the experimental value?

As the reviewer suggested, we have included statistical tests in the figure (now Supplementary Fig. 1C). Please see our response to the Public Review of Reviewer 3’s comments as well as our changes in Materials and Methods on other changes and their rationale for this figure. We have now specified the P₁ value of the experimental data used to generate the simulated data on this panel both in Figure Legends and Materials and Methods. Based on the suggestion, we have now used the same P₁ value in Fig. 2B.

This part really stands out as a necessary and urgent conversation. With how normalized AI tools have become on platforms like TikTok, I can see how some students might not fully grasp the seriousness of using them to generate explicit content. It’s not a harmless joke—it’s a form of harassment with real legal and emotional consequences. As someone who spends a lot of time online, I think we all need to take more responsibility in calling out this kind of behavior and making sure people know where to get help,

Author response:

The following is the authors’ response to the previous reviews

Reviewer #3 (Public Review)

Summary:

In this paper the authors examined the effects of strip cropping, a relatively new agricultural technique of alternating crops in small strips of several meters wide, on ground beetle diversity. The results show an increase in species diversity (i.e. abundance and species richness) of the ground beetle communities compared to monocultures.

Strengths:

The article is well written; it has an easily readable tone of voice without too much jargon or overly complicated sentence structure. Moreover, as far as reviewing the models in depth without raw data and R scripts allows, the statistical work done by the authors looks good. They have well thought out how to handle heterogenous, unbalanced and taxonomically unspecific yet spatially and temporarily correlated field data. The models applied and the model checks performed are appropriate for the data at hand. Combining RDA and PCA axes together is a nice touch. Moreover, after the first round of reviews, the authors have done a great job at rewriting the paper to make it less overstated, more relevant to the data at hand and more solid in the findings. Many of the weaknesses noted in the first review have been dealt with. The overall structure of the paper is good, with a clear introduction, hypotheses, results section and discussion.

We are grateful for this positive feedback. We are glad that our extensive revision after extensive review from three reviewers has paid off in addressing earlier weakness of our manuscript.

Weaknesses:

The weaknesses that remain are mainly due to a difficult dataset and choices that could have stressed certain aspects more, like the relationship between strip cropping and intercropping. The mechanistic understanding of strip cropping is what is at stake here. Does strip cropping behave similar to intercropping, a technique which has been proven to be beneficial to biodiversity because of added effects due to increased resource efficiency and greater plant species richness.

Unfortunately, the authors do not go into this in the introduction or otherwise and simply state that they consider strip cropping a form of intercropping.

We agree with the reviewer that a mechanistic understanding on how intercropping and strip cropping differ would be very interesting. However, we also feel that this topic is somewhat beyond the scope of the current manuscript. We are already planning work to elucidate mechanisms that may explain the pest and suppressive effects of strip cropping.

I also do not like the exclusive focus on percentages, as these are dimensionless. I think more could have been done to show underlying structure in the data, even after rarefaction.

While we generally agree with this point raised by the reviewer, for our heterogeneous dataset it was difficult to come up with meaningful units with dimensions. Therefore, we believe that percentages are the most suitable approach to present readers a fair comparison of the treatments.

A further weakness is a limited embedding into the larger scientific discourses other than providing references. But this may be a matter of style and/or taste

We believe our manuscript to be well-embedded within the relevant scientific discourse, but as indicated by reviewer 3 this might indeed be a matter of style/taste. Without exact examples it is difficult for us to judge this point.

Reviewer #3 (Recommendations for the authors): 

Suggestion for title: "Strip cropping shows promising preliminary increases in ground beetle community diversity compared to monocultures"

We agree that the title could indeed be nuanced. We incorporated the suggested title, except for the word “preliminary”, as we felt that this is slightly misplaced for a 4-year study conducted at 4 locations.

line 26: the word previous may be confusing to readers, as it suggests previous research on beetles or insects. I think it would be better to use for instance "related" or "productivity focused research"

We agree that this wording might be confusing, and changed it to “other studies showed”.

Line 84-85: this is vague. can you make explicit what you are trying to answer here?

We made “biodiversity metric changes” more explicit, and changed the sentence accordingly.

Line 88-89: I think this would fit better with the first question in line 83-84, so I suggest placing it upwards. Also, I think you mean abundant instead of common. Common suggests commonness in the entire population. Abundant suggests found often in this study. While these definitions may very much overlap, they are distinctly different.

We have moved this sentence up and changed “common” to “abundant”. To make the result section more in line with this section, we also moved the section on the relationship between crop configuration and abundant genera up.  

Line 146: defining rareness of species should be in the methods section. Also "following" would be better than "according"

We now added a sentence on how we examine habitat preferences and rarity in the methods section (line 316-317). We also changed “according to” to “following”.

Line 291: it is called being "flush" with the soil surface. This expression is not much used by non-native speakers, but is regularly encountered in studies on pitfalls, so the authors could decide to change the sentence using the proper English vernacular.

Suggestion incorporated.

Line 322-327, this method could do with a reference

This method is a relatively standard calculation to calculate relative changes and to center variation around zero. Nevertheless, we added a reference to a paper that used the same method.

Line: 333-335. I would still like to see a reference for this method.

This methodology has not been described in literature to the best of our knowledge. As we compared two crops within strip cropping with their respective monoculture references, we compare one strip cropping field with two monocultural fields. Here we took a conservative approach by comparing the strip crop field with the monoculture with the highest richness and activity density, to see if strip cropped fields outperformed monocultures with diverse ground beetle communities.

Line 364-366. references?

We have added references for these R packages.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors claim that they can use a combination of repetitive transcranial magnetic stimulation (intermittent theta burst-iTBS) and transcranial alternating current stimulation (gamma tACS) to cause slight improvements in memory in a face/name/profession task.

Strengths:

The idea of stimulating the human brain non-invasively is very attractive because, if it worked, it could lead to a host of interesting applications. The current study aims to evaluate one such exciting application.

Weaknesses:

(1) It is highly unclear what, if anything, transpires in the brain with non-invasive stimulation. To cite one example of many, a rigorous study in rats and human cadavers, compellingly showed that traditional parameters of transcranial electrical stimulation lead to no change in brain activity due to the attenuation by the soft tissue and skull (Mihály Vöröslakos et al Nature Communications 2018): https://www.nature.com/articles/s41467-018-02928-3. It would be very useful to demonstrate via invasive neurophysiological recordings that the parameters used in the current study do indeed lead to any kind of change in brain activity. Of course, this particular study uses a different non-invasive stimulation protocol.

Thank you for raising the important issue regarding the actual neurophysiological effects of non-invasive brain stimulation. Unfortunately, invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints, while studies on cadavers or rodents would not fully resolve our question. Indeed, the authors of the cited study (Mihály Vöröslakos et al., Nature Communications, 2018) highlight the impossibility of drawing definitive conclusions about the exact voltage required in the in-vivo human brain due to significant differences between rats and humans, as well as the in-vivo human brain and cadavers due to alterations in electrical conductivity that occur in postmortem tissue. Huang and colleagues addressed the difficulties in reaching direct evidence of non-invasive brain stimulation (NIBS) effects in a review published in Clinical Neurophysiology in 2017. They conclude that the use of EEG to assess brain response to TMS has great potential for a less indirect demonstration of plasticity mechanisms induced by NIBS in humans.

To address this challenge, we conducted Experiments 3 and 4, which respectively examined the neurophysiological and connectivity changes induced by the stimulation in a non-invasive manner using TMS-EEG and fMRI. The observed changes in brain oscillatory activity (increased gamma oscillatory activity), cortical excitability (enhanced posteromedial parietal cortex reactivity), and brain connectivity (strengthened connections between the precuneus and hippocampi) provided evidence of the effects of our non-invasive brain stimulation protocol, further supporting the behavioral data.

Additionally, we carefully considered the issue of stimulation distribution and, in response, performed a biophysical modeling analysis and E-field calculation using the parameters employed in our study (see Supplementary Materials).

We acknowledge that further exploration of this aspect would be highly valuable, and we agree that it is worth discussing both as a technical limitation and as a potential direction for future research. We therefore, modify the discussion accordingly (main text, lines 280-289).

“Although we studied TMS and tACS propagation through the E-field modeling and observed an increase in the precuneus gamma oscillatory activity, excitability and connectivity with the hippocampi, we cannot exclude that our results might reflect the consequences of stimulating more superficial parietal regions other than the precuneus nor report direct evidence of microscopic changes in the brain after the stimulation. Invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints. Studies on cadavers or rodents would not fully resolve our question due to significant differences between them (i.e. rodents do not have an anatomical correspondence while cadavers have an alterations in electrical conductivity occurring in postmortem tissue). However, further exploration of this aspect in future studies would help in the understanding of γtACS+iTBS effects.”

(2) If there is any brain activity triggered by the current stimulation parameters, then it is extremely difficult to understand how this activity can lead to enhancing memory. The brain is complex. There are hundreds of neuronal types. Each neuron receives precise input from about 10,000 other neurons with highly tuned synaptic strengths. Let us assume that the current protocol does lead to enhancing (or inhibiting) simultaneously the activity of millions of neurons. It is unclear whether there is any activity at all in the brain triggered by this protocol, it is also unclear whether such activity would be excitatory, or inhibitory. It is also unclear how many neurons, let alone what types of neurons would change their activity. How is it possible that this can lead to memory enhancement? This seems like using a hammer to knock on my laptop and hope that the laptop will output a new Mozart-like sonata.

Thank you for your comment. As you correctly point out, we still do not have precise knowledge of which neurons—and to what extent—are activated during non-invasive brain stimulation in humans. However, this challenge is not limited to brain stimulation but applies to many other therapeutic interventions, including psychiatric medications, without limiting their use.

Nevertheless, a substantial body of research has investigated the mechanisms underlying the efficacy of TMS and tACS in producing behavioral after-effects, primarily through its ability to induce long-term potentiation (Bliss & Collingridge, The Journal of Physiology, 1993a; Ridding & Rothwell, Nature Reviews Neuroscience, 2007; Huang et al., Clinical Neurophysiology, 2017; Koch et al., Neuroimage 2018; Koch et al., Brain 2022; Jannati et al., Neuropsychopharmacology, 2023; Wischnewski et al., Trends in Cognitive Science, 2023; Griffiths et al., Trends in Neuroscience, 2023).

We acknowledge that we took this important aspect for granted. We consequently expanded the introduction accordingly (main text, lines 48-60).

“Repetitive transcranial magnetic stimulation (rTMS) and transcranial alternating current stimulation (tACS) are two forms of NIBS widely used to enhance memory performances (Grover et al., 2022; Koch et al., 2018; Wang et al., 2014). rTMS, based on the principle of Faraday, induces depolarization of cortical neuronal assemblies and leads to after-effects that have been linked to changes in synaptic plasticity involving mechanisms of long-term potentiation (LTP) (Huang et al., 2017; Jannati et al., 2023). On the other hand, tACS causes rhythmic fluctuations in neuronal membrane potentials, which can bias spike timing, leading to an entrainment of the neural activity (Wischnewski et al., 2023). In particular, the induction of gamma oscillatory a has been proposed to play an important role in a type of LTP known as spike timing-dependent plasticity, which depends on a precise temporal delay between the firing of a presynaptic and a postsynaptic neuron (Griffiths and Jensen, 2023). Both LTP and gamma oscillations have a strong link with memory processes such as encoding (Bliss and Collingridge, 1993; Griffiths and Jensen, 2023; Rossi et al., 2001), pointing to rTMS and tACS as good candidates for memory enhancement.”

(3) Even if there is any kind of brain activation, it is unclear why the authors seem to be so sure that the precuneus is responsible. Are there neurophysiological data demonstrating that the current protocol only activates neurons in the precuneus? Of note, the non-invasive measurements shown in Figure 3 are very weak (Figure 3A top and bottom look very similar, and Figure 3C left and right look almost identical). Even if one were to accept the weak alleged differences in Figure 3, there is no indication in this figure that there is anything specific to the precuneus, rather a whole brain pattern. This would be the kind of minimally rigorous type of evidence required to make such claims. In a less convincing fashion, one could look at different positions of the stimulation apparatus. This would not be particularly compelling in terms of making a statement about the precuneus. But at least it would show that the position does matter, and over what range of distances it matters, if it matters.

Thank you for your feedback. Our assumption that the precuneus plays a key role in the observed effects is based on several factors:

(1) The non-invasive stimulation protocol was applied to an individually identified precuneus for each participant. Given existing evidence on TMS propagation, we can reasonably assume that the precuneus was at least a mediator of the observed effects (Ridding & Rothwell, Nature Reviews Neuroscience 2007). For further details about target identification and TMS and tACS propagation, please refer to the MRI data acquisition section in the main text and Biophysical modeling and E-field calculation section in the supplementary materials.

(2) To investigate the effects of the neuromodulation protocol on cortical responses, we conducted a whole-brain analysis using multiple paired t-tests comparing each data point between different experimental conditions. To minimize the type I error rate, data were permuted with the Monte Carlo approach and significant p-values were corrected with the false discovery rate method (see the Methods section for details). The results identified the posterior-medial parietal areas as the only regions showing significant differences across conditions.

(3) To control for potential generalized effects, we included a control condition in which TMS-EEG recordings were performed over the left parietal cortex (adjacent to the precuneus). This condition did not yield any significant results, reinforcing the cortical specificity of the observed effects.

However, as stated in the Discussion, we do not claim that precuneus activity alone accounts for the observed effects. As shown in Experiment 4, stimulation led to connectivity changes between the precuneus and hippocampus, a network widely recognized as a key contributor to long-term memory formation (Bliss & Collingridge, Nature 1993). These connectivity changes suggest that precuneus stimulation triggered a ripple effect extending beyond the stimulation site, engaging the broader precuneus-hippocampus network.

Regarding Figure 3A, it represents the overall expression of oscillatory activity detected by TMS-EEG. Since each frequency band has a different optimal scaling, the figure reflects a graphical compromise. A more detailed representation of the significant results is provided in Figure 3B. The effect sizes for gamma oscillatory activity in the delta T1 and T2 conditions were 0.52 and 0.50, respectively, which correspond to a medium effect based on Cohen’s d interpretation.

We add a paragraph in the discussion to improve the clarity of the manuscript regarding this important aspect (lines 193-198).

“Given the existing evidence on TMS propagation and the computation of the Biophysical model with the Efield, we can reasonably assume that the individually identified PC was a mediator of the observed effects (Ridding and Rothwell, 2007). Moreover, we observed specific cortical changes in the posteromedial parietal areas, as evidenced by the whole-brain analysis conducted on TMS-EEG data and the absence of effect on the lateral posterior parietal cortex used as a control condition.”

(4) In the absence of any neurophysiological documentation of a direct impact on the brain, an argument in this type of study is that the behavioral results show that there must be some kind of effect. I agree with this argument. This is also the argument for placebo effects, which can be extremely powerful and useful even if the mechanism is unrelated to what is studied. Then let us dig into the behavioral results.

Hoping to have already addressed your concern regarding the neurophysiological impact of the stimulation on the brain, we would like to emphasize that the behavioral results were obtained controlling for placebo effects. This was achieved by having participants perform the task under different stimulation conditions, including a sham condition.

4a. There does not seem to be any effect on the STMB task, therefore we can ignore this.

4b. The FNAT task is minimally described in the supplementary material. There are no experimental details to understand what was done. What was the size of the images? How long were the images presented for? Were there any repetitions of the images? For how long did the participants study the images? Presumably, all the names and occupations are different? What were the genders of the faces? What is chance level performance? Presumably, the same participant saw different faces across the different stimulation conditions. If not, then there can be memory effects across different conditions that are even more complex to study. If yes, then it would be useful to show that the difficulty is the same across the different stimuli.

We thank you for signaling the lack in the description of FNAT task. We added the information required in the supplementary information (lines 93-101).

“Each picture's face size was 19x15cm. In the learning phase, faces were shown along with names and occupations for 8 seconds each (totaling approximately 2 minutes). During immediate recall, the faces were displayed alone for 8 seconds. In the delayed recall and recognition phase, pictures were presented until the subject provided answers. We used a different set of stimuli for each stimulation condition, resulting in a total of 3 parallel task forms balanced across conditions and session order. All parallel forms comprised 6 male and 6 female faces; for each sex, there were 2 young adults (around 30 years old), 2 middle-aged adults (around 50 years old), and 2 elderly adults (around 70 years old). Before the experiments, we conducted a pilot study to ensure no differences existed between the parallel forms of the task.”

The chance level in the immediate and delayed recall is not quantifiable since the participants had to freely recall the name and the occupation without a multiple choice. In the recognition, the chance level was around 33% (since the possible answers were 3).

4c. Although not stated clearly, if I understand FNAT correctly, the task is based on just 12 presentations. Each point in Figure 2A represents a different participant. Unfortunately, there is no way of linking the performance of individual participants across the conditions with the information provided. Lines joining performance for each participant would be useful in this regard. Because there are only 12 faces, the results are quantized in multiples of 100/12 % in Figure 3A. While I do not doubt that the authors did their homework in terms of the statistical analyses, it is difficult to get too excited about these 12 measurements. For example, take Figure 3A immediate condition TOTAL, arguably the largest effect in the whole paper. It seems that on average, the participants may remember one more face/name/occupation.

Thank you for the suggestion. We added graphs showing lines linking the performance of individual participants across conditions to improve clarity, please see Fig.2 revised. We apologize for the lack of clarity in the description of the FNAT. As you correctly pointed out, we used the percentage based on the single association between face, name and occupation (12 in total). However, each association consisted of three items, resulting in a total of 36 items to learn and associate – we added a paragraph to make it more explicit in the manuscript (lines 425-430).

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

In the example you mentioned, participants were, on average, able to correctly recall and associate three more items compared to the other conditions. While this difference may not seem striking at first glance, it is important to consider that we assessed memory performance after a single, three-minute stimulation session. Similar effects are typically observed only after multiple stimulation sessions (Koch et al., NeuroImage, 2018; Grover et al., Nature Neuroscience, 2022). Moreover, memory performance changes are often measured by a limited set of stimuli due to methodological constraints related to memory capacity. For example, Rey Auditory Verbal learning task, requiring to learn and recall 15 words, is a typical test used to detect memory changes (Koch et al., Neuroimage, 2018; Benussi et al., Brain stimulation 2021; Benussi et al., Annals of Neurology, 2022). 

4d. Block effects. If I understand correctly, the experiments were conducted in blocks. This is always problematic. Here is one example study that articulated the big problems in block designs (Li et al TPAMI 2021):https://ieeexplore.ieee.org/document/9264220

Thank you for the interesting reference. According to this paper, in a block design, EEG or fMRI recordings are performed in response to different stimuli of a given class presented in succession. If this is the case, it does not correspond to our experimental design where both TMS-EEG and fMRI were conducted in resting state on different days according to the different stimulation conditions.

4e. Even if we ignore the lack of experimental descriptions, problems with lack of evidence of brain activity, the minimalistic study of 12 faces, problems with the block design, etc. at the end of the day, the results are extremely weak. In FNAT, some results are statistically significant, some are not. The interpretation of all of this is extremely complex. Continuing with Figure 3A, it seems that the author claims that iTBS+gtACS > iTBS+sham-tACS, but iTBS+gtACS ~ sham+sham. I am struggling to interpret such a result. When separating results by name and occupation, the results are even more perplexing. There is only one condition that is statistically significant in Figure 3A NAME and none in the occupation condition.

Thank you again for your feedback. Hoping to have thoroughly addressed your initial concerns in our previous responses, we now move on to your observations regarding the behavioral results, assuming you were referring to Figure 2A. The main finding of this study is the improvement in long-term memory performance, specifically the ability to correctly recall the association between face, name, and occupation (total FNAT), which was significantly enhanced in both Experiments 1 and 2. However, we also aimed to explore the individual contributions of name and occupation separately to gain a deeper understanding of the results. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall. We understand that this may have caused some confusion. We consequently modified the manuscript in the (lines 97-99; 107-111; 425-430) to make it clearer and moved the graph relative to FNAT NAME and OCCUPATION from fig.2 in the main text to fig. S4 in supplementary information.

“Dual iTBS+γtACS increased the performances in recalling the association between face, name and occupation (FNAT accuracy) both for the immediate (F_2,38=7.18; p =0.002; η²_p=0.274) and the delayed (F_2,38=5.86; p =0.006; η²_p=0.236) recall performances (Fig. 2, panel A).”

“The in-depth analysis of the FNAT accuracy investigating the specific contribution of face-name and face-occupation recall reveald that dual iTBS+γtACS increased the performances in the association between face and name (FNAT NAME) delayed recall (F_2,38 =3.46; p =0.042; η²p =0.154; iTBS+γtACS vs. sham-iTBS+sham-tACS: 42.9±21.5 % vs. 33.8±19 %; p=0.048 Bonferroni corrected) (Fig. S4, supplementary information).”

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

Regarding the stimulation conditions, your concerns about the performance pattern (iTBS+gtACS > iTBS+sham-tACS, but iTBS+gtACS ~ sham+sham) are understandable. However, this new protocol was developed precisely in response to the variability observed in behavioral outcomes following non-invasive brain stimulation, particularly when used to modulate memory functions (Corp et al., 2020; Pabst et al., 2022). As discussed in the manuscript, it is intended as a boost to conventional non-invasive brain stimulation protocols, leveraging the mechanisms outlined in the Discussion section.

(5) In sum, it would be amazing to be able to use non-invasive stimulation for any kind of therapeutic purpose as the authors imagine. More work needs to be done to convince ourselves that this kind of approach is viable. The evidence provided in this study is weak.

We hope our response will be carefully considered, fostering a constructive exchange and leading to a reassessment of your evaluation.

Reviewer #2 (Public review):

Summary:

The manuscript "Dual transcranial electromagnetic stimulation of the precuneus-hippocampus network boosts human long-term memory" by Borghi and colleagues provides evidence that the combination of intermittent theta burst TMS stimulation and gamma transcranial alternating current stimulation (γtACS) targeting the precuneus increases long-term associative memory in healthy subjects compared to iTBS alone and sham conditions. Using a rich dataset of TMS-EEG and resting-state functional connectivity (rs-FC) maps and structural MRI data, the authors also provide evidence that dual stimulation increased gamma oscillations and functional connectivity between the precuneus and hippocampus. Enhanced memory performance was linked to increased gamma oscillatory activity and connectivity through white matter tracts.

Strengths:

The combination of personalized repetitive TMS (iTBS) and gamma tACS is a novel approach to targeting the precuneus, and thereby, connected memory-related regions to enhance long-term associative memory. The authors leverage an existing neural mechanism engaged in memory binding, theta-gamma coupling, by applying TMS at theta burst patterns and tACS at gamma frequencies to enhance gamma oscillations. The authors conducted a thorough study that suggests that simultaneous iTBS and gamma tACS could be a powerful approach for enhancing long-term associative memory. The paper was well-written, clear, and concise.

Weaknesses:

(1) The study did not include a condition where γtACS was applied alone. This was likely because a previous work indicated that a single 3-minute γtACS did not produce significant effects, but this limits the ability to isolate the specific contribution of γtACS in the context of this target and memory function

Thank you for your comments. As you pointed out, we did not include a condition where γtACS was applied alone. This decision was based on the findings of Guerra et al. (Brain Stimulation 2018), who investigated the same protocol and reported no aftereffects. Given the substantial burden of the experimental design on patients and our primary goal of demonstrating an enhancement of effects compared to the standalone iTBS protocol, we decided to leave out this condition. However, you raise an important aspect that should be further discussed, we modified the limitation section accordingly (lines 290-297).

“We did not assess the effects of γtACS alone. This decision was based on the findings of Guerra et al. (Guerra et al., 2018), who investigated the same protocol and reported no aftereffects. Given the substantial burden of the experimental design on patients and our primary goal of demonstrating an enhancement of effects compared to the standalone iTBS protocol, we decided to leave out this condition. While examining the effects of γtACS alone could help isolate its specific contribution to this target and memory function, extensive research has shown that achieving a cognitive enhancement aftereffect with tACS alone typically requires around 20–25 minutes of stimulation (Grover et al., 2023).”

(2) The authors applied stimulation for 3 minutes, which seems to be based on prior tACS protocols. It would be helpful to present some rationale for both the duration and timing relative to the learning phase of the memory task. Would you expect additional stimulation prior to recall to benefit long-term associative memory?

Thank you for your comment and for raising this interesting point. As you correctly noted, the protocol we used has a duration of three minutes, a choice based on previous studies demonstrating its greater efficacy with respect to single stimulation from a neurophysiological point of view. Specifically, these studies have shown that the combined stimulation enhanced gamma-band oscillations and increased cortical plasticity (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Given that the precuneus (Brodt et al., Science 2018; Schott et al., Human Brain Mapping 2018), gamma oscillations (Osipova et al., Journal of Neuroscience 2006; Deprés et al., Neurobiology of Aging 2017; Griffiths et al., Trends in Neurosciences 2023), and cortical plasticity (Brodt et al., Science 2018) are all associated with memory formation and encoding processes, we decided to apply the co-stimulation immediately before it to enhance the efficacy. We added this paragraph to the manuscript rationale (lines 48-60).

“Repetitive transcranial magnetic stimulation (rTMS) and transcranial alternating current stimulation (tACS) are two forms of NIBS widely used to enhance memory performances (Grover et al., 2022; Koch et al., 2018; Wang et al., 2014). rTMS, based on the principle of Faraday, induces depolarization of cortical neuronal assemblies and leads to after-effects that have been linked to changes in synaptic plasticity involving mechanisms of long-term potentiation (LTP) (Huang et al., 2017; Jannati et al., 2023). On the other hand, tACS causes rhythmic fluctuations in neuronal membrane potentials, which can bias spike timing, leading to an entrainment of the neural activity (Wischnewski et al., 2023). In particular, the induction of gamma oscillatory a has been proposed to play an important role in a type of LTP known as spike timing-dependent plasticity, which depends on a precise temporal delay between the firing of a presynaptic and a postsynaptic neuron (Griffiths and Jensen, 2023). Both LTP and gamma oscillations have a strong link with memory processes such as encoding (Bliss and Collingridge, 1993; Griffiths and Jensen, 2023; Rossi et al., 2001), pointing to rTMS and tACS as good candidates for memory enhancement.”

Regarding the question of whether stimulation could also benefit recall, the answer is yes. We can speculate that repeating the stimulation before recall might provide an additional boost. This is supported by evidence showing that both the precuneus and gamma oscillations are involved in recall processes (Flanagin et al., Cerebral Cortex 2023; Griffiths et al., Trends in Neurosciences 2023). Furthermore, previous research suggests that reinstating the same brain state as during encoding can enhance recall performance (Javadi et al., The Journal of Neuroscience 2017). We added this consideration to the discussion (lines 305-311).

“Future studies should further investigate the effects of stimulation on distinct memory processes. In particular, stimulation could be applied before retrieval (Rossi et al., 2001), to better elucidate its specific contribution to the observed enhancements in memory performance. Additionally, it would be worth examining whether repeated stimulation - administered both before encoding and before retrieval - could produce a boosting effect. This is especially relevant in light of findings showing that matching the brain state between retrieval and encoding can significantly enhance memory performance (Javadi et al., 2017).”

(3) How was the burst frequency of theta iTBS and gamma frequency of tACS chosen? Were these also personalized to subjects' endogenous theta and gamma oscillations? If not, were increases in gamma oscillations specific to patients' endogenous gamma oscillation frequencies or the tACS frequency?

The stimulation protocol was chosen based on previous studies (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022).  Gamma tACS sinusoid frequency wave was set at 70 Hz while iTBS consisted of ten bursts of three pulses at 50 Hz lasting 2 s, repeated every 10 s with an 8 s pause between consecutive trains, for a total of 600 pulses total lasting 190 s (see iTBS+γtACS neuromodulation protocol section). In particular, the theta iTBS has been inspired by protocols used in animal models to elicit LTP in the hippocampus (Huang et al., Neuron 2005). Consequently, neither Theta iTBS nor the gamma frequency of tACS were personalized. The increase in gamma oscillations was referred to the patient’s baseline and did not correspond to the administrated tACS frequency.

(4) The authors do a thorough job of analyzing the increase in gamma oscillations in the precuneus through TMS-EEG; however, the authors may also analyze whether theta oscillations were also enhanced through this protocol due to the iTBS potentially targeting theta oscillations. This may also be more robust than gamma oscillations increases since gamma oscillations detected on the scalp are very low amplitude and susceptible to noise and may reflect activity from multiple overlapping sources, making precise localization difficult without advanced techniques.

Thank you for the suggestion. We analyzed theta oscillations, finding no changes.

(5) Figure 4: Why are connectivity values pre-stimulation for the iTBS and sham tACS stimulation condition so much higher than the dual stimulation? We would expect baseline values to be more similar.

We acknowledge that the pre-stimulation connectivity values for the iTBS and sham tACS conditions appear higher than those for the dual stimulation condition. However, as noted in our statistical analyses, there were no significant differences at baseline between conditions (p-FDR= 0.3514), suggesting that any apparent discrepancy is due to natural variability rather than systematic bias. One potential explanation for these differences is individual variability in baseline connectivity measures, which can fluctuate due to factors such as intrinsic neural dynamics, participant state, or measurement noise. Despite these variations, our statistical approach ensures that any observed post-stimulation effects are not confounded by pre-existing differences.

(6) Figure 2: How are total association scores significantly different between stimulation conditions, but individual name and occupation associations are not? Further clarification of how the total FNAT score is calculated would be helpful.

We apologize for any lack of clarity. The total FNAT score reflects the ability to correctly recall all the information associated with a person—specifically, the correct pairing of the face, name, and occupation. Participants received one point for each triplet they accurately recalled. The scores were then converted into percentages, as detailed in the Face-Name Associative Task Construction and Scoring section in the supplementary materials.

Total FNAT was the primary outcome measure. However, we also analyzed name and occupation recall separately to better understand their partial contributions. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall.

We acknowledge that this distinction may have caused some confusion. To improve clarity, we revised the manuscript accordingly (lines 97-98; 107-111; 425-430).

“Dual iTBS+γtACS increased the performances in recalling the association between face, name and occupation (FNAT accuracy) both for the immediate (F_2,38=7.18 ;p=0.002; η²_p=0.274) and the delayed (F_2,38=5.86;p=0.006; η²_p=0.236) recall performances (Fig. 2, panel A).”

“The in-depth analysis of the FNAT accuracy investigating the specific contribution of face-name and face-occupation recall revealed that dual iTBS+γtACS increased the performances in the association between face and name (FNAT NAME) delayed recall (F_2,38 =3.46; p =0.042; η²p =0.154; iTBS+γtACS vs. sham-iTBS+sham-tACS: 42.9±21.5 % vs. 33.8±19 %; p=0.048 Bonferroni corrected) (Fig. S4, supplementary information).”

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

We also moved the data regarding the specific contribution of name and occupation recall in the supplementary information (fig.S4) and further specified how we computed the score in the score (lines 102-104).

“The score was computed by deriving an accuracy percentage index dividing by 12 and multiplying by 100 the correct association sum. The partial recall scores were computed in the same way only considering the sum of face-name (NAME) and face-occupation (OCCUPATION) correctly recollected.”

Reviewer #3 (Public review):

Summary:

Borghi and colleagues present results from 4 experiments aimed at investigating the effects of dual γtACS and iTBS stimulation of the precuneus on behavioral and neural markers of memory formation. In their first experiment (n = 20), they found that a 3-minute offline (i.e., prior to task completion) stimulation that combines both techniques leads to superior memory recall performance in an associative memory task immediately after learning associations between pictures of faces, names, and occupation, as well as after a 15-minute delay, compared to iTBS alone (+ tACS sham) or no stimulation (sham for both iTBS and tACS). Performance in a second task probing short-term memory was unaffected by the stimulation condition. In a second experiment (n = 10), they show that these effects persist over 24 hours and up to a full week after initial stimulation. A third (n = 14) and fourth (n = 16) experiment were conducted to investigate the neural effects of the stimulation protocol. The authors report that, once again, only combined iTBS and γtACS increase gamma oscillatory activity and neural excitability (as measured by concurrent TMS-EEG) specific to the stimulated area at the precuneus compared to a control region, as well as precuneus-hippocampus functional connectivity (measured by resting-state MRI), which seemed to be associated with structural white matter integrity of the bilateral middle longitudinal fasciculus (measured by DTI).

Strengths:

Combining non-invasive brain stimulation techniques is a novel, potentially very powerful method to maximize the effects of these kinds of interventions that are usually well-tolerated and thus accepted by patients and healthy participants. It is also very impressive that the stimulation-induced improvements in memory performance resulted from a short (3 min) intervention protocol. If the effects reported here turn out to be as clinically meaningful and generalizable across populations as implied, this approach could represent a promising avenue for the treatment of impaired memory functions in many conditions.

Methodologically, this study is expertly done! I don't see any serious issues with the technical setup in any of the experiments (with the only caveat that I am not an expert in fMRI functional connectivity measures and DTI). It is also very commendable that the authors conceptually replicated the behavioral effects of experiment 1 in experiment 2 and then conducted two additional experiments to probe the neural mechanisms associated with these effects. This certainly increases the value of the study and the confidence in the results considerably.

The authors used a within-subject approach in their experiments, which increases statistical power and allows for stronger inferences about the tested effects. They are also used to individualize stimulation locations and intensities, which should further optimize the signal-to-noise ratio.

Weaknesses:

I want to state clearly that I think the strengths of this study far outweigh the concerns I have. I still list some points that I think should be clarified by the authors or taken into account by readers when interpreting the presented findings.

I think one of the major weaknesses of this study is the overall low sample size in all of the experiments (between n = 10 and n = 20). This is, as I mentioned when discussing the strengths of the study, partly mitigated by the within-subject design and individualized stimulation parameters. The authors mention that they performed a power analysis but this analysis seemed to be based on electrophysiological readouts similar to those obtained in experiment 3. It is thus unclear whether the other experiments were sufficiently powered to reliably detect the behavioral effects of interest. That being said, the authors do report significant effects, so they were per definition powered to find those. However, the effect sizes reported for their main findings are all relatively large and it is known that significant findings from small samples may represent inflated effect sizes, which may hamper the generalizability of the current results. Ideally, the authors would replicate their main findings in a larger sample. Alternatively, I think running a sensitivity analysis to estimate the smallest effect the authors could have detected with a power of 80% could be very informative for readers to contextualize the findings. At the very least, however, I think it would be necessary to address this point as a potential limitation in the discussion of the paper.

Thank you for the observation. As you mentioned, our power analysis was based on our previous study investigating the same neuromodulation protocol with a corresponding experimental design. The relatively small sample could be considered a possible limitation of the study which we will add to the discussion. A fundamental future step will be to replay these results on a larger population, however, to strengthen our results we performed the sensitivity analysis you suggested.

In detail, we performed a sensitivity analysis for repeated-measures ANOVA with α=0.05 and power(1-β)=0.80 with no sphericity correction. For experiment 1, a sensitivity analysis with 1 group and 3 measurements showed a minimal detectable effect size of f=0.524 with 20 participants. In our paper, the ANOVA on total FNAT immediate performance revealed an effect size of η²=0.274 corresponding to f=0.614; the ANOVA on FNAT delayed performance revealed an effect size of η²=0.236 corresponding to f=0.556. For experiment 2, a sensitivity analysis for total FNAT immediate performance (1 group and 3 measurements) showed a minimal detectable effect size of f=0.797 with 10 participants. In our paper, the ANOVA on total FNAT immediate performance revealed an effect size of η²=0.448 corresponding to f=0.901. The sensitivity analysis for total FNAT delayed performance (1 group and 6 measurements) showed a minimal detectable effect size of f=0.378 with 10 participants. In our paper, the ANOVA on total FNAT delayed performance revealed an effect size of η²=0.484 corresponding to f=0.968. Thus, the sensitivity analysis showed that both experiments were powered enough to detect the minimum effect size computed in the power analysis. We have now added this information to the manuscript and we thank the reviewer for her/his suggestion in the statistical analysis and results section (lines 99-100; 127-128; 130-131; 543-545).

“The sensitivity analysis showed a minimal detectable effect size of  η²=0.215 with 20 participants.”

“The sensitivity analysis showed a minimal detectable effect size of  η²=0.388 with 10 participants.”

“The sensitivity analysis showed a minimal detectable effect size of η²=0.125 with 10 participants.”

“Since we do not have an a priori effect size for experiment 1 and 2, we performed a sensitivity power analysis to ensure that these experiments were able to detect the minimum effect size with 80% power and alpha level of 0.05.”

It seems that the statistical analysis approach differed slightly between studies. In experiment 1, the authors followed up significant effects of their ANOVAs by Bonferroni-adjusted post-hoc tests whereas it seems that in experiment 2, those post-hoc tests where "exploratory", which may suggest those were uncorrected. In experiment 3, the authors use one-tailed t-tests to follow up their ANOVAs. Given some of the reported p-values, these choices suggest that some of the comparisons might have failed to reach significance if properly corrected. This is not a critical issue per se, as the important test in all these cases is the initial ANOVA but non-significant (corrected) post-hoc tests might be another indicator of an underpowered experiment. My assumptions here might be wrong, but even then, I would ask the authors to be more transparent about the reasons for their choices or provide additional justification. Finally, the authors sometimes report exact p-values whereas other times they simply say p < .05. I would ask them to be consistent and recommend using exact p-values for every result where p >= .001.

Thank you again for the suggestions. Your observations are correct, we used a slightly different statistical depending on our hypothesis. Here are the details:

In experiment 1, we used a repeated-measure ANOVA with one factor “stimulation condition” (iTBS+γtACS; iTBS+sham-tACS; sham-iTBS+sham-tACS). Following the significant effect of this factor we performed post-hoc analysis with Bonferroni correction.

In experiment 2, we used a repeated-measures with two factors “stimulation condition” and “time”. As expected, we observed a significant effect of condition, confirming the result of experiment 1, but not of time. Thus, this means that the neuromodulatory effect was present regardless of the time point. However, to explore whether the effects of stimulation condition were present in each time point we performed some explorative t-tests with no correction for multiple comparisons since this was just an explorative analysis.

In experiment 3, we used the same approach as experiment 1. However, since we had a specific hypothesis on the direction of the effect already observed in our previous study, i.e. increase in spectral power (Maiella et al., Scientific Report 2022), our tests were 1-tailed.

For the p-values, we corrected the manuscript reporting the exact values for every result.

While the authors went to great lengths trying to probe the neural changes likely associated with the memory improvement after stimulation, it is impossible from their data to causally relate the findings from experiments 3 and 4 to the behavioral effects in experiments 1 and 2. This is acknowledged by the authors and there are good methodological reasons for why TMS-EEG and fMRI had to be collected in sperate experiments, but it is still worth pointing out to readers that this limits inferences about how exactly dual iTBS and γtACS of the precuneus modulate learning and memory.

Thank you for your comment. We fully agree with your observation, which is why this aspect has been considered in the study's limitations. To address your concern, we add this sentence to the limitation discussion (lines 299-301).

“Consequently, these findings do not allow precise inferences regarding the specific mechanisms by which dual iTBS and γtACS of the precuneus modulate learning and memory.”

There were no stimulation-related performance differences in the short-term memory task used in experiments 1 and 2. The authors argue that this demonstrates that the intervention specifically targeted long-term associative memory formation. While this is certainly possible, the STM task was a spatial memory task, whereas the LTM task relied (primarily) on verbal material. It is thus also possible that the stimulation effects were specific to a stimulus domain instead of memory type. In other words, could it be possible that the stimulation might have affected STM performance if the task taxed verbal STM instead? This is of course impossible to know without an additional experiment, but the authors could mention this possibility when discussing their findings regarding the lack of change in the STM task.

Thank you for your interesting observation. We argue that the intervention primarily targeted long-term associative memory formation, as our findings demonstrated effects only on FNAT. However, as you correctly pointed out, we cannot exclude the possibility that the stimulation may also influence short-term verbal associative memory. We add this aspect when discussing the absence of significant findings in the STM task (lines 205-210).

“Visual short-term associative memory, measured by STBM performance, was not modulated by any experimental condition. Even if we cannot exclude the possibility that the stimulation could have influenced short-term verbal associative memory, we expected this result since short-term associative memory is known to rely on a distinct frontoparietal network while FNAT, used to investigate long-term associative memory, has already been associated with the neural activity of the PC and the hippocampus (Parra et al., 2014; Rentz et al., 2011).”

While the authors discuss the potential neural mechanisms by which the combined stimulation conditions might have helped memory formation, the psychological processes are somewhat neglected. For example, do the authors think the stimulation primarily improves the encoding of new information or does it also improve consolidation processes? Interestingly, the beneficial effect of dual iTBS and γtACS on recall performance was very stable across all time points tested in experiments 1 and 2, as was the performance in the other conditions. Do the authors have any explanation as to why there seems to be no further forgetting of information over time in either condition when even at immediate recall, accuracy is below 50%? Further, participants started learning the associations of the FNAT immediately after the stimulation protocol was administered. What would happen if learning started with a delay? In other words, do the authors think there is an ideal time window post-stimulation in which memory formation is enhanced? If so, this might limit the usability of this procedure in real-life applications.

Thank you for your comment and for raising these important points.

We hypothesized that co-stimulation would enhance encoding processes. Previous studies have shown that co-stimulation can enhance gamma-band oscillations and increase cortical plasticity (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Given that the precuneus (Brodt et al., Science 2018; Schott et al., Human Brain Mapping 2018), gamma oscillations (Osipova et al., Journal of Neuroscience 2006; Deprés et al., Neurobiology of Aging 2017; Griffiths et al., Trends in Neurosciences 2023), and cortical plasticity (Brodt et al., Science 2018) have all been associated with encoding processes, we decided to apply co-stimulation before the encoding phase, to boost it. We enlarged the introduction to specify the link between neural mechanisms and the psychological process of the encoding (lines 55-60).

“In particular, the induction of gamma oscillatory activity has been proposed to play an important role in a type of LTP known as spike timing-dependent plasticity, which depends on a precise temporal delay between the firing of a presynaptic and a postsynaptic neuron (Griffiths and Jensen, 2023). Both LTP and gamma oscillations have a strong link with memory processes such as encoding (Bliss and Collingridge, 1993; Griffiths and Jensen, 2023; Rossi et al., 2001), pointing to rTMS and tACS as good candidates for memory enhancement.”

We applied the co-stimulation immediately before the learning phase to maximize its potential effects. While we observed a significant increase in gamma oscillatory activity lasting up to 20 minutes, we cannot determine whether the behavioral effects we observed would have been the same with a co-stimulation applied 20 minutes before learning. Based on existing literature, a reduction in the efficacy of co-stimulation over time could be expected (Huang et al., Neuron 2005; Thut et al., Brain Topography 2009). However, we hypothesize that multiple stimulation sessions might provide an additional boost, helping to sustain the effects over time (Thut et al., Brain Topography 2009; Koch et al., Neuroimage 2018; Koch et al., Brain 2022).

Regarding the absence of further forgetting in both stimulation conditions, we think that the clinical and demographical characteristics of the sample (i.e. young and healthy subjects) explain the almost absence of forgetting after one week.

Reviewer #1 (Recommendations for the authors):

To address the concerns, the authors should:

(1) Include invasive neuronal recordings (e.g., in rats or monkeys if not possible in humans) demonstrating that the current stimulation protocol leads to direct changes in brain activity.

We understand the interest of the first reviewer in the understanding of neurophysiological correlates of the stimulation protocol, however, we are skeptical about this request as we think it goes beyond the aims of the study. As already mentioned in the response to the reviewer, invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints. At the same time, studies on cadavers or rodents would not fully resolve the question. Indeed, the authors of the study cited by the reviewer (Mihály Vöröslakos et al., Nature Communications, 2018) highlight the impossibility of drawing definitive conclusions about the exact voltage required in the in-vivo human brain due to significant differences between rats and humans, as well as the in-vivo human cadavers due to alterations in electrical conductivity that occur in postmortem tissue. Huang and colleagues addressed the difficulties in reaching direct evidence of non-invasive brain stimulation (NIBS) effects in a review published in Clinical Neurophysiology in 2017. They conclude that the use of EEG to assess brain response to TMS has a great potential for a less indirect demonstration of plasticity mechanisms induced by NIBS in humans.

It is exactly to meet the need to investigate the changes in brain activity after the stimulation protocol that we conducted Experiments 3 and 4. These experiments respectively examined the neurophysiological and connectivity changes induced by the stimulation in a non-invasive manner using TMS-EEG and fMRI. The observed changes in brain oscillatory activity (increased gamma oscillatory activity), cortical excitability (enhanced posteromedial parietal cortex reactivity), and brain connectivity (strengthened connections between the precuneus and hippocampi) provided evidence of the effects of our non-invasive brain stimulation protocol, further supporting the behavioral data.

Additionally, we carefully considered the issue of stimulation distribution and, in response, performed a biophysical modeling analysis and E-field calculation using the parameters employed in our study (see Supplementary Materials).

Acknowledging the reviewer's point of view, we modified the manuscript accordingly, discussing this aspect both as a technical limitation and as a potential direction for future research (main text, lines 280-289).

“Although we studied TMS and tACS propagation through the E-field modeling and observed an increase in the precuneus gamma oscillatory activity, excitability and connectivity with the hippocampi, we cannot exclude that our results might reflect the consequences of stimulating more superficial parietal regions other than the precuneus nor report direct evidence of microscopic changes in the brain after the stimulation. Invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints. Studies on cadavers or rodents would not fully resolve our question due to significant differences between them (i.e. rodents do not have an anatomical correspondence while cadavers have an alterations in electrical conductivity occurring in postmortem tissue). However, further exploration of this aspect in future studies would help in the understanding of γtACS+iTBS effects.”

(2) Address all the technical questions about the experimental design.

We addressed all the technical questions about the experimental design.

(3) Repeat the experiments with randomized trial order and without a block design.

The experiments were conducted with randomized trial order and we did not use a block design.

(4) Add many more faces to the study. It is extremely difficult to draw any conclusion from merely 12 faces. Ideally, there would be lots of other relevant memory experiments where the authors show compelling positive results.

We understand your perplexity about drawing conclusions from 12 faces, however, this is not the case. As we explained in the response reviewer, the task we implemented did not rely on the recall of merely 12 faces. Instead, participants had to correctly learn, associate and recall 12 faces, 12 names and 12 occupations for a total of 36 items. To improve the clarity of the manuscript, we added a paragraph to make this aspect more explicit (lines 425-430).

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

The behavioral changes we observed are similar to those who are typically observed after multiple stimulation sessions (Koch et al., NeuroImage, 2018; Grover et al., Nature Neuroscience, 2022, Benussi et al., Annals of Neurology, 2022). Moreover, memory performance changes are often measured by a limited set of stimuli due to methodological constraints related to memory capacity. For example, Rey Auditory Verbal learning task, requiring to learn and recall 15 words, is a typical test used to detect memory changes (Koch et al., Neuroimage, 2018; Benussi et al., Brain stimulation 2021; Benussi et al., Annals of Neurology, 2022). 

(5) Provide a clear explanation of the apparent randomness of which results are statistically significant or not in Figure 3. But perhaps with many more experiments, a lot more memory evaluations, many more stimuli, and addressing all the other technical concerns, either the results will disappear or there will be a more interpretable pattern of results.

We provided explanations for all the concerns shown by the reviewer.

Reviewer #2 (Recommendations for the authors):

Minor comments:

(1) Figure 4: Why are connectivity values pre-stimulation for the iTBS and sham tACS stimulation condition so much higher than the dual stimulation? We would expect baseline values to be more similar.

We acknowledge that the pre-stimulation connectivity values for the iTBS and sham tACS conditions appear higher than those for the dual stimulation condition. However, as noted in our statistical analyses, there were no significant differences at baseline between conditions (p-FDR= 0.3514), suggesting that any apparent discrepancy is due to natural variability rather than systematic bias. One potential explanation for these differences is individual variability in baseline connectivity measures, which can fluctuate due to factors such as intrinsic neural dynamics, participant state, or measurement noise. Despite these variations, our statistical approach ensures that any observed post-stimulation effects are not confounded by pre-existing differences.

(2) Figure 2: How are total association scores significantly different between stimulation conditions, but individual name and occupation associations are not? Further clarification of how the total FNAT score is calculated would be helpful.

We apologize for any lack of clarity. The total FNAT score reflects the ability to correctly recall all the information associated with a person—specifically, the correct pairing of the face, name, and occupation. Participants received one point for each triplet they accurately recalled. The scores were then converted into percentages, as detailed in the Face-Name Associative Task Construction and Scoring section in the supplementary materials.

Total FNAT was the primary outcome measure. However, we also analyzed name and occupation recall separately to better understand their partial contributions. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall.

We acknowledge that this distinction may have caused some confusion. To improve clarity, we revised the manuscript accordingly (lines 97-98; 107-111; 425-430).

“Dual iTBS+γtACS increased the performances in recalling the association between face, name and occupation (FNAT accuracy) both for the immediate (F_2,38=7.18; p=0.002; η²_p=0.274) and the delayed (F_2,38=5.86; p =0.006; η²_p=0.236) recall performances (Fig. 2, panel A).”

“The in-depth analysis of the FNAT accuracy investigating the specific contribution of face-name and face-occupation recall revealed that dual iTBS+γtACS increased the performances in the association between face and name (FNAT NAME) delayed recall (F_2,38 =3.46; p =0.042; η²p =0.154; iTBS+γtACS vs. sham-iTBS+sham-tACS: 42.9±21.5 % vs. 33.8±19 %; p=0.048 Bonferroni corrected) (Fig. S4, supplementary information).”

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

We also moved the data regarding the specific contribution of name and occupation recall in the supplementary information (fig.S4) and further specified how we computed the score in the score (lines 102-104).

“The score was computed by deriving an accuracy percentage index dividing by 12 and multiplying by 100 the correct association sum. The partial recall scores were computed in the same way only considering the sum of face-name (NAME) and face-occupation (OCCUPATION) correctly recollected.”

Reviewer #3 (Recommendations for the authors):

A very small detail, in the caption for Figure 2A, OCCUPATION is described as being shown on the 'left' but it should be 'right'.

We corrected this error.

Author response:

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

Reviewer #1 (Public review):

Summary:

Phytophathogens including fungal pathogens such as F. graminearum remain a major threat to agriculture and food security. Several agriculturally relevant fungicides including the potent Quinofumelin have been discovered to date, yet the mechanisms of their action and specific targets within the cell remain unclear. This paper sets out to contribute to addressing these outstanding questions.

We appreciate the reviewer's accurate summary of our manuscript.

Strengths:

The paper is generally well-written and provides convincing data to support their claims for the impact of Quinofumelin on fungal growth, the target of the drug, and the potential mechanism. Critically the authors identify an important pyrimidine pathway dihydroorotate dehydrogenase (DHODH) gene FgDHODHII in the pathway or mechanism of the drug from the prominent plant pathogen F. graminearum, confirming it as the target for Quinofumelin. The evidence is supported by transcriptomic, metabolomic as well as MST, SPR, molecular docking/structural biology analyses.

We appreciate the reviewer's recognition of the strengths of our manuscript.

Weaknesses:

Whilst the study adds to our knowledge about this drug, it is, however, worth stating that previous reports (although in different organisms) by Higashimura et al., 2022 https://pmc.ncbi.nlm.nih.gov/articles/PMC9716045/ had already identified DHODH as the target for Quinofumelin and hence this knowledge is not new and hence the authors may want to tone down the claim that they discovered this mechanism and also give sufficient credit to the previous authors work at the start of the write-up in the introduction section rather than in passing as they did with reference 25? other specific recommendations to improve the text are provided in the recommendations for authors section below.

We appreciate the reviewer's suggestion. In the revised manuscript, we have incorporated the reference in the introduction section and expanded the discussion of previous work on quinofumelin by Higashimura et al., 2022 in the discussion section to more effectively contextualize their contributions. Moreover, we have made revisions and provided responses in accordance with the recommendations.

Reviewer #2 (Public review):

Summary:

In the current study, the authors aim to identify the mode of action/molecular mechanism of characterized a fungicide, quinofumelin, and its biological impact on transcriptomics and metabolomics in Fusarium graminearum and other Fusarium species. Two sets of data were generated between quinofumelin and no treatment group, and differentially abundant transcripts and metabolites were identified. The authors further focused on uridine/uracil biosynthesis pathway, considering the significant up- and down-regulation observed in final metabolites and some of the genes in the pathways. Using a deletion mutant of one of the genes and in vitro biochemical assays, the authors concluded that quinofumelin binds to the dihydroorotate dehydrogenase.

We appreciate the reviewer's accurate summary of our manuscript.

Strengths:

Omics datasets were leveraged to understand the physiological impact of quinofumelin, showing the intracellular impact of the fungicide. The characterization of FgDHODHII deletion strains with supplemented metabolites clearly showed the impact of the enzyme on fungal growth.

We appreciate the reviewer's recognition of the strengths of our manuscript.

Weaknesses:

Some interpretation of results is not accurate and some experiments lack controls. The comparison between quinofumelin-treated deletion strains, in the presence of different metabolites didn't suggest the fungicide is FgDHODHII specific. A wild type is required in this experiment.

Potential Impact: Confirming the target of quinofumelin may help understand its resistance mehchanism, and further development of other inhibitory molecules against the target.

The manuscript would benefit more in explaining the study rationale if more background on previous characterization of this fungicide on Fusarium is given.

We appreciate the reviewer's suggestion. Under no treatment with quinofumelin, mycelial growth remains normal and does not require restoration. In the presence of quinofumelin treatment, the supplementation of downstream metabolites in the de novo pyrimidine biosynthesis pathway can restore mycelial growth that is inhibited by quinofumelin. The wild-type control group is illustrated in Figure 4. Figure 5b depicts the phenotypes of the deletion mutants. With respect to the relationship among quinofumelin, FgDHODHII, and other metabolites, quinofumelin specifically targets the key enzyme FgDHODHII in the de novo pyrimidine biosynthesis pathway, disrupting the conversion of dihydroorotate to orotate, which consequently inhibits the synthesis downstream metabolites including uracil. In our previous study, quinofumelin not only exhibited excellent antifungal activity against the mycelial growth and spore germination of F. graminearum, but also inhibited the biosynthesis of deoxynivalenol (DON). We have added this part to the introduction section.

Reviewer #3 (Public review):

Summary:

The manuscript shows the mechanism of action of quinofumelin, a novel fungicide, against the fungus Fusarium graminearum. Through omics analysis, phenotypic analysis, and in silico approaches, the role of quinofumelin in targeting DHODH is uncovered.

We appreciate the reviewer's accurate summary of our manuscript.

Strengths:

The phenotypic analysis and mutant generation are nice data and add to the role of metabolites in bypassing pyrimidine biosynthesis.

We appreciate the reviewer's recognition of the strengths of our manuscript.

Weaknesses:

The role of DHODH in this class of fungicides has been known and this data does not add any further significance to the field. The work of Higashimura et al is not appreciated well enough as they already showed the role of quinofumelin upon DHODH II.

There is no mention of the other fungicide within this class ipflufenoquin, as there is ample data on this molecule.

We appreciate the reviewer's suggestion. We sincerely appreciate the reviewer's insightful comment regarding the work of Higashimura et al. We agree that their investigation into the role of quinofumelin in DHODH II inhibition provides critical foundational insights for this field. In the revised manuscript, we have incorporated the reference in the introduction section and expanded the discussion of their work in the discussion section to more effectively contextualize their contributions. The information regarding action mechanism of ipflufenoquin against filamentous fungi was added in discussion section.

Reviewer #1 (Recommendations for the authors):

(1) Given that the DHODH gene had been identified as a target earlier, could the authors perform blast experiments with this gene instead and let us know the percentage similarity between the FgDHODHII gene and the Pyricularia oryzae class II DHODH gene in the report by Higashimura et al., 2022.

BLAST experiment revealed that the percentage similarity between the FgDHODHII gene and the class II DHODH gene of P. oryzae was 55.41%. We have added the description ‘Additionally, the amino acid sequence of the FgDHODHII exhibits 55.41% similarity to that of DHODHII from Pyricularia oryzae, as previously reported (Higashimura et al., 2022)’ in section Results.

(2) Abstract:

The authors started abbreviating new terms e.g. DEG, DMP, etc but then all of a sudden stopped and introduced UMP with no full meaning of the abbreviation. Please give the full meaning of all abbreviations in the text, UMP, STC, RM, etc.

We have provided the full meaning for all abbreviations as requested.

(3) Introduction section:

The introduction talks very little about the work of other groups on quinofumelin. Perhaps add this information in and reference them including the work of Higashimura et al., 2022 which has done quite significant work on this topic but is not even mentioned in the background

We have added the work of other groups on quinofumelin in section introduction.

(4) General statements:

Please show a model of the pyrimidine pathway that quinofumelin attacks to make it easier for the reader to understand the context. They could just copy this from KEGG

We have added the model (Fig. 7).

(5) Line 186:

The authors did a great job of demonstrating interactions with the Quinofumelin and went to lengths to perform MST, SPR, molecular docking, and structural biology analyses yet in the end provide no details about the specific amino acid residues involved in the interaction. I would suggest that site-directed mutagenesis studies be performed on FgDHODHII to identify specific amino acid residues that interact with Quinofumelin and show that their disruption weakens Quinofumelin interaction with FgDHODHII.

Thank you for this insightful suggestion. We fully agree with the importance of elucidating the interaction mechanism. At present, we are conducting site-directed mutagenesis studies based on interaction sites from docking results and the mutation sites of FgDHODHII from the resistant mutants; however, due to the limitations in the accuracy of existing predictive models, this work remains ongoing. Additionally, we are undertaking co-crystallization experiments of FgDHODHII with quinofumelin to directly and precisely reveal their interaction pattern

(6) Line 76:

What is the reference or evidence for the statement 'In addition, quinofumelin exhibits no cross-resistance to currently extensively used fungicides, indicating its unique action target against phytopathogenic fungi.

If two fungicides share the same mechanism of action, they will exhibit cross resistance. Previous studies have demonstrated that quinofumelin retains effective antifungal activity against fungal strains resistant to commercial fungicides, indicating that quinofumelin does not exhibit cross-resistance with other commercially available fungicides and possesses a novel mechanism of action. Additionally, we have added the relevant inference.

(7) Line 80-82:

Again, considering the work of previous authors, this target is not newly discovered. Please consider toning down this statement 'This newly discovered selective target for antimicrobial agents provides a valuable resource for the design and development of targeted pesticides.'

We have rewritten the description of this sentence.

(8) Line 138: If the authors have identified DHODH in experimental groups (I assume in F. graminearum), what was the exact locus tag or gene name in F. graminearum, and why not just continue with this gene you identified or what is the point of doing a blast again to find the gene if the DHODH gene if it already came up in your transcriptomic or metabolic studies? This unfortunately doesn't make sense but could be explained better.

The information of FgDHODHII (gene ID: FGSG_09678) has been added. We have revised this part.

Reviewer #2 (Recommendations for the authors):

(1) Line 40:

Please add a reference.

We have added the reference

(2) Line 47:

Please add a reference.

We have added the reference.

(3) Line 50:

The lack of target diversity in existing fungicides doesn't necessarily serve as a reason for discovering new targets being more challenging than identifying new fungicides within existing categories, please consider adjusting the argument here. Instead, the authors can consider reasons for the lack of new targets in the field.

We have revised the description.

(4) Line 63:

Please cite your source with the new technology.

We have added the reference.

(5) Line 68:

What are you referring to for "targeted medicine", do you have a reference?

We have revised the description and the reference.

(6) Line 74:

One of the papers referred to "quinoxyfen", what are the similarities and differences between the two? Please elaborate for the readership.

Quinoxyfen, similar to quinofumelin, contains a quinoline ring structure. It inhibits mycelial growth by disrupting the MAP kinase signaling pathway in fungi (https://www.frac.info). In addition, quinoxyfen still exhibits excellent antifungal activity against the quinofumelin-resistant mutants (the findings from our group), indicating that action mechanism for quinofumelin and quinoxyfen differ.

(7) Line 84:

Please introduce why RNA-Seq was designed in the study first. What were the groups compared? How was the experiment set up? Without this background, it is hard to know why and how you did the experiment.

According to your suggestions, we have added the description in Section Results. In addition, the experimental process was described in Section Materials and methods as follows: A total of 20 mL of YEPD medium containing 1 mL of conidia suspension (1×105 conidia/mL) was incubated with shaking (175 rpm/min) at 25°C. After 24 h, the medium was added with quinofumelin at a concentration of 1 μg/mL, while an equal amount of dimethyl sulfoxide was added as the control (CK). The incubation continued for another 48 h, followed by filtration and collection of hyphae. Carry out quantitative expression of genes, and then analyze the differences between groups based on the results of DESeq2 for quantitative expression.

(8) Figures:

The figure labeling is missing (Figures 1,2,3 etc). Please re-order your figure to match the text

The figures have been inserted.

(9) Line. 97:

"Volcano plot" is a common plot to visualize DEGs, you can directly refer to the name.

We have revised the description.

(10) Figure 1d, 1e:

Can you separate down- and up-regulated genes here? Does the count refer to gene number?

The expression information for down- and up-regulated genes is presented in Figure 1a and 1b. However, these bubble plots do not distinguish down- and up-regulated genes. Instead, they only display the significant enrichment of differentially expressed genes in specific metabolic pathways. To more clearly represent the data, we have added the detailed counts of down- and up-regulated genes for each metabolic pathway in Supplementary Table S1 and S2. Here, the term "count" refers to differentially expressed genes that fall within a certain pathway.

(11) Line 111:

Again, no reasoning or description of why and how the experiment was done here.

Based on the results of KEGG enrichment analysis, DEMs are associated with pathways such as thiamine metabolism, tryptophan metabolism, nitrogen metabolism, amino acid sugar and nucleotide sugar metabolism, pantothenic acid and CoA biosynthesis, and nucleotide sugar production compounds synthesis. To specifically investigate the metabolic pathways involved action mechanism of quinofumelin, we performed further metabolomic experiments. Therefore, we have added this description according the reviewer’s suggestions.

(12) Figure 2a:

It seems many more metabolites were reduced than increased. Is this expected? Due to the antifungal activity of this compound, how sick is the fungus upon treatment? A physiological study on F. graminearum (in a dose-dependent manner) should be done prior to the omics study. Why do you think there's a stark difference between positive and negative modes in terms of number of metabolites down- and up-regulated?

Quinofumelin demonstrates exceptional antifungal activity against Fusarium graminearum. The results indicate that the number of reduced metabolites significantly exceeds the number of increased metabolites upon quinofumelin treatment. Mycelial growth is markedly inhibited under quinofumelin exposure. Prior to conducting omics studies, we performed a series of physiological and biochemical experiments (refer to Qian Xiu's dissertation https://paper.njau.edu.cn/openfile?dbid=72&objid=50_49_57_56_49_49&flag=free). Upon quinofumelin treatment, the number of down-regulated metabolites notably surpasses that of up-regulated metabolites compared to the control group. Based on the findings from the down-regulated metabolites, we conducted experiments by exogenously supplementing these metabolites under quinofumelin treatment to investigate whether mycelial growth could be restored. The results revealed that only the exogenous addition of uracil can restore mycelial growth impaired by quinofumelin.

Quinofumelin exhibits an excellent antifungal activity against F. graminearum. At a concentration of 1 μg/mL, quinofumelin inhibits mycelial growth by up to 90%. This inhibitory effect indicates that life activities of F. graminearum are significantly disrupted by quinofumelin. Consequently, there is a marked difference in down- and up-regulated metabolites between quinofumelin-treated group and untreated control group. The detailed results were presented in Figures 1 and 2.

(13) Figure 2e:

This is a good analysis. To help represent the data more clearly, the authors can consider representing the expression using fold change with a p-value for each gene.

To more clearly represent the data, we have incorporated the information on significant differences in metabolites in the de novo pyrimidine biosynthesis pathway, as affected by quinofumelin, in accordance with the reviewer’s suggestions.

(14) Line 142:

Please indicate fold change and p-value for statistical significance. Did you validate this by RT-qPCR?

We validated the expression level of the DHODH gene under quinofumelin treatment using RT-qPCR. The results indicated that, upon treatment with the EC50 and EC90 concentrations of quinofumelin, the expression of the DHODH gene was significantly reduced by 11.91% and 33.77%, respectively (P<0.05). The corresponding results have been shown in Figure S4.

(15) Line 145:

It looks like uracil is the only metabolite differentially abundant in the samples - how did you conclude this whole pathway was impacted by the treatment?

The experiments involving the exogenous supplementation of uracil revealed that the addition of uracil could restore mycelial growth inhibited by quinofumelin. Consequently, we infer that quinofumelin disrupts the de novo pyrimidine biosynthesis pathway. In addition, as uracil is the end product of the de novo pyrimidine biosynthesis pathway, the disruption of this pathway results in a reduction in uracil levels.

(16) Figure 3:

What sequence was used as the root of the tree? Why were the species chosen? Since the BLAST query was Homo sapiens sequence, would it be good to use that as the root?

FgDHODHII sequence was used as the root of the tree. These selected fungal species represent significant plant-pathogenic fungi in agriculture production. According to your suggestion, we have removed the BLAST query of Homo sapiens in Figure 3.

(17) Figure 4:

How were the concentrations used to test chosen?

Prior to this experiment, we carried out concentration-dependent exogenous supplementation experiments. The results indicated that 50 μg/mL of uracil can fully restore mycelial growth inhibited by quinofumelin. Consequently, we chose 50 μg/mL as the testing concentration.

(18) Line 164:

Why do you hypothesize supplementing dihydroorotate would restore resistance? The metabolite seemed accumulated in the treatment condition, whereas downstream metabolites were comparable or even depleted. The DHODH gene expression was suppressed. Would accumulation of dihydroorotate be associated with growth inhibition by quinofumelin? Please include the hypothesis and rationale for the experimental setup.

DHODH regulates the conversion of dihydroorotate to orotate in the de novo pyrimidine biosynthesis pathway. The inhibition of DHODH by quinofumelin results in the accumulation of dihydroorotate and the depletion of the downstream metabolites, including UMP, uridine and uracil. Consequently, downstream metabolites were considered as positive controls, while upstream metabolite dihydroorotate served as a negative control. This design further demonstrates DHODH as action target of quinofumelin against F. graminearum. In addition, the accumulation of dihydroorotate is not associated with growth inhibition by quinofumelin; however, but the depletion of downstream metabolites in the de novo pyrimidine biosynthesis pathway is closely associated with growth inhibition by quinofumelin.

(19) Line 168:

I'm not sure if this conclusion is valid from your results in Figure 4 showing which metabolites restore growth.

o minimize the potential influence of strain-specific effects, five strains were tested in the experiments shown in Figure 4. For each strain, the first row (first column) corresponds to control condition, while second row (first column) represents treatment with 1 μg/mL of quinofumelin, which completely inhibits mycelial growth. The second row (second column) for each strain represents the supplementation with 50 μg/mL of dihydroorotate fails to restore mycelial growth inhibited by quinofumelin. In contrast, the second row (third column, fourth column, fifth colomns) for each strain demonstrated that the supplementation of 50 μg/mL of UMP, uridine and uracil, respectively, can effectively restore mycelial growth inhibited by quinofumelin.

(20) Figure 5a:

The fact you saw growth of the deletion mutant means it's not lethal. However, the growth was severely inhibited.

Our experimental results indicate that the growth of the deletion mutant is lethal. The mycelial growth observed originates from mycelial plugs that were not exposed to quinofumelin, rather than from the plates amended with quinofumelin.

(21) Figure 5b:

Would you expect different restoration of growth in the presence of quinofumelin vs. no treatment? The wild type control is missing here. Any conclusions about the relationship between quinofumelin, FgDHODHII, and other metabolites in the pathway?

Under no treatment with quinofumelin, mycelial growth remains normal and does not require restoration. In the presence of quinofumelin treatment, the supplementation of downstream metabolites in the de novo pyrimidine biosynthesis pathway can restore mycelial growth that is inhibited by quinofumelin. The wild-type control group is illustrated in Figure 4. Figure 5b depicts the phenotypes of the deletion mutants. With respect to the relationship among quinofumelin, FgDHODHII, and other metabolites, quinofumelin specifically targets the key enzyme FgDHODHII in the de novo pyrimidine biosynthesis pathway, disrupting the conversion of dihydroorotate to orotate, which consequently inhibits the synthesis downstream metabolites including uracil.

(22) Figure 6b:

Lacking positive and negative controls (known binder and non-binder). What does the Kd (in comparison to other interactions) indicate in terms of binding strength?

We tested the antifungal activities of publicly reported DHODH inhibitors (such as leflunomide and teriflunomide) against F. graminearum. The results showed that these inhibitors exhibited no significant inhibitory effects against the strain PH-1. Therefore, we lacked an effective chemical for use as a positive control in subsequent experiments. Biacore experiments offers detailed insights into molecular interactions between quinofumelin and DHODHII. As shown in Figure 6b, the left panel illustrates the time-dependent kinetic curve of quinofumelin binding to DHODHII. Within the first 60 s after quinofumelin was introduced onto the DHODHII surface, it bound to the immobilized DHODHII on the chip surface, with the response value increasing proportionally to the quinofumelin concentration. Following cessation of the injection at 60 s, quinofumelin spontaneously dissociated from the DHODHII surface, leading to a corresponding decrease in the response value. The data fitting curve presented on the right panel indicates that the affinity constant KD of quinofumelin for DHODHII is 6.606×10-6 M, which falls within the typical range of KD values (10-3 ~ 10-6 M) for protein-small molecule interaction patterns. A lower KD value indicates a stronger affinity; thus, quinofumelin exhibits strong binding affinity towards DHODHII.

Reviewer #3 (Recommendations for the authors):

The authors should add information about the other molecule within this class, ipflufenoquin, and what is known about it. There are already published data on its mode of action on DHODH and the role of pyrimidine biosynthesis.

We have added the information regarding action mechanism of ipflufenoquin against filamentous fungi in discussion section.

The work of Higashimura et al is not appreciated well enough as they already showed the role of quinofumelin upon DHODH II.

We sincerely appreciate the reviewer's insightful comment regarding the work of Higashimura et al. We agree that their investigation into the role of quinofumelin in DHODH II inhibition provides critical foundational insights for this field. In the revised manuscript, we have incorporated the reference in the introduction section and expanded the discussion of their work in the discussion section to more effectively contextualize their contributions.

It is unclear how the protein model was established and this should be included. What species is the molecule from and how was it obtained? How are they different from Fusarium?

The three-dimensional structural model of F. graminearum DHODHII protein, as predicted by AlphaFold, was obtained from the UniProt database. Additionally, a detailed description along with appropriate citations has been incorporated in the ‘Manuscript’ file.

Author response:

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

Reviewer #1 (Public Review):

We thank the reviewer for the positive feedback on the work. The reviewer has raised two weaknesses and in the following we discuss how those can be addressed.  

Weaknesses:

The impact of the article is limited by using a network with discrete time- steps, and only a small number of time steps from stimulus to reward. They assume that each time step is on the order of hundreds of ms. They justify this by pointing to some slow intrinsic mechanisms, but they do not implement these slow mechanisms is a network with short time steps, instead they assume without demonstration that these could work as suggested. This is a reasonable first approximation, but its validity should be explicitly tested.

Our goal here was to give a proof of concept that online random feedback is sufficient to train an RNN to estimate value. Indeed, it is important to show that the idea works in a model where the slow mechanisms are explicitly implemented. However, this is a non-trivial task and desired to be addressed in future works.  

As the delay between cue and reward increases the performance decreases. This is not surprising given the proposed mechanism, but is still a limitation, especially given that we do not really know what a is the reasonable value of a single time step.

In reply to this comment and the other reviewer's related comment, we have conducted two sets of additional simulations, one for examining incorporation of eligibility traces, and the other for considering (though not mechanistically implementing) behavioral time-scale synaptic plasticity (BTSP). We have added their results to the revised manuscript as Appendix. We think that the results addressed this point to some extent while how longer cue-reward delay can be learnt by elaboration of the model remains as a future issue.

Reviewer #2 (Public Review):

We thank the reviewer for the positive feedback on the work. The reviewer gave comments on our revisions, and here we discuss how those can be addressed.

Comments on revisions: I would still want to see how well the network learns tasks with longer time delays (on the order of 100 or even 1000 timesteps). Previous work has shown that random feedback struggles to encode longer timescales (see Murray 2019, Figure 2), so I would be interested to see how that translates to the RL context in your model.

We would like to note that in Murray et al 2019 the random feedback per se appeared not to be primarily responsible for the difficulty in encoding longer timesclaes. In the Figure 2d (Murray 2019), the author compared his RFLO (random feedback local online) and BPTT with two intermediate algorithms, which incorporated either one of the two approximations made in RFLO: i) random feedback instead of symmetric feedback, and ii) omittance of non-local effect (i.e., dependence of the derivative of the loss with respect to a given weight on the other weights). The performance difference between RFLO and BPTT was actually mostly explained by ii), as the author mentioned "The results show that the local approximation is essentially fully responsible for the performance difference between RFLO and BPTT, while there is no significant loss in performance due to the random feedback alone. (Line 6-8, page 7 of Murray, 2019, eLife)".

Meanwhile, regarding the difference in the performance of the model with random feedback vs the model with symmetric feedback in our settings, actually it appeared (already) in the case with 6 time-steps or less (the biologically constrained model with random feedback performed worse: Fig. 6J, left).

In practice, our model, either with random or symmetric feedback, would not be able to learn the cases with very long delays. This is indeed a limitation of our model. However, our model is critically different from the model of Murray 2019 in that we use RL rather than supervised learning and we use a scalar bootstrapped (TD) reward-prediction-error rather than the true output error. We would think that these differences may be major reasons for the limited learning ability of our model.

Regarding the feasibility of the model when tasks involve longer time delays: Indeed this is a problem and the other reviewers have also raised the same point. Our model can be extended by incorporating either a kind of eligibility trace (similar one to those contained in RFLO and e-prop) or behavioral time-scale synaptic plasticity (BTSP), and we have added the results of simulations incorporating each to the revised manuscript as Appendix. But how longer cue-reward delay can be learnt by elaboration of the model remains as a future issue.

Reviewer #3 (Public Review):

Comments on revisions: Thank you for addressing all my comments in your reply.

We are happy to learn that all concerns raised by the reviewer in the previous round were addressed adequately. We agree with the reviewer that there are several ways the work can be improved.

The various points raised by the reviewers at weaknesses are desired to be taken up in future works.

Author response:

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

Reviewer #1 (Recommendations for the authors):

Suggestions:

Although this study has an impressive dataset, I felt that some parts of the discussion would benefit from further explanation, specifically when discussing the differences in female aggression direction between groups with different sex compositions. In the discussion is suggested that males buffer female-on-female aggression and that they 'support' lower-ranking females (see line 212), however, the study only tested the sex composition of the group and does not provide any evidence of this buffering. Thus, I would suggest adding more information on how this buffering or protection from males might manifest (for example, listing male behaviours that might showcase this protection) or referencing other studies that support this claim. Another example of this can be found in lines 223-224, which suggests that females choose lower-ranking individuals when they are presented with a larger pool of competitors; however, in lines 227-228, it's stated that this result contradicts previous work in baboons, which makes the previous claim seem unjustified. I recommend adding other examples from studies that support the results of this paper and adding a line that addresses reasons why these differences between gorillas and baboons might be caused (for example, different social dynamics or ecological constraints). In addition, I suggest the inclusion of physiological data such as direct measures of energy expenditure, caloric intake, or hormone levels, as it would strengthen the claims made in the second paragraph of the discussion. However, I understand this might not be possible due to data or time constraints, so I suggest adding more robust justification on why lactation and pregnancy were used as a proxy for energetic need. In the methods (lines 127-128), it is unclear which phase of the pregnancy or lactation is more energetically demanding. I would also suggest adding a comment on the limitations of using reproductive state to infer energetic need. Lastly, if the data is available, I believe it would be interesting to add body size and age of the females or the size difference between aggressor and target as explanatory variables in the models to test if physiological characteristics influence female-on-female aggression.

Male support:

We have now added more references (Watts 1994, 1997) and enriched our arguments regarding male presence buffering aggression. Previous research suggests that male gorillas may support lower-ranking females and they may intervene in female-female conflicts (Sicotte 2002). Unfortunately, our dataset did not allow us to test for male protection. We conduct proximity scans every 10 minutes and these scans are not associated to each interaction, meaning that we cannot reliably test if proximity to a male influences the likelyhood to receive aggression.

Number of competitors and choice of weaker competitors:

We added a very relevant reference in humans, showing that people choose weaker competitors when they have they can choose. We removed the example to baboons because it used sex ratio and the relevance to our study was not that straightforward.

Reproductive state as a proxy for energetic needs:

We now mention clearly that reproductive state is an indirect measure of energetic needs.

We rephrased our methods to: “Lactation is often considered more energetically demanding than pregnancy as a whole but the latest stages of pregnancy are highly energetically demanding, potentially even more than lactation”

Unfortunately, we do not have access to physiological and body size data. Regarding female age, for many females, ages are estimates with errors up to a decade, and thus, we choose not to use them as a reliable predictor. Having accurate values for all these variables, would indeed be very valuable and improve the predicting power of our study.

Recommendations for writing and presentation:

Overall, the manuscript is well-organised and well-written, but there are certain areas that could improve in clarity. In the introduction, I believe that the term 'aggression heuristic' should be introduced earlier and properly defined in order to accommodate a broader audience. The main question and aims of the study are not stated clearly in the last paragraph of the introduction. In the methods, I think it would improve the clarity to add a table for the classification of each type of agonistic interactions instead of naming them in the text. For example, a table that showcase the three intensity categories (severe, mild and moderate), than then dives into each behaviour (e.g. hit, bite, attack, etc.) and a short description of these behaviours, I think this would be helpful since some of the behaviours mentioned can be confusing (what's the difference between attack, hit and fight?). In addition, in line 104, it states that all interactions were assigned equal intensity, which needs to be explained.

We now define aggression heuristics in both the abstract and the first paragraph of the introduction. We have also explained aggressive interactions that their nature was not obvious from their names. Hopefully, these explanations make clear the differences among the recorded behaviours.

We have now specified that the “equal intensity” refers to avoidances and displacements used to infer power relationships: “We assigned to all avoidance/displacement interactions equal intensity, that is, equal influence to the power relationship of the interacting individuals”

Minor corrections:

(1) In line 41, there is a 1 after 'similar'. I am unsure if it's a mistake or a reference.

We corrected the typo.

(2) In lines 68-69, there is mention of other studies, but no references are provided.

We added citations as suggested.

(3) Remove the reference to Figure 1 (line 82) from the introduction; the figure should be referenced in the text just before the image, however, your figure is in a different section.

We removed the reference as suggested.

(4) Line 98 and 136, it's written 'ad libtum' but the correct spelling is 'ad libitum'.

We corrected the typo.

(5) Figure 3, remove the underscores between the words in the axis titles.

We removed the underscores.

Reviewer #2 (Recommendations for the authors):

Here, I have outlined some specific suggestions that require attention. Addressing these comments will enhance the readability and enhance the quality of the manuscript.

(1) L69. Add citation here, indicating the studies focusing on aggression rates.

We added citations as suggested.

(2) L88. The study periods used in this study and the authors' previous study (Reference 11) are different. So please add one table as Table 1 showing the details info on the sampling efforts and data included in their analysis of this study. For example, the study period, the numbers of females and males, sampling hours, the number of avoidance/displacement behaviors used to calculate individual Elo-ratings, and the number of mild/moderate/severe aggressive interactions, etc.

We have now added another table, as suggested (new Table 1) and we have also made clear that we used the hierarchies presented in detail in (Smit & Robbins 2025).

(3) L103. If readers do not look over Reference 25 on purpose, they do not know what the authors want to talk about and why they mention the optimized Elo-rating method. Clarify this statement and add more content explaining the differences between the two methods, or just remove it.

We rephrased the text and in response to the previous comment, we clearly state that there are more details about our approach in Smit & Robbins 2025. At the end of the relevant sentence, we added the following parenthesis “(see “traditional Elo rating method”; we do not use the “optimized Elorating method” as it yields similar results and it is not widely used)” and we removed the sentence referring to the optimized Elo-rating method.

(4) L110. Here, the authors stated that the individual with the standardized Elo-score 1 was the highest-ranking. L117, the "aggression direction" score of each aggressive interaction was the standardized Elo-score of the aggressor, subtracting that of the recipient. So, when the "aggression direction" score was 1, it should mean that the aggressor was the highest-ranking and the recipient was the lowest-ranking female. This is not as the authors stated in L117-120 (where the description was incorrectly reversed). Please clarify.

The highest ranking individual has indeed Elo_score equal to 1 and we calculated the interaction score (or "aggression direction score") of each aggressive interaction by subtracting the standardized Elo-score of the aggressor from that of the recipient (Elo_recepient – Elo_aggressor). So, when the aggressor is the lowest-ranking female (Elo_score=0) and the recipient the highestranking female one (Elo_score=1), the "aggression direction score" is 1-0 = 1.

(5) Regarding point 3 of the Public Review, please also revise/expand the paragraph L193-208 in the Discussion section accordingly.

Please see our response to the public review. We have enriched the results section, added pairwise comparisons in a new table (Table 2) and modified the discussion accordingly.

(6) Table 1. It's not clear why authors added the column 'Aggression Rate' but did not provide any explanation in the Methods/Results section. How did they calculate the correlation between each tested variable and the "overall adult female aggression rates"? Correlating the number of females in the first trimester of female pregnancy with the female aggression rates in each study group? What did the correlation coefficients mean? L202-204 may provide some hints as to why the authors introduced the Aggression Rate. But it should be made clear in the previous text.

We now added more details in the legend of the table to make our point clear: “To highlight that aggression rates can increase due to increase in interactions of different score, we also include the effect of some of the tested variables on overall adult female aggression rates, based on results of linear mixed effects models from (Smit & Robbins 2024).”  We did not include detailed methods to calculate those results because they are detailed in (Smit & Robbins 2024). We find it valuable to show the results of both aggression rates and aggression directionality according to the same predictor variables as a means to clarify that aggression rates and aggression directionality are not always coordinated to one another (they do not always change in a consistent manner relative to one another).

(7) L166.This is not rigorous. Please rephrase. There is only one western gorilla group containing only one resident male included in the analysis.

We have toned down our text: “Our results did not show any significant difference between femalefemale aggression patterns within the one western and four mountain gorillas groups”

(8) L167. I don't think the interaction scores in the third trimester of female pregnancy were significantly higher than those in the first trimester. The same concern applies in L194-195.

We have now added a new table with post hoc pairwise comparisons among the different reproductive states that clarifies that.

(9) L202. There is no column 'Aggression rates' in Table 1 of Reference 11.

We have rephrased to make clear that we refer to Table 1 of the present study.

(10) L204-205. Reference 49. Maybe not a proper citation here. This claim requires stronger evidence or further justification. Additionally, please rephrase and clarify the arguments in L204208 for better readability and precision.

We have added three more references and rephrased to clarify our argument.

Reviewer #3 (Recommendations for the authors):

(1) Line 41: The word "similar" is misspelled.

We corrected the typo.

Author response:

Reviewer #1 (Public review):

Summary:

Chao et al. produced an updated version of the SpliceAI package using modern deep learning frameworks. This includes data preprocessing, model training, direct prediction, and variant effect prediction scripts. They also added functionality for model fine-tuning and model calibration. They convincingly evaluate their newly trained models against those from the original SpliceAI package and investigate how to extend SpliceAI to make predictions in new species. While their comparisons to the original SpliceAI models are convincing on the grounds of model performance, their evaluation of how well the new models match the original's understanding of non-local mutation effects is incomplete. Further, their evaluation of the new calibration functionality would benefit from a more nuanced discussion of what set of splice sites their calibration is expected to hold for, and tests in a context for which calibration is needed.

Strengths:

(1) They provide convincing evidence that their new implementation of SpliceAI matches the performance of the original model on a similar dataset while benefiting from improved computational efficiencies. This will enable faster prediction and retraining of splicing models for new species as well as easier integration with other modern deep learning tools.

(2) They produce models with strong performance on non-human model species and a simple, well-documented pipeline for producing models tuned for any species of interest. This will be a boon for researchers working on splicing in these species and make it easy for researchers working on new species to generate their own models.

(3) Their documentation is clear and abundant. This will greatly aid the ability of others to work with their code base.

We thank the reviewer for these positive comments.  

Weaknesses:

(1) The authors' assessment of how much their model retains SpliceAI's understanding of "nonlocal effects of genomic mutations on splice site location and strength" (Figure 6) is not sufficiently supported. Demonstrating this would require showing that for a large number of (non-local) mutations, their model shows the same change in predictions as SpliceAI or that attribution maps for their model and SpliceAI are concordant even at distances from the splice site. Figure 6A comes close to demonstrating this, but only provides anecdotal evidence as it is limited to 2 loci. This could be overcome by summarizing the concordance between ISM maps for the two models and then comparing across many loci. Figure 6B also comes close, but falls short because instead of comparing splicing prediction differences between the models as a function of variants, it compares the average prediction difference as a function of the distance from the splice site. This limits it to only detecting differences in the model's understanding of the local splice site motif sequences. This could be overcome by looking at comparisons between differences in predictions with mutants directly and considering non-local mutants that cause differences in splicing predictions.

We agree that two loci are insufficient to demonstrate preservation of non-local effects. To address this, we have extended our analysis to a larger set of sites: we randomly sampled 100 donor and 100 acceptor sites, applied our ISM procedure over a 5,001 nt window centered at each site for both models, and computed the ISM map as before. We then calculated the Pearson correlation between the collection of OSAI_MANE and SpliceAI ISM importance scores. We also created 10 additional ISM maps similar to those in Figure 6A, which are now provided in Figure S23.

Follow is the revised paragraph in the manuscript’s Results section:

First, we recreated the experiment from Jaganathan et al. in which they mutated every base in a window around exon 9 of the U2SURP gene and calculated its impact on the predicted probability of the acceptor site. We repeated this experiment on exon 2 of the DST gene, again using both SpliceAI and OSAI_MANE . In both cases, we found a strong similarity between the resultant patterns between SpliceAI and OSAI_MANE , as shown in Figure 6A. To evaluate concordance more broadly, we randomly selected 100 donor and 100 acceptor sites and performed the same ISM experiment on each site. The Pearson correlation between SpliceAI and OSAI_MANE yielded an overall median correlation of 0.857 (see Methods; additional DNA logos in Figure S23). 

To characterize the local sequence features that both models focus on, we computed the average decrease in predicted splice-site probability resulting from each of the three possible singlenucleotide substitutions at every position within 80bp for 100 donor and 100 acceptor sites randomly sampled from the test set (Chromosomes 1, 3, 5, 7, and 9). Figure 6B shows the average decrease in splice site strength for each mutation in the format of a DNA logo, for both tools.

We added the following text to the Methods section:

Concordance evaluation of ISM importance scores between OSAI_MANE and SpliceAI

To assess agreement between OSAI_MANE and SpliceAI across a broad set of splice sites, we applied our ISM procedure to 100 randomly chosen donor sites and 100 randomly chosen acceptor sites. For each site, we extracted a 5,001 nt window centered on the annotated splice junction and, at every coordinate within that window, substituted the reference base with each of the three alternative nucleotides. We recorded the change in predicted splice-site probability for each mutation and then averaged these Δ-scores at each position to produce a 5,001-score ISM importance profile per site.

Next, for each splice site we computed the Pearson correlation coefficient between the paired importance profiles from ensembled OSAI_MANE and ensembled SpliceAI. The median correlation was 0.857 for all splice sites. Ten additional zoom-in representative splice site DNA logo comparisons are provided in Supplementary Figure S23.

(2) The utility of the calibration method described is unclear. When thinking about a calibrated model for splicing, the expectation would be that the models' predicted splicing probabilities would match the true probabilities that positions with that level of prediction confidence are splice sites. However, the actual calibration that they perform only considers positions as splice sites if they are splice sites in the longest isoform of the gene included in the MANE annotation. In other words, they calibrate the model such that the model's predicted splicing probabilities match the probability that a position with that level of confidence is a splice site in one particular isoform for each gene, not the probability that it is a splice site more broadly. Their level of calibration on this set of splice sites may very well not hold to broader sets of splice sites, such as sites from all annotated isoforms, sites that are commonly used in cryptic splicing, or poised sites that can be activated by a variant. This is a particularly important point as much of the utility of SpliceAI comes from its ability to issue variant effect predictions, and they have not demonstrated that this calibration holds in the context of variants. This section could be improved by expanding and clarifying the discussion of what set of splice sites they have demonstrated calibration on, what it means to calibrate against this set of splice sites, and how this calibration is expected to hold or not for other interesting sets of splice sites. Alternatively, or in addition, they could demonstrate how well their calibration holds on different sets of splice sites or show the effect of calibrating their models against different potentially interesting sets of splice sites and discuss how the results do or do not differ.

We thank the reviewer for highlighting the need to clarify our calibration procedure. Both SpliceAI and OpenSpliceAI are trained on a single “canonical” transcript per gene: SpliceAI on the hg 19 Ensembl/Gencode canonical set and OpenSpliceAI on the MANE transcript set. To calibrate each model, we applied post-hoc temperature scaling, i.e. a single learnable parameter that rescales the logits before the softmax. This adjustment does not alter the model’s ranking or discrimination (AUC/precision–recall) but simply aligns the predicted probabilities for donor, acceptor, and non-splice classes with their observed frequencies. As shown in our reliability diagrams (Fig. S16-S22), temperature scaling yields negligible changes in performance, confirming that both SpliceAI and OpenSpliceAI were already well-calibrated. However, we acknowledge that we didn’t measure how calibration might affect predictions on non-canonical splice sites or on cryptic splicing. It is possible that calibration might have a detrimental effect on those, but because this is not a key claim of our paper, we decided not to do further experiments. We have updated the manuscript to acknowledge this potential shortcoming; please see the revised paragraph in our next response.

(3) It is difficult to assess how well their calibration method works in general because their original models are already well calibrated, so their calibration method finds temperatures very close to 1 and only produces very small and hard to assess changes in calibration metrics. This makes it very hard to distinguish if the calibration method works, as it doesn't really produce any changes. It would be helpful to demonstrate the calibration method on a model that requires calibration or on a dataset for which the current model is not well calibrated, so that the impact of the calibration method could be observed.

It’s true that the models we calibrated didn’t need many changes. It is possible that the calibration methods we used (which were not ours, but which were described in earlier publications) can’t improve the models much. We toned down our comments about this procedure, as follows.

Original:

“Collectively, these results demonstrate that OSAIs were already well-calibrated, and this consistency across species underscores the robustness of OpenSpliceAI’s training approach in diverse genomic contexts.” Revised:

“We observed very small changes after calibration across phylogenetically diverse species, suggesting that OpenSpliceAI’s training regimen yielded well‐calibrated models, although it is possible that a different calibration algorithm might produce further improvements in performance.”

Reviewer #2 (Public review):

Summary:

The paper by Chao et al offers a reimplementation of the SpliceAI algorithm in PyTorch so that the model can more easily/efficiently be retrained. They apply their new implementation of the SpliceAI algorithm, which they call OpenSpliceAI, to several species and compare it against the original model, showing that the results are very similar and that in some small species, pretraining on other species helps improve performance.

Strengths:

On the upside, the code runs fine, and it is well documented.

Weaknesses:

The paper itself does not offer much beyond reimplementing SpliceAI. There is no new algorithm, new analysis, new data, or new insights into RNA splicing. There is no comparison to many of the alternative methods that have since been published to surpass SpliceAI. Given that some of the authors are well-known with a long history of important contributions, our expectations were admittedly different. Still, we hope some readers will find the new implementation useful.

We thank the reviewer for the feedback. We have clarified that OpenSpliceAI is an open-source PyTorch reimplementation optimized for efficient retraining and transfer learning, designed to analyze cross-species performance gains, and supported by a thorough benchmark and the release of several pretrained models to clearly position our contribution.

Reviewer #3 (Public review):

Summary:

The authors present OpenSpliceAI, a PyTorch-based reimplementation of the well-known SpliceAI deep learning model for splicing prediction. The core architecture remains unchanged, but the reimplementation demonstrates convincing improvements in usability, runtime performance, and potential for cross-species application.

Strengths:

The improvements are well-supported by comparative benchmarks, and the work is valuable given its strong potential to broaden the adoption of splicing prediction tools across computational and experimental biology communities.

Major comments:

Can fine-tuning also be used to improve prediction for human splicing? Specifically, are models trained on other species and then fine-tuned with human data able to perform better on human splicing prediction? This would enhance the model's utility for more users, and ideally, such fine-tuned models should be made available.

We evaluated transfer learning by fine-tuning models pretrained on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), Arabidopsis (OSAI_Arabidopsis), and zebrafish (OSAI_Zebrafish) on human data. While transfer learning accelerated convergence compared to training from scratch, the final human splicing prediction accuracy was comparable between fine-tuned and scratch-trained models, suggesting that performance on our current human dataset is nearing saturation under this architecture.

We added the following paragraph to the Discussion section:

We also evaluated pretraining on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), zebrafish (OSAI_Zebrafish), and Arabidopsis (OSAI_Arabidopsis) followed by fine-tuning on the human MANE dataset. While cross-species pretraining substantially accelerated convergence during fine-tuning, the final human splicing-prediction accuracy was comparable to that of a model trained from scratch on human data. This result indicates that our architecture seems to capture all relevant splicing features from human training data alone, and thus gains little or no benefit from crossspecies transfer learning in this context (see Figure S24).

Reviewer #1 (Recommendations for the authors):

We thank the editor for summarizing the points raised by each reviewer. Below is our point-bypoint response to each comment:

(1) In Figure 3 (and generally in the other figures) OpenSpliceAI should be replaced with OSAI_{Training dataset} because otherwise it is hard to tell which precise model is being compared. And in Figure 3 it is especially important to emphasize that you are comparing a SpliceAI model trained on Human data to an OSAI model trained and evaluated on a different species.

We have updated the labels in Figures 3, replacing “OpenSpliceAI” with “OSAI_{training dataset}” to more clearly specify which model is being compared.

(2) Are genes paralogous to training set genes removed from the validation set as well as the test set? If you are worried about data leakage in the test set, it makes sense to also consider validation set leakage.

Thank you for this helpful suggestion. We fully agree, and to avoid any data leakage we implemented the identical filtering pipeline for both validation and test sets: we excluded all sequences paralogous or homologous to sequences in the training set, and further removed any sequence sharing > 80 % length overlap and > 80 % sequence identity with training sequences. The effect of this filtering on the validation set is summarized in Supplementary Figure S7C.

Figure S7. (C) Scatter plots of DNA sequence alignments between validation and training sets for Human-MANE, mouse, honeybee, zebrafish, and Arabidopsis. Each dot represents an alignment, with the x-axis showing alignment identity and the y-axis showing alignment coverage. Alignments exceeding 80% for both identity and coverage are highlighted in the redshaded region and were excluded from the test sets.

Reviewer #3 (Recommendations for the authors):

(1) The legend in Figure 3 is somewhat confusing. The labels like "SpliceAI-Keras (species name)" may imply that the model was retrained using data from that species, but that's not the case, correct?

Yes, “SpliceAI-Keras (species name)” was not retrained; it refers to the released SpliceAI model evaluated on the specified species dataset. We have revised the Figure 3 legends, changing “SpliceAI-Keras (species name)” to “SpliceAI-Keras” to clarify this.

(2) Please address the minor issues with the code, including ensuring the conda install works across various systems.

We have addressed the issues you mentioned. OpenSpliceAI is now available on Conda and can be installed with:  conda install openspliceai. 

The conda package homepage is at: https://anaconda.org/khchao/openspliceai We’ve also corrected all broken links in the documentation.

(3) Utility:

I followed all the steps in the Quick Start Guide, and aside from the issues mentioned below, everything worked as expected.

I attempted installation using conda as described in the instructions, but it was unsuccessful. I assume this method is not yet supported.

In Quick Start Guide: predict, the link labeled "GitHub (models/spliceai-mane/10000nt/)" appears to be incorrect. The correct path is likely "GitHub (models/openspliceaimane/10000nt/)".

In Quick Start Guide: variant (https://ccb.jhu.edu/openspliceai/content/quick_start_guide/quickstart_variant.html#quick-startvariant), some of the download links for input files were broken. While I was able to find some files in the GitHub repository, I think the -A option should point to data/grch37.txt, not examples/data/input.vcf, and the -I option should be examples/data/input.vcf, not data/vcf/input.vcf.

Thank you for catching these issues. We’ve now addressed all issues concerning Conda installation and file links. We thank the editor for thoroughly testing our code and reviewing the documentation.

Author Response:

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

Reviewer #1 (Public review):

Summary:

This work uses a novel, ethologically relevant behavioral task to explore decision-making paradigms in C. elegans foraging behavior. By rigorously quantifying multiple features of animal behavior as they navigate in a patch food environment, the authors provide strong evidence that worms exhibit one of three qualitatively distinct behavioral responses upon encountering a patch: (1) "search", in which the encountered patch is below the detection threshold; (2) "sample", in which animals detect a patch encounter and reduce their motor speed, but do not stay to exploit the resource and are therefore considered to have "rejected" it; and (3) "exploit", in which animals "accept" the patch and exploit the resource for tens of minutes. Interestingly, the probability of these outcomes varies with the density of the patch as well as the prior experience of the animal. Together, these experiments provide an interesting new framework for understanding the ability of the C. elegans nervous system to use sensory information and internal state to implement behavioral state decisions.

Strengths:

The work uses a novel, neuroethologically-inspired approach to studying foraging behavior

The studies are carried out with an exceptional level of quantitative rigor and attention to detail

Powerful quantitative modeling approaches including GLMs are used to study the behavioral states that worms enter upon encountering food, and the parameters that govern the decision about which state to enter

The work provides strong evidence that C. elegans can make 'accept-reject' decisions upon encountering a food resource

Accept-reject decisions depend on the quality of the food resource encountered as well as on internally represented features that provide measurements of multiple dimensions of internal state, including feeding status and time

Reviewer #2 (Public review):

This study provides an experimental and computational framework to examine and understand how C. elegans make decisions while foraging environments with patches of food. The authors show that C. elegans reject or accept food patches depending on a number of internal and external factors.

The key novelty of this paper is the explicit demonstration of behavior analysis and quantitative modeling to elucidate decision-making processes. In particular, the description of the exploring vs. exploiting phases, and sensing vs. non-sensing categories of foraging behavior based on the clustering of behavioral states defined in a multi-dimensional behavior-metrics space, and the implementation of a generalized linear model (GLM) whose parameters can provide quantitative biological interpretations.

The work builds on the literature of C. elegans foraging by adding the reject/accept framework.

Reviewer #3 (Public review):

Summary:

In this study by Haley et al, the authors investigated explore-exploit foraging using C. elegans as a model system. Through an elegant set of patchy environment assays, the authors built a GLM based on past experience that predicts whether an animal will decide to stay on a patch to feed and exploit that resource, instead of choosing to leave and explore other patches.

Strengths:

I really enjoyed reading this paper. The experiments are simple and elegant, and address fundamental questions of foraging theory in a well-defined system. The experimental design is thoroughly vetted, and the authors provide a considerable volume of data to prove their points. My only criticisms have to do with the data interpretation, which I think are easily addressable.

Weaknesses:

History-dependence of the GLM

The logistic GLM seems like a logical way to model a binary choice, and I think the parameters you chose are certainly important. However, the framing of them seem odd to me. I do not doubt the animals are assessing the current state of the patch with an assessment of past experience; that makes perfect logical sense. However, it seems odd to reduce past experience to the categories of recently exploited patch, recently encountered patch, and time since last exploitation. This implies the animals have some way of discriminating these past patch experiences and committing them to memory. Also, it seems logical that the time on these patches, not just their density, should also matter, just as the time without food matters. Time is inherent to memory. This model also imposes a prior categorization in trying to distinguish between sensed vs. not-sensed patches, which I criticized earlier. Only "sensed" patches are used in the model, but it is questionable whether worms genuinely do not "sense" these patches.

It seems more likely that the worm simply has some memory of chemosensation and relative satiety, both of which increase on patches and decrease while off of patches. The magnitudes are likely a function of patch density. That being said, I leave it up to the reader to decide how best to interpret the data.

Model design: We agree with the reviewer that past experience is not likely to be discretized into the exact parameters of our model. We have added to our manuscript to further clarify this point (lines 645-647). Investigating the mechanisms behind this behavior is beyond the scope of this project but is certainly an exciting trajectory for future C. elegans research.

osm-6

The argument is that osm-6 animals can't sense food very well, so when they sense it, they enter the exploitation state by default. That is what they appear to do, but why? Clearly they are sensing the food in some other way, correct? Are ciliated neurons the only way worms can sense food? Don't they also actively pump on food, and can therefore sense the food entering their pharynx? I think you could provide further insight by commenting on this. Perhaps your decision model is dependent on comparing environmental sensing with pharyngeal sensing? Food intake certainly influences their decision, no? Perhaps food intake triggers exploitation behavior, which can be over-run by chemo/mechanosensory information?

osm-6 behavior: We thank the reviewer for pointing out the need to further elaborate on a mechanistic hypothesis to explain the behavior of osm-6 sensory mutants. We agree with the reviewer’s speculation that post-ingestive and other non-ciliary sensory cues likely drive detection of food. We have added additional commentary to our manuscript to state this (lines 529-538).

Impact

I think this work will have a solid impact on the field, as it provides tangible variables to test how animals assess their environment and decide to exploit resources. I think the strength of this research could be strengthened by a reassessment of their model that would both simplify it and provide testable timescales of satiety/starvation memory.

Reviewer #2 (Recommendations for the authors):

The authors have addressed most of my concerns.

Reviewer #3 (Recommendations for the authors):

The authors provide a considerable amount of processed data (great, thank you!), but it would be even better if they provided the raw data of the worm coordinates, and when and where these coordinates overlapped with patches. This is the raw data that was ultimately used for all the quantifications in the paper, and would be incredibly useful to readers who are interested in modeling the data themselves.

This should not be prohibitive.

Data Availability: We thank the reviewer for pointing out this need. We are uploading all processed data (e.g. worm coordinates relative to the arena and patches) to a curated data storage server. We have updated our data availability statement to state this (lines 684-688).

Search vs. sample & sensing vs. non-sensing.

The different definitions of behaviors in Figures 2H-K are a bit confusing. I think the confusion stems in part from the changing terms and color associations in Figures 2 H-K. Essentially the explore density in Figure 2 H is split into two densities based on the two densities (sensing vs. non-responding) observed in Figure 2I. In turn, the sensing density in Figure 2I is split into two densities (explore vs exploit) based on the two densities observed in Figure 2 H. But the way the figures are colored, yellow means search (Figure 2H) and non-responding (Figure 2I), green means exploit (Figure 2H) which includes sensing and non-responding, but also exclusively sensing (Figure 2I), and blue consistently means exploit in both figures. It might help to use two different color codes for Figures 2H and 2I, and then in 2J you define search as explore AND non-responding, sample as explore AND sensing, and exploit as exploit.

Color schema: While we understand the confusion, we believe that introducing additional colors may also present some misunderstandings. We have decided to leave the figure as it is.

Author Response:

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

Reviewer #1 (Public Review):

Summary:

Two important factors in visual performance are the resolving power of the lens and the signal-to-noise ratio of the photoreceptors. These both compete for space: a larger lens has improved resolving power over a smaller one, and longer photoreceptors capture more photons and hence generate responses with lower noise. The current paper explores the tradeoff of these two factors, asking how space should be allocated to maximize eye performance (measured as encoded information).

Your summary is clear, concise and elegant. The competition is not just for space, it is for space, materials and energy. We  now emphasise that we are considering these three costs in our rewrites of the Abstract and the first paragraph of the Discussion.  

Strengths:

The topic of the paper is interesting and not well studied. The approach is clearly described and seems appropriate (with a few exceptions - see weaknesses below). In most cases, the parameter space of the models are well explored and tradeoffs are clear.  

Weaknesses:

Light level

The calculations in the paper assume high light levels (which reduces the number of parameters that need to be considered). The impact of this assumption is not clear. A concern is that the optimization may be quite different at lower light levels. Such a dependence on light level could explain why the model predictions and experiment are not in particularly good agreement. The paper would benefit from exploring this issue.

Thank you for raising this point. We briefly explained in our original Discussion, under Understanding the adaptive radiation of eyes (Version 1, Iines 756 – 762), how our method can be modified to investigate eyes adapted for lower light levels. We have some thoughts on how eyes might be adapted. In general, transduction rates are increased by increasing D, reducing f, increasing d_rh and increasing L . In addition, d_rh is increased to allow for a larger D within the constraint of eye radius/corneal surface area, and to avoid wasteful oversampling (the changes in D, f and d_rh increase acceptance angle ∆ρ). We suspect that in eyes optimised for the efficient use of space, materials and energy the increases in L will be relatively small, first because  increasing D, reducing f and increasing d_rh are much more effective at increasing transduction rate than increasing L. Second, increasing sensitivity by reducing f decreases the cost Vo whereas increasing sensitivity by increasing L increases the cost V_ph. This disadvantage, together with exponential absorption, might explain why L is only 10% - 20% longer in the apposition eyes of nocturnal bees (Somanathan et al, J. comp. Physiol. A195, 571583, 2009). Because this line of argument is speculative and enters new territory, we have not included it in our revised version. We already present a lot of new material for readers to digest, and we agree with referee 2 that “It is possible to extend the theory to other types of eyes, although it would likely require more variables and assumptions/constraints to the theory. It is thus good to introduce the conceptual ideas without overdoing the applications of the theory”. Nonetheless, we take your point that some of the eyes in our data set might be adapted for lower light levels, and we have rewritten the Discussion section, How efficiently do insects allocate resources within their apposition eyes accordingly. On line 827 – 843 we address the assumption that eyes are adapted for full daylight,  and also take the opportunity  to mention two more reasons for increasing the eye parameter p: namely increasing image velocity (Snyder, 1979), and constructing  bright zones that increase the detectability of small targets (van Hateren et al., 1989; Straw et al., 2006).

Discontinuities

The discontinuities and non-monotonicity of the optimal parameters plotted in Figure 4 are concerning. Are these a numerical artifact? Some discussion of their origin would be quite helpful.

Good points, we now address the discontinuities in the Results, where they are first observed (lines 311 - 319) 

Discrepancies between predictions and experiment

As the authors clearly describe, experimental measurements of eye parameters differ systematically from those predicted. This makes it difficult to know what to take away from the paper. The qualitative arguments about how resources should be allocated are pretty general, and the full model seems a complex way to arrive at those arguments. Could this reflect a failure of one of the assumptions that the model rests on - e.g. high light levels, or that the cost of space for photoreceptors and optics is similar? Given these discrepancies between model and experiment, it is also hard to evaluate conclusions about the competition between optics and photoreceptors (e.g. at the end of the abstract) and about the importance for evolution (end of introduction).

Your misgivings boil down to two issues: what use is a model that fails to fit the data, and do we need a complicated model to show something that seems to be intuitively obvious?  Our study is useful because it introduces new approaches, methods, factors and explanations which advance our analysis and understanding of eye design and evolution. Your comments make it clear that we failed to get this message across and we have revised the manuscript accordingly. We have rewritten the Abstract and the first paragraph of the Discussion to emphasise the value of our new measure of cost, specific volume, by including more of its practical advantages. In particular, our use of specific volume 1) opens the door to the morphospace of all eyes of given type and cost. 2) This allows one to construct performance surfaces across morphospace that not only identify optima, but by evaluating the sub-optimal cast light on efficiency and adaptability. 3) Shows that photoreceptor energy costs have a major impact on design and efficiency, and 4) allows us to calculate and compare the capacities and efficiencies of compound eyes and simple eyes using a superior measure of cost. It is also possible that your dissatisfaction was deepened by disappointment. The first sentence of our original Abstract said that the goal of design is to maximize performance, so you might have expected to see that eyes are optimised.  Given that optimization provides cast iron proof that a system is designed to be efficient, and previous studies of coding by fly LMCs (Laughlin, 1981; Srinivasan et al., 1982 & van Hateren 1992) validated Barlow’s Efficient Coding Hypothesis by showing that coding is optimised, your expectation is reasonable. However, our investigation of how the allocation of resources to optics and photoreceptors affects an eye’s performance, efficiency and design does not depend a priori  on finding optima, therefore we have removed the “maximized”. Our revised Abstract now says, “to improve performance”.  

In short, our study illustrates an old adage in statistics “All models fail to fit, but some are useful”. As is often the case, the way in which our model fails is useful. In the original version of the Results and Discussion, we argued that the allocation of resources is efficient, and identified factors that can, in principle, explain the scattering of data points. Indeed, our modelling identifies two of these deficiencies; a lack of data on species-specific energy usage, and the need for models that quantify the relationship between the quality of the captured image and the behavioural tasks for which an eye might be specialised. Thus, by examining the model’s failings we identify critical factors and pose new questions for future research.  We have rewritten the Discussion section How efficiently do insects allocate resources…. to make these points. We hope that these revisions will convince you that we have established a starting point for definitive studies, invented a vehicle that has travelled far enough to discover new territory, and shown that it can be modified to cope with difficult terrain.

Turning to the need for a complicated model, because the costs and benefits depend on elementary optics and geometry, we too thought that there ought to be a simple model. However, when we tried to formulate a simple set of equations that approximate the definitive findings of our more complicated model we discovered that this is not as straightforward as we thought.  Many of the parameters in our model interact to determine costs and benefits, and many of these interactions are non-linear (e.g. the volumes of shells in spheres involve quadratic and cubic terms, and information depends on the log of a square root). So, rather than hold back publication of our complicated model, we decided to explain how it works as clearly as we can and demonstrate its value.

In response to your final comment, “it is hard to evaluate conclusions about the competition between optics and photoreceptors (e.g. at the end of the abstract) and about the importance for evolution (end of introduction)”, we stand by our original argument. There must be competition in an eye of fixed cost, and because competition favours a heavy investment in photoreceptors, both in theory and in practice, it  is a significant factor in eye design. A match between investments in optics and photoreceptors is predicted by theory and observed in fly NS eyes, therefore this is a design principle. As for evolution, no one would deny that it is important to view the adaptive radiation of eyes through a cost-benefit lens. Our lens is the first to view the whole eye, optics and photoreceptor array, and the first to treat the costs of space, materials and energy. Although the view through our lens is a bit fuzzy, it reveals that costs, benefits and trade-offs are important. Thus we have established a promising starting point for a new and more comprehensive cost-benefit approach to understanding eye design and evolution.  As for the involvement of genes, when there are heritable changes in phenotype genes must be involved and if, as we suggest, efficient resource allocation is beneficial, the developmental mechanisms responsible for allocating resources to optics and photoreceptor array will be playing a formative role in eye evolution.

Reviewer #2 (Public Review):

Summary:

In short, the paper presents a theoretical framework that predicts how resources should be optimally distributed between receptors and optics in eyes.

Strengths:

The authors build on the principle of resource allocation within an organism and develop a formal theory for optimal distribution of resources within an eye between the receptor array and the optics. Because the two parts of eyes, receptor arrays and optics, share the same role of providing visual information to the animal it is possible to isolate these from resource allocation in the rest of the animal. This allows for a novel and powerful way of exploring the principles that govern eye design. By clever and thoughtful assumptions/constraints, the authors have built a formal theory of resource allocation between the receptor array and the optics for two major types of compound eye as well as for camera-type eyes. The theory is formalized with variables that are well characterized in a number of different animal eyes, resulting in testable predictions.

The authors use the theory to explain a number of design features that depend on different optimal distribution of resources between the receptor array and the optics in different types of eyes. As an example, they successfully explain why eye regions with different spatial resolution should be built in different ways. They also explain differences between different types of eyes, such as long photoreceptors in apposition compound eyes and much shorter receptors in camera type eyes. The predictive power in the theory is impressive.

To keep the number of parameters at a minimum, the theory was developed for two types of compound eye (neural superposition, and apposition) and for camera-type eyes. It is possible to extend the theory to other types of eyes, although it would likely require more variables and assumptions/constraints to the theory. It is thus good to introduce the conceptual ideas without overdoing the applications of the theory.

The paper extends a previous theory, developed by the senior author, that develops performance surfaces for optimal cost/benefit design of eyes. By combining this with resource allocation between receptors and optics, the theoretical understanding of eye design takes a major leap and provides entirely new sets of predictions and explanations for why eyes are built the way they are.

The paper is well written and even though the theory development in the Results may be difficult to take in for many biologists, the Discussion very nicely lists all the major predictions under separate headings, and here the text is more tuned for readers that are not entirely comfortable with the formalism of the Results section. I must point out though that the Results section is kept exemplary concise. The figures are excellent and help explain concepts that otherwise may go above the head of many biologists.

We are heartened by your appreciation of our manuscript - it persuaded us not to undertake extensive revisions – thank you.

Reviewer #3 (Public Review):

Summary:

This is a proposal for a new theory for the geometry of insect eyes. The novel costbenefit function combines the cost of the optical portion with the photoreceptor portion of the eye. These quantities are put on the same footing using a specific (normalized) volume measure, plus an energy factor for the photoreceptor compartment. An optimal information transmission rate then specifies each parameter and resource allocation ratio for a variable total cost. The elegant treatment allows for comparison across a wide range of species and eye types. Simple eyes are found to be several times more efficient across a range of eye parameters than neural superposition eyes. Some trends in eye parameters can be explained by optimal allocation of resources between the optics and photoreceptors compartments of the eye.

Strengths:

Data from a variety of species roughly align with rough trends in the cost analysis, e.g. as a function of expanding the length of the photoreceptor compartment.

New data could be added to the framework once collected, and many species can be compared.

Eyes of different shapes are compared.

Weaknesses:

Detailed quantitative conclusions are not possible given the approximations and simplifying assumptions in the models and poor accounting for trends in the data across eye types.

Reviewer #1 (Recommendations For The Authors):

Figure 1: Panel E defines the parameters described in panel d. Consider swapping the order of those panels (or defining D and Delta Phi in the figure legend for d). Order follows narrative, eye types then match 

We think that you are referring to Figure 1. We modified the legend.

Lines 143-145: How does a different relative cost impact your results?

Thank you for raising this question. Because our assumption that relative costs are the same is our starting point, and for optics it is not an obvious mistake, we do not raise your question here. We address your question where you next raise it because, for photoreceptors the assumption is obviously wrong.  We now emphasise that our method for accounting for photoreceptor energy costs can be applied to other costs. 

Lines 187-190: Same as above - how do your results change if this assumption is not accurate?

We have revised our manuscript to emphasise that we are dealing with the situation in which our initial assumption (costs per unit volume are equal) breaks down. On (lines 203 - 208) we write “ However, this assumption breaks down when we consider specific metabolic rates. To enable and power phototransduction, photoreceptors have an exceptionally high specific metabolic rate (energy consumed per gram, and hence unit volume, per second) (Laughlin et al., 1998; Niven et al., 2007; Pangršič et al., 2005). We account for this extra cost by applying an energy surcharge, S_E. To equate…. 

We also revised part of the Discussion section, Specific volume is a useful measure of cost to make it clear that we are able take account for situations in which the costs per unit volume are not equal, and we give our treatment of photoreceptor energy costs as an example of how this is done. On lines 626 - 640 we say  

Cost estimates can be adjusted for situations in which costs per unit volume are not equal, as illustratedby our treatment of photoreceptor energy consumption.  To support transduction the photoreceptor array has an exceptionally high metabolic rate (Laughlin et al., 1998; Niven et al., 2007; Pangršič et al., 2005). We account forthis higher energy cost by using the animal’s specific metabolic rate (power per unit mass and hence power per unit volume) to convert an array’s power consumption into an equivalent volume (Methods). Photoreceptor ion pumps are the major consumers of energy and the smaller contribution of pigmented glia (Coles, 1989) is included in our calculation of the energy tariff K_E. (Methods) The higher costs of materials and their turnover in the photoreceptor array can be added the energy tariff K_E but given the magnitude of the light-gated current (Laughlin et al., 1998) the relative increase will be very small. Thus for our intents and purposes the effects of these additional costs are covered by our models. For want of sufficient data…”.

Reviewer #2 (Recommendations For The Authors):

A few comments for consideration by the authors:

(1) In the abstract, Maybe give another example explaining why other eyes should be different to those of fast diurnal insects.

This worthwhile extrapolation is best kept to the Discussion.

(2) Would it be worthwhile mentioning that the photopigment density is low in rhabdoms compared to vertebrate outer segments? This will have major effects on the relative size of retina and optics.

Thank you, we now make this good point in the Discussion (lines 698-702).

(3) It took me a while to understand what you mean by an energy tariff. For the less initiated reader many other variables may be difficult to comprehend. A possible remedy would be to make a table with all variables explained first very briefly in a formal way and then explained again with a few more words for readers less fluent in the formalism.

A very useful suggestion. We have taken your advice (p.4).

(4) The "easy explanation" on lines 356-357 need a few more words to be understandable.

We have expanded this argument, and corrected a mistake, the width of the head front to back is not 250 μm, it is 600 μm (lines 402-407)

(5) Maybe devote a short paragraph in the Discussion to other types of eye, such as optical superposition eyes and pinhole eyes. This could be done very shortly and without formalism. I'm sure the authors already have a good idea of the optimal ratio of receptor arrays and optics in these eye types.

We do not discuss this because we have not found a full account of the trade-offs and their  effects on costs and benefits. We hope that our analysis of apposition and simple eyes will encourage people to analyse the relationships between costs and benefits in other eye types. To this end we pointed out in the Discussion that recent advances in imaging and modelling could be helpful.

(6)  Could the sentence on lines 668-671 be made a little clearer?

“Efficiency is also depressed by increasing the photoreceptor energy tariff K_E, and in line with the greater impact of photoreceptor energy costs in simple eyes, the reduction in efficiency is much greater in simple eyes (Figure 8b).0.

We replaced this sentence with “In both simple and apposition eyes efficiency is reduced by increasing the photoreceptor energy tariff K_E. This effect is much greater in simple eyes, thus as found for reductions in photoreceptor length (Figure 7b),K_E has more impact on the design of simple eyes” (lines749 – 752).

(7)  I have some reservations about the text on lines 789-796. The problem is that optics can do very little to improve the performance of a directional photoreceptor where delrho should optimally be very wide. Here, membrane folding is the only efficient way to improve performance (SNR). The option to reduce delrho for better performance comes later when simultaneous spatial resolution (multiple pixels) is introduced.

Yes, we have been careless. We have rewritten this paragraph to say (lines 920-931)

“Two key steps in the evolution of eyes were the stacking of photoreceptive membranes to absorb more photons, and the formation of optics to intercept more photons and concentrate them according to angle of incidence to form an image (Nilsson, 2013, 2021). Our modelling of well-developed image forming eyes shows that to improve performance stacked membranes (rhabdomeres) compete with optics for the resources invested in an eye, and this competition profoundly influences both form and function. It is likely that competition between optics and photoreceptors was shaping eyes as lenses evolved to support low resolution spatial vision. Thus the developmental mechanisms that allocate resources within modern high resolution eyes (Casares & MacGregor, 2021), by controlling cell size and shape, and as our study emphasises, gradients in size and shape across an eye, will have analogues or homologues in more ancient eyes. Their discovery….” (lines 920-931

Reviewer #3 (Recommendations For The Authors):

Suggestions for major revisions:

While the approach is novel and elegant, the results from the analysis of insect morphology do not broadly support the optimization argument and hardly constrain parameters, like the energy tariff value, at all. The most striking result of the paper is the flat plateau in information across a broad range of shape parameters and the length, and resolution trend in Figure 5.

At no point in the Results and Discussion do we argue that resource allocation is optimized. Indeed, we frequently observe that it is not. Our mistake was to start the Abstract by observing that animals evolve to minimise costs. We have rewritten the Abstract accordingly.

The information peaks are quite shallow. This might actually be a very important and interesting result in the paper - the fact that the information plateaus could give the insect eye quite a wide range of parameters to slide between while achieving relatively efficient sensing of the environment. Instead of attempting to use a rather ad hoc and poorly supported measure of energetics in PR cost, perhaps the pitch could focus on this flexibility. K_E does not seem to constrain eye parameters and does not add much to the paper.

We agree, being able to construct performance surfaces across morphospace is an important advance in the field of eye design and evolution, and the performance surface’s flat top has interesting implications for the evolution of adaptations. Encouraged by your remarks, we have rewritten the Abstract and the introductory paragraph of the Discussion to draw attention to these points. 

We are disappointed that we failed to convince you that our energy tariff, K_E , is no better than a poorly supported ad hoc parameter that does not add much to the paper. In our opinion a resource allocation model that ignores photoreceptor energy consumption is obviously inadequate because the high energy cost of phototransduction is both wellknown and considered to be a formative factor in eye evolution (Niven and Laughlin, 2008). One of the advantages of modelling is that one can assess the impact of factors that are known to be present, are thought to be important, but have not been quantified. We followed standard modelling practice by introducing a cost that has the same units as the other costs and, for good physiological reasons, increases linearly with the number of microvilli, according to K_E. We then vary this unknown cost parameter to discover when and why it is significant. We were pleased to discover that we could combine data on photoreceptor energy demands and whole animal metabolic rates to establish the likely range of K_E. This procedure enabled us to unify the cost-benefit analyses of optics and photoreceptors, and to discover that realistic values of K_E have a profound impact on the structure and performance of an efficient eye. We hope that this advance will encourage people to collect the data needed to evaluate K_E.To emphasise the importance of K_E and dispel doubts associated with the failure of the model to fit the data, we have revised two sections:  Flies invest efficiently in costly photoreceptor arrays in the Results, and How efficiently do insects allocate resources within their apposition eyes?  in the Discussion. These rewrites also explain why it is impossible for us to infer K_E by adjusting its value so that the model’s predictions fit the data.

The graphics after Figure 3 are quite dense and hard to follow. None of the plateau extent shown in Fig 3 is carried through to the subsequent plots, which makes the conclusions drawn from these figures very hard to parse. If the peak information occurs on a flat plateau, it would be more helpful to see those ranges of parameters displayed in the figures.

Ideally one should do as you suggest and plot the extent of the plateau, but in our situation this is not very helpful. In the best data set, flies, optimised models predict D well, get close to ∆φ in larger eyes, and demonstrate that these optimum values are not very sensitive to K_E L is a different matter, it is very sensitive to K_E L which, as we show (and frequently remind) is poorly constrained by experimental data. The best we can do is estimate the envelope of L vs C_tot  curves, as defined by a plausible range of K_EL . Because most of the plateau boundaries you ask for will fall within this envelope, plotting them does little to clear the fog of uncertainty. We note that all three referees agree that our model can account for two robust trends, i) in apposition eyes L increase with optical resolving power and acuity, both within individual eyes and among eyes of different sizes, and ii) L is much longer is apposition eyes than in simple eyes. Nonetheless, the scatter of data points and their failure to fit creates a bad impression. We gave a number of reasons why the model does not fit the data points, but these were scattered throughout the Results and Discussion and, as referees 1 and 3 point out, this makes it difficult to draw convincing conclusions. To rectify this failing, we have rewritten two sections, in the Results Flies invest efficiently in costly photoreceptor arrays and in the Discussion, How efficiently do insects allocate resources within their apposition eyes?, to discuss these reasons en bloc, draw conclusions and suggest how better data and refinements to modelling could resolve these issues.  

Throughout the figures, the discontinuities in the optimal cuts through parameter space are not sufficiently explained.

We added a couple of sentences that address the “jumps” (lines 313 – 318)

None of the data seems to hug any of the optimal lines and only weakly follow the trends shown in the plots. This makes interpretation difficult for the reader and should be better explained. The text can be a little telegraphic in the Results after roughly page 10, and requires several readings to glean insight into the manuscript's conclusions.

We revised the Results section in which we compare the best data set, flies’  NS eyes with theoretical predictions, Flies invest efficiently in costly photoreceptor arrays,  to expand our interpretation of the data and clarify our arguments. The remaining sections have not been expanded. In the next section, which is on fused rhabdom apposition eyes, our interpretation of the scattering of data points follows the same line of argument. The remaining Results sections are entirely theoretical.  

Overall, the rough conclusions outlined in the Results seem moderately supported by the matches of the data to the optimal information transmission cuts through parameter space, but only weakly.

We agree, more data is required to test and refine our theoretical predictions.

The Discussion is long and well-argued, and contains the most cogent writing in the manuscript.

Thank you: this is most pleasing. We submitted our study to eLife because it allows longer Discussions, but we worried that ours was too long. However, we felt that our extensive Discussion was necessary for two reasons. First, we are introducing a new approach to understanding of eye design and evolution. Second, because the data on eye morphology and costs are limited, we had to make a number of assumptions and by discussing these, warts and all, we hoped to encourage experimentalists to gather more data and focus their efforts on the most revealing material.  

Minor comments:

We have acted upon most of your minor comments and we confine our remarks to our disagreements. We are grateful for your attention to details that we \textshould have picked up on.  

It's a more standard convention to say "cost-benefit" rather than with a colon. 

"equation" should be abbreviated "eq" or "eqn", never with a "t"

when referring to the work of van Hateren, quote the paper and the database using "van Hateren" not just "Hateren"

small latex note: use "\textit{SNR}" to get the proper formatting for those letters when in the math environment

Line 100-110: "f" is introduced, but only f' is referenced in the figure. This should be explained in order. d_rh is not included in the figure. Also in this section, d_rh/f is also referenced before \Delta \rho_rf, which is the same quantity, without explanation.  

Figure 1 shows eye structure and geometry. f’ is a lineal dimension of the eye but f is not, so f is not shown in Fig 1e. We eliminated the confusion surrounding ∆ρ_rh  by deleting “and changing the acceptance angle of the photoreceptive waveguide ∆ρ_rh (Snyder, 1979)”.  

Fig 1 caption: this says "From dorsal to ventral," then describes trends that run ventral to dorsal, which is a confusing typo.

Fig 3 - adding some data points to these plots might help the reader understand how (or if) K_E is constrained by the data.

It is not possible to add data points because to total cost, Ctot ,is unknown.

Fig 4c (and in other subplots): the jumps in L with C_tot could be explained better in the text - it wasn't clear to this reviewer why there are these discontinuities.

Dealt with in the revised text (lines  310-318).

Fig 4d: The caption for this subplot could be more clearly written.

We have rewritten the subscript for subplot 4d.

Fig 5 and other plots with data: please indicate which symbols are samples from the same species. This info is hard to reconstruct from the tables.

We have revised Figure 5 accordingly. Species were already indicated in Figure 6.

Line 328: missing equation number

Reviewer #3 (Public review):

Summary:

The manuscript by Qiu and co-workers describes the single-particle cryo-electron microscopy structures of various oligomeric states of the orphan GPCR, GPR3. It describes the monomeric and dimeric structure of a mutant of GPR3 with a modified G-protein complex (miniGs) and then builds on this work to attempt an inactive 'apo' dimer and an allosteric modulator (AF bound dimer structure, by using an ICL3 insertion and stabilizing FAB fragments.

In general, I'm supportive of the work done in this study, and it does indeed provide valuable insight into GPR3 function. It may be that dimerization of certain class A GPCRs may be a means of signalling regulation or perhaps even amplification. However, some of the interpretation of the single particle data needs some extra attention to strengthen the hypothesis presented in the manuscript.

Firstly, I want to thank the authors for providing the unfiltered half-maps and PDB models for careful assessment. During this review, I did my own post-processing of the half-maps and used the resultant maps for careful analysis of models.

So to begin, I understand that the authors didn't model any lipid in the binding orthosteric binding site in any of the maps, but it may be worthwhile to model something in there, as many readers only download coordinates and not the maps.

A more general point about all the maps. In no case were any focussed refinements carried out. As the point of this paper are some of the finer details between active and intermediate states and the effect of an allosteric modulator, masking out hypervariable portions of the structure and doing local Euler searches would most certainly provide richer insights of the details in GPR3 (especially as the BRIL:Fab structures are not of interest). And also, generally, no 3D-variability studies were performed to see if minor differences in, say, TM4/5/6 positions were due to large variation in the single particles or were a stable consensus position.

As for the PFK dimeric structure. It appears to be refined with C2 point group symmetry (which is not mentioned anywhere except in a tiny bit of text in a supplemental figure). Was this also calculated in C1 to assess if there is any difference in either GPR3 protomer? Also, how certain are the authors of the cholesterol positions at the bottom of TM4/5? At lower map thresholds in the PFK dimer structure, one of them appears to be continuous with the orthosteric lipid. It also appears that there are many unmodelled lipids in this structure, and only two were assigned as cholesterol. It appears that many of the unmodelled lipids are forming bridging connections between the GPR3 protomers. Also, it may be worthwhile to provide a table of the key interactions between the protomers (although I note that there was a figure highlighting them).

With the PFK monomer structure, there was weak density for the same cholesterol, which was not modelled in this one; perhaps some commentary on the authors' approach for deciding how to assign density would be helpful. It also appears that the refinement mask was probably a bit tight in this one (something that cryoSPARC is notorious for), and rerefining with a much looser mask around the TM domain may be helpful in resolving the inner lipid leaflet positions.

The Apo structure, I think, I have the most issues with. Firstly, it is not 'apo'. There is definitely unaccounted for density in the orthosteric site. Also, the structure definitely needs a bit more attention. Firstly, masking out the BRIL and FABs would be a good start in helping better resolve the TMD regions, and then even focussing on a single monomer to increase the map interpretability. My major problem here is that, if this is being called 'apo' and inactive, the map doesn't reflect this; also, the TM5/6 does not look to be in a fully inactive position. The map density (at least around one of the protomers) in this region looks to be poorly resolved, most likely due to averaging due to internal motion. I think some 3DVA is certainly warranted here to strengthen the hypothesis that they have solved an 'apo' inactive.

The AF (allosteric modulator) bound structure is of significantly better quality. But again, only AF is modelled, and no lipids are. How are the authors sure? Perhaps some focussed refinements (and changing the Euler Origin to centre it on the AF molecule could be a good start). To this reviewer, at least in one of the protomers, adjacent to the AF position, there is a density that looks very much like the allosteric modulator, so it could even be forming a bridging dimer. Also, some potential assignments of the lipids may enlighten some of the structure-activity relationship of this modulator, as it seems to make as many contacts with surrounding lipids as it does with TM4/5. Also, it may be worthwhile exploring carefully the 3DVA of this data. In our studies (Russel et al.), we noted that the orthosteric lipid appears to ratchet back-and-forth in concert with TM4/5 twisting. Perhaps in the AF bound structure, as it binds at the 'exit' site of the lipid, perhaps it is locking in a specific conformation.

Reviewer #3 (Public review):

Summary:

In their study McDermott et al. investigate the neurocomputational mechanism underlying sensory prediction errors. They contrast two accounts: representational sharpening and dampening. Representational sharpening suggests that predictions increase the fidelity of the neural representations of expected inputs, while representational dampening suggests the opposite (decreased fidelity for expected stimuli). The authors performed decoding analyses on EEG data, showing that first expected stimuli could be better decoded (sharpening), followed by a reversal during later response windows where unexpected inputs could be better decoded (dampening). These results are interpreted in the context of opposing process theory (OPT), which suggests that such a reversal would support perception to be both veridical (i.e., initial sharpening to increase the accuracy of perception) and informative (i.e., later dampening to highlight surprising, but informative inputs).

Strengths:

The topic of the present study is of significant relevance for the field of predictive processing. The experimental paradigm used by McDermott et al. is well designed, allowing the authors to avoid several common confounds in investigating predictions, such as stimulus familiarity and adaptation. The introduction of the manuscript provides a well written summery of the main arguments for the two accounts of interest (sharpening and dampening), as well as OPT. Overall, the manuscript serves as a good overview of the current state of the field.

Weaknesses:

In my opinion some details of the methods, results and manuscript raise some doubts about the reliability of the reported findings. Key concerns are:

(1) In the previous round of comments, I noted that: "I am not fully convinced that Figures 3A/B and the associated results support the idea that early learning stages result in dampening and later stages in sharpening. The inference made requires, in my opinion, not only a significant effect in one-time bin and the absence of an effect in other bins. Instead to reliably make this inference one would need a contrast showing a difference in decoding accuracy between bins, or ideally an analysis not contingent on seemingly arbitrary binning of data, but a decrease (or increase) in the slope of the decoding accuracy across trials. Moreover, the decoding analyses seem to be at the edge of SNR, hence making any interpretation that depends on the absence of an effect in some bins yet more problematic and implausible". The authors responded: "we fitted a logarithmic model to quantify the change of the decoding benefit over trials, then found the trial index for which the change of the logarithmic fit was < 0.1%. Given the results of this analysis and to ensure a sufficient number of trials, we focused our further analyses on bins 1-2". However, I do not see how this new analysis addresses the concern that the conclusion highlights differences in decoding performance between bins 1 and 2, yet no contrast between these bins are performed. While I appreciate the addition of the new model, in my current understanding it does not solve the problem I raised. I still believe that if the authors wish to conclude that an effect differs between two bins they must contrast these directly and/or use a different appropriate analysis approach.

Relatedly, the logarithmic model fitting and how it justifies the focus on analysis bin 1-2 needs to be explained better, especially the rationale of the analysis, the choice of parameters (e.g., why logarithmic, why change of logarithmic fit < 0.1% as criterion, etc), and why certain inferences follow from this analysis. Also, the reporting of the associated results seems rather sparse in the current iteration of the manuscript.

(2) A critical point the authors raise is that they investigate the buildup of expectations during training. They go on to show that the dampening effect disappears quickly, concluding: "the decoding benefit of invalid predictions [...] disappeared after approximately 15 minutes (or 50 trials per condition)". Maybe the authors can correct me, but my best understanding is as follows: Each bin has 50 trials per condition. The 2:1 condition has 4 leading images, this would mean ~12 trials per leading stimulus, 25% of which are unexpected, so ~9 expected trials per pair. Bin 1 represents the first time the participants see the associations. Therefore, the conclusion is that participants learn the associations so rapidly that ~9 expected trials per pair suffice to not only learn the expectations (in a probabilistic context) but learn them sufficiently well such that they result in a significant decoding difference in that same bin. If so, this would seem surprisingly fast, given that participants learn by means of incidental statistical learning (i.e. they were not informed about the statistical regularities). I acknowledge that we do not know how quickly the dampening/sharpening effects develop, however surprising results should be accompanied with a critical evaluation and exceptionally strong evidence (see point 1). Consider for example the following alternative account to explain these results. Category pairs were fixed across and within participants, i.e. the same leading image categories always predicted the same trailing image categories for all participants. Some category pairings will necessarily result in a larger representational overlap (i.e., visual similarity, etc.) and hence differences in decoding accuracy due to adaptation and related effects. For example, house  barn will result in a different decoding performance compared to coffee cup  barn, simply due to the larger visual and semantic similarity between house and barn compared to coffee cup and barn. These effects should occur upon first stimulus presentation, independent of statistical learning, and may attenuate over time e.g., due to increasing familiarity with the categories (i.e., an overall attenuation leading to smaller between condition differences) or pairs.

(3) In response to my previous comment, why the authors think their study may have found different results compared to multiple previous studies (e.g. Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011), particularly the sharpening to dampening switch, the authors emphasize the use of non-repeated stimuli (no repetition suppression and no familiarity confound) in their design. However, I fail to see how familiarity or RS could account for the absence of sharpening/dampening inversion in previous studies.

First, if the authors argument is about stimulus novelty and familiarity as described by Feuerriegel et al., 2021, I believe this point does not apply to the cited studies. Feuerriegel et al., 2021 note: "Relative stimulus novelty can be an important confound in situations where expected stimulus identities are presented often within an experiment, but neutral or surprising stimuli are presented only rarely", which indeed is a critical confound. However, none of the studies (Han et al., 2019; Richter et al., 2018; Kumar et al., 2017; Meyer and Olson, 2011) contained this confound, because all stimuli served as expected and unexpected stimuli, with the expectation status solely determined by the preceding cue. Thus, participants were equally familiar with the images across expectation conditions.

Second, for a similar reason the authors argument for RS accounting for the different results does not hold either in my opinion. Again, as Feuerriegel et al. 2021 correctly point out: "Adaptation-related effects can mimic ES when the expected stimuli are a repetition of the last-seen stimulus or have been encountered more recently than stimuli in neutral expectation conditions." However, it is critical to consider the precise design of previous studies. Taking again the example of Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011. To my knowledge none of these studies contained manipulations that would result in a more frequent or recent repetition of any specific stimulus in the expected compared to unexpected condition. The crucial manipulation in all these previous studies is not that a single stimulus or stimulus feature (which could be subject to familiarity or RS) determines the expectation status, but rather the transitional probability (i.e. cue-stimulus pairing) of a particular stimulus given the cue. Therefore, unless I am missing something critical, simple RS seems unlikely to differ between expectation condition in the previous studies and hence seems implausible to account for differences in results compared to the current study.

Moreover, studies cited by the authors (e.g. Todorovic & de Lange, 2012) showed that RS and ES are separable in time, again making me wonder how avoiding stimulus repetition should account for the difference in the present study compared to previous ones. I am happy to be corrected in my understanding, but with the currently provided arguments by the authors I do not see how RS and familiarity can account for the discrepancy in results.

I agree with the authors that stimulus familiarity is a clear difference compared to previous designs, but without a valid explanation why this should affect results I find this account rather unsatisfying. I see the key difference in that the authors manipulated category predictability, instead of exemplar prediction - i.e. searching for a car instead of your car. However, if results in support of OPT would indeed depend on using novel images (i.e. without stimulus repetition), would this not severely limit the scope of the account and hence also its relevance? Certainly, the account provided by the authors casts the net wider and tries to explain visual prediction. Relatedly, if OPT only applies during training, as the authors seem to argue, would this again not significantly narrow the scope of the theory? Combined these two caveats would seem to demote the account from a general account of prediction and perception to one about perception during very specific circumstances. In my understanding the appeal of OPT is that it accounts for multiple challenges faced by the perceptual system, elegantly integrating them into a cohesive framework. Most of this would be lost by claiming that OPT's primary prediction would only apply to specific circumstances - novel stimuli during learning of predictions. Moreover, in the original formulation of the account, as outlined by Press et al., I do not see any particular reason why it should be limited to these specific circumstances. This does of course not mean that the present results are incorrect, however it does require an adequate discussion and acknowledgement in the manuscript.

Impact:

McDermott et al. present an interesting study with potentially impactful results. However, given my concerns raised in this and the previous round of comments, I am not entirely convinced of the reliability of the results. Moreover, the difficulty of reconciling some of the present results with previous studies highlights the need for more convincing explanations of these discrepancies and a stronger discussion of the present results in the context of the literature.

Author response:

The following is the authors’ response to the original reviews

Public reviews:

Reviewer 1 (Public Review):

Many thanks for the positive and constructive feedback on the manuscript.

This study reveals a great deal about how certain neural representations are altered by expectation and learning on shorter and longer timescales, so I am loath to describe certain limitations as 'weaknesses'. But one limitation inherent in this experimental design is that, by focusing on implicit, task-irrelevant predictions, there is not much opportunity to connect the predictive influences seen at the neural level to the perceptual performance itself (e.g., how participants make perceptual decisions about expected or unexpected events, or how these events are detected or appear).

Thank you for the interesting comment. We now discuss the limitation of task-irrelevant prediction . In brief, some studies which showed sharpening found that task demands were relevant, while some studies which showed dampening were based on task-irrelevant predictions, but it is unlikely that task relevance - which was not manipulated in the current study - would explain the switch between sharpening and dampening that we observe within and across trials.

The behavioural data that is displayed (from a post-recording behavioural session) shows that these predictions do influence perceptual choice - leading to faster reaction times when expectations are valid. In broad strokes, we may think that such a result is broadly consistent with a 'sharpening' view of perceptual prediction, and the fact that sharpening effects are found in the study to be larger at the end of the task than at the beginning. But it strikes me that the strongest test of the relevance of these (very interesting) EEG findings would be some evidence that the neural effects relate to behavioural influences (e.g., are participants actually more behaviourally sensitive to invalid signals in earlier phases of the experiment, given that this is where the neural effects show the most 'dampening' a.k.a., prediction error advantage?)

Thank you for the suggestion. We calculated Pearson’s correlation coefficients for behavioural responses (difference in mean reaction times), neural responses during the sharpening effect (difference in decoding accuracy), and neural responses during the dampening effect for each participant, which resulted in null findings.

Reviewer 2 (Public Review):

Thank you for your helpful and constructive comments on the manuscript.

The strength in controlling for repetition effects by introducing a neutral (50% expectation) condition also adds a weakness to the current version of the manuscript, as this neutral condition is not integrated into the behavioral (reaction times) and EEG (ERP and decoding) analyses. This procedure remained unclear to me. The reported results would be strengthened by showing differences between the neutral and expected (valid) conditions on the behavioral and neural levels. This would also provide a more rigorous check that participants had implicitly learned the associations between the picture category pairings.

Following the reviewer's suggestion, we have included the neutral condition in the behavioural analysis and performed a repeated measures ANOVA on all three conditions.

It is not entirely clear to me what is actually decoded in the prediction condition and why the authors did not perform decoding over trial bins in prediction decoding as potential differences across time could be hidden by averaging the data. The manuscript would generally benefit from a more detailed description of the analysis rationale and methods.

In the original version of the manuscript, prediction decoding aimed at testing if the upcoming stimulus category can be decoded from the response to the preceding ( leading) stimulus. However, in response to the other Reviewers’ comments we have decided to remove the prediction decoding analysis from the revised manuscript as it is now apparent that prediction decoding cannot be separated from category decoding based on pixel information.

Finally, the scope of this study should be limited to expectation suppression in visual perception, as the generalization of these results to other sensory modalities or to the action domain remains open for future research.

We have clarified the scope of the study in the revised manuscipt .

Reviewer 3 (Public Review):

Thank you for the thought-provoking and interesting comments and suggestions.

(1) The results in Figure 2C seem to show that the leading image itself can only be decoded with ~33% accuracy (25% chance; i.e. ~8% above chance decoding). In contrast, Figure 2E suggests the prediction (surprisingly, valid or invalid) during the leading image presentation can be decoded with ~62% accuracy (50% chance; i.e. ~12% above chance decoding). Unless I am misinterpreting the analyses, it seems implausible to me that a prediction, but not actually shown image, can be better decoded using EEG than an image that is presented on-screen.

Following this and the remaining comments by the Reviewer (see below), we have decided to remove the prediction analysis from the manuscript. Specifically, we have focused on the Reviewer’s concern that it is implausible that image prediction would be better decoded that an image that is presented on-screen. This led us to perform a control analysis, in which we tried to decode the leading image category based on pixel values alone (rather than on EEG responses). Since this decoding was above chance, we could not rule out the possibility that EEG responses to leading images reflect physical differences between image categories. This issue does not extend to trailing images, as the results of the decoding analysis based on trailing images are based on accuracy comparisons between valid and invalid trials, and thus image features are counterbalanced. We would like to thank the Reviewer for raising this issue

(2) The "prediction decoding" analysis is described by the authors as "decoding the predictable trailing images based on the leading images". How this was done is however unclear to me. For each leading image decoding the predictable trailing images should be equivalent to decoding validity (as there were only 2 possible trailing image categories: 1 valid, 1 invalid). How is it then possible that the analysis is performed separately for valid and invalid trials? If the authors simply decode which leading image category was shown, but combine L1+L2 and L4+L5 into one class respectively, the resulting decoder would in my opinion not decode prediction, but instead dissociate the representation of L1+L2 from L4+L5, which may also explain why the time-course of the prediction peaks during the leading image stimulus-response, which is rather different compared to previous studies decoding predictions (e.g. Kok et al. 2017). Instead for the prediction analysis to be informative about the prediction, the decoder ought to decode the representation of the trailing image during the leading image and inter-stimulus interval. Therefore I am at present not convinced that the utilized analysis approach is informative about predictions.

In this analysis, we attempted to decode ( from the response to leading images) which trailing categories ought to be presented. The analysis was split between trials where the expected category was indeed presented (valid) vs. those in which it was not (invalid). The separation of valid vs invalid trials in the prediction decoding analysis served as a sanity check as no information about trial validity was yet available to participants. However, as mentioned above, we have decided to remove the “prediction decoding” analysis based on leading images as we cannot disentangle prediction decoding from category decoding.

(3) I may be misunderstanding the reported statistics or analyses, but it seems unlikely that >10  of the reported contrasts have the exact same statistic of Tmax= 2.76 . Similarly, it seems implausible, based on visual inspection of Figure 2, that the Tmax for the invalid condition decoding (reported as Tmax = 14.903) is substantially larger than for the valid condition decoding (reported as Tmax = 2.76), even though the valid condition appears to have superior peak decoding performance. Combined these details may raise concerns about the reliability of the reported statistics.

Thank you for bringing this to our attention. This copy error has now been rectified.

(4) The reported analyses and results do not seem to support the conclusion of early learning resulting in dampening and later stages in sharpening. Specifically, the authors appear to base this conclusion on the absence of a decoding effect in some time-bins, while in my opinion a contrast between time-bins, showing a difference in decoding accuracy, is required. Or better yet, a non-zero slope of decoding accuracy over time should be shown ( not contingent on post-hoc and seemingly arbitrary binning).

Thank you for the helpful suggestion. We have performed an additional analysis to address this issue, we calculated the trial-by-trial time-series of the decoding accuracy benefit for valid vs. invalid for each participant and averaged this benefit across time points for each of the two significant time windows. Based on this, we fitted a logarithmic model to quantify the change of this benefit over trials, then found the trial index for which the change of the logarithmic fit was < 0.1% (i.e., accuracy was stabilized). Given the results of this analysis and to ensure a sufficient number of trials, we focussed our further analyses on bins 1-2 to directly assess the effects of learning. This is explained in more detail in the revised manuscript .

(5) The present results both within and across trials are difficult to reconcile with previous studies using MEG (Kok et al., 2017; Han et al., 2019), single-unit and multi-unit recordings (Kumar et al., 2017; Meyer & Olson 2011), as well as fMRI (Richter et al., 2018), which investigated similar questions but yielded different results; i.e., no reversal within or across trials, as well as dampening effects with after more training. The authors do not provide a convincing explanation as to why their results should differ from previous studies, arguably further compounding doubts about the present results raised by the methods and results concerns noted above.

The discussion of these findings has been expanded in the revised manuscript . In short, the experimental design of the above studies did not allow for an assessment of these effects prior to learning. Several of them also used repeated stimuli (albeit some studies changed the pairings of stimuli between trials), potentially allowing for RS to confound their results.

Recommendations for the Authors:

Reviewer 1 (Recommendations for the authors):

(1) On a first read, I was initially very confused by the statement on p.7 that each stimulus was only presented once - as I couldn't then work out how expectations were supposed to be learned! It became clear after reading the Methods that expectations are formed at the level of stimulus category (so categories are repeated multiple times even if exemplars are not). I suspect other readers could have a similar confusion, so it would be helpful if the description of the task in the 'Results' section (e.g., around p.7) was more explicit about the way that expectations were generated, and the (very large) stimulus set that examples are being drawn from.

Following your suggestion, we have clarified the paradigm by adding details about the categories and the manner in which expectations are formed.

(2) p.23: the authors write that their 1D decoding images were "subjected to statistical inference amounting to a paired t-test between valid and invalid categories". What is meant by 'amounting to' here? Was it a paired t-test or something statistically equivalent? If so, I would just say 'subjected to a paired t-test' to avoid any confusion, or explaining explicitly which statistic inference was done over.

We have rephrased this as “subjected to (1) a one-sample t-test against chance-level, equivalent to a fixed-effects analysis, and (2) a paired t-test”.

Relatedly, this description of an analysis amounting to a 'paired t-test' only seems relevant for the sensory decoding and memory decoding analyses (where there are validity effects) rather than the prediction decoding analysis. As far as I can tell the important thing is that the expected image category can be decoded, not that it can be decoded better or worse on valid or invalid trials.

In the previous version of the manuscript, the comparison of prediction decoding between valid and invalid trials was meant as a sanity check. However, in response to the other Reviewers’ comments we have decided to remove the prediction decoding analysis from the revised manuscript due to confounds.

It would be helpful if authors could say a bit more about how the statistical inferences were done for the prediction decoding analyses and the 'condition against baseline' contrasts (e.g., when it is stated that decoding accuracy in valid trials *,in general,* is above 0 at some cluster-wise corrected value). My guess is that this amounts to something like a one-sample t-test - but it may be worth noting that one-sample t-tests on information measures like decoding accuracy cannot support population-level inference, because these measures cannot meaningfully be below 0 (see Allefeld et al, 2016).

When testing for decoding accuracy against baseline, we used one-sample t-tests against chance level (rather than against 0) throughout the manuscript. We now clarify in the manuscript that this corresponds to a fixed-effects analysis (Allefeld et al., 2016). In contrast, when testing for differences in decoding accuracy between valid and invalid conditions, we used paired-sample t-tests. As mentioned above, the prediction decoding analysis has been removed from the analysis.

(3) By design, the researchers focus on implicit predictive learning which means the expectations being formed are ( by definition) task-irrelevant. I thought it could be interesting if the authors might speculate in the discussion on how they think their results may or may not differ when predictions are deployed in task-relevant scenarios -  particularly given that some studies have found sharpening effects do not seem to depend on task demands ( e.g., Kok et al, 2012 ; Yon et al, 2018)  while other studies have found that some dampening effects do seem to depend on what the observer is attending to ( e.g., Richter et al, 2018) . Do these results hint at a possible explanation for why this might be? Even if the authors think they don't, it might be helpful to say so!

Thank you for the interesting comment. We have expanded on this in the revised manuscript.

Reviewer 2  (Recommendations for the authors):

Methods/results

(1) The goal of this study is the assessment of expectation effects during statistical learning while controlling for repetition effects, one of the common confounds in prediction suppression studies (see, Feuerriegel et al., 2021). I agree that this is an important aspect and I assume that this was the reason why the authors introduced the P=0.5 neutral condition (Figure 1B, L3). However, I completely missed the analyses of this condition in the manuscript. In the figure caption of Figure 1C, it is stated that the reaction times of the valid, invalid, and neutral conditions are shown, but only data from the valid and invalid conditions are depicted. To ensure that participants had built up expectations and had learned the pairing, one would not only expect a difference between the valid and invalid conditions but also between the valid and neutral conditions. Moreover, it would also be important to integrate the neutral condition in the multivariate EEG analysis to actually control for repetition effects. Instead, the authors constructed another control condition based on the arbitrary pairings. But why was the neutral condition not compared to the valid and invalid prediction decoding results? Besides this, I also suggest calculating the ERP for the neutral condition and adding it to Figure 2A to provide a more complete picture.

As mentioned above, we have included the neutral condition in the behavioural analysis, as outlined in the revised manuscript. We have also included a repeated measures ANOVA on all 3 conditions. The purpose of the neutral condition was not to avoid RS, but rather to provide a control condition. We avoided repetition by using individual, categorised stimuli. Figure 1C has been amended to include the neutral condition). In response to the remaining comments, we have decided to remove the prediction decoding analysis from the manuscript.

(2) One of the main results that is taken as evidence for the OPT is that there is higher decoding accuracy for valid trials (indicate sharpening) early in the trial and higher decoding accuracy for invalid trials (indicate dampening) later in the trial. I would have expected this result for prediction decoding that surprisingly showed none of the two effects. Instead, the result pattern occurred in sensory decoding only, and partly (early sharpening) in memory decoding. How do the authors explain these results? Additionally, I would have expected similar results in the ERP; however, only the early effect was observed. I missed a more thorough discussion of this rather complex result pattern. The lack of the opposing effect in prediction decoding limits the overall conclusion that needs to be revised accordingly.

Since sharpening vs. dampening rests on the comparison between valid and invalid trials, evidence for sharpening vs. dampening could only be obtained from decoding based on responses to trailing images. In prediction decoding (removed from the current version), information about the validity of the trial is not yet available. Thus, our original plan was to compare this analysis with the effects of validity on the decoding of trailing images (i.e. we expected valid trials to be decoded more accurately after the trailing image than before). The results of the memory decoding did mirror the sensory decoding of the trailing image in that we found significantly higher decoding accuracy of the valid trials from 123-180 ms. As with the sensory decoding, there was a tendency towards a later flip (280-296 ms) where decoding accuracy of invalid trials became nominally higher, but this effect did not reach statistical significance in the memory decoding.

(3) To increase the comprehensibility of the result pattern, it would be helpful for the reader to clearly state the hypotheses for the ERP and multivariate EEG analyses. What did you expect for the separate decoding analyses? How should the results of different decoding analyses differ and why? Which result pattern would (partly, or not) support the OPT?

Our hypotheses are now stated in the revised manuscript.

(4) I was wondering why the authors did not test for changes during learning for prediction decoding. Despite the fact that there were no significant differences between valid and invalid conditions within-trial, differences could still emerge when the data set is separated into bins. Please test and report the results.

As mentioned above, we have decided to remove the prediction decoding analysis from the current version of the manuscript.

(5) To assess the effect of learning the authors write: 'Given the apparent consistency of bins 2-4, we focused our analyses on bins 1-2.' Please explain what you mean by 'apparent consistency'. Did you test for consistency or is it based on descriptive results? Why do the authors not provide the complete picture and perform the analyses for all bins? This would allow for a better assessment of changes over time between valid and invalid conditions. In Figure 3, were valid and invalid trials different in any of the QT3 or QT4 bins in sensory or memory encoding?

We have performed an additional analysis to address this issue. The reasoning behind the decision to focus on bins 1-2 is now explained in the revised manuscript. In short, fitting a learning curve to trial-by-trial decoding estimates indicates that decoding stabilizes within <50% of the trials. To quantify changes in decoding occurring within these <50% of the trials while ensuring a sufficient number of trials for statistical comparisons, we decided to focus on bins 1-2 only.

(6) Please provide the effect size for all statistical tests.

Effect sizes have now been provided.

(7) Please provide exact p-values for non-significant results and significant results larger than 0.001.

Exact p-values have now been provided.

(8) Decoding analyses: I suppose there is a copy/paste error in the T-values as nearly all T-values on pages 11 and 12 are identical (2.76) leading to highly significant p-values (0.001) as well as non-significant effects (>0.05). Please check.

Thank you for bringing this to our attention. This error has now been corrected.

(9) Page 12:  There were some misleading phrases in the result section. To give one example: 'control analyses was slightly above change' - this sounds like a close to non-significant effect, but it was indeed a highly significant effect of p<0.001. Please revise.

This phrase was part of the prediction decoding analysis and has therefore been removed.

(10) Sample size: How was the sample size of the study be determined (N=31)? Why did only a subgroup of participants perform the behavioral categorization task after the EEG recording? With a larger sample, it would have been interesting to test if participants who showed better learning (larger difference in reaction times between valid and invalid conditions) also showed higher decoding accuracies.

This has been clarified in the revised manuscript. In short, the larger sample size of N=31 was based on previous research; ten participants were initially tested as part of a pilot which was then expanded to include the categorisation task.

(11) I assume catch trials were removed before data analyses?

We have clarified that catch trials were indeed removed prior to analyses.

(12) Page 23, 1st line: 'In each, the decoder...' Something is missing here.

Thank you for bringing this to our attention, this sentence has now been rephrased as “In both valid and invalid analyses” in the revised manuscript.

Discussion

(1) The analysis over multiple trials showed dampening within the first 15 min followed by sharpening. I found the discussion of this finding very lengthy and speculative (page 17). I recommend shortening this part and providing only the main arguments that could stimulate future research.

Thank you for the suggestion. Since Reviewer 3 has requested additional details in this part of the discussion, we have opted to keep this paragraph in the manuscript. However, we have also made it clearer that this section is relatively speculative and the arguments provided for the across trials dynamics are meant to stimulate further research.

(2) As this task is purely perceptual, the results support the OPT for the area of visual perception. For action, different results have been reported. Suppression within-trial has been shown to be larger for expected than unexpected features of action targets and suppression even starts before the start of the movement without showing any evidence for sharpening ( e.g., Fuehrer et al., 2022, PNAS). For suppression across trials, it has been found that suppression decreases over the course of learning to associate a sensory consequence to a specific action (e.g., Kilteni et al., 2019, ELife). Therefore, expectation suppression might function differently in perception and action (an area that still requires further research). Please clarify the scope of your study and results on perceptual expectations in the introduction, discussion, and abstract.

We have clarified the scope of the study in the revised manuscript.

Figures

(1) Figure 1A: Add 't' to the arrow to indicate time.

This has been rectified.

(2) Figure 3:  In the figure caption, sensory and memory decoding seem to be mixed up. Please correct. Please add what the dashed horizontal line indicates.

Thank you for bringing this to our attention, this has been rectified.

Reviewer 3  (Recommendations for the authors):

I applaud the authors for a well-written introduction and an excellent summary of a complicated topic, giving fair treatment to the different accounts proposed in the literature. However, I believe a few additional studies should be cited in the Introduction, particularly time-resolved studies such as Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011. This would provide the reader with a broader picture of the current state of the literature, as well as point the reader to critical time-resolved studies that did not find evidence in support of OPT, which are important to consider in the interpretation of the present results.

The introduction has been expanded to include the aforementioned studies in the revised manuscript.

Given previous neuroimaging studies investigating the present phenomenon, including with time-resolved measures (e.g. Kok et al., 2017; Han et al., 2019; Kumar et al., 2017; Meyer & Olson 2011), why do the authors think that their data, design, or analysis allowed them to find support for OPT but not previous studies? I do not see obvious modifications to the paradigm, data quantity or quality, or the analyses that would suggest a superior ability to test OPT predictions compared to previous studies. Given concerns regarding the data analyses (see points below), I think it is essential to convincingly answer this question to convince the reader to trust the present results.

The most obvious alteration to the paradigm is the use of non-repeated stimuli. Each of the above time-resolved studies utilised repeated stimuli (either repeated, identical stimuli, or paired stimuli where pairings are changed but the pool of stimuli remains the same), allowing for RS to act as a confound as exemplars are still presented multiple times. By removing this confound, it is entirely plausible that we may find different time-resolved results given that it has been shown that RS and ES are separable in time (Todorovic & de Lange, 2012). We also test during learning rather than training participants on the task beforehand. By foregoing a training session, we are better equipped to assess OPT predictions as they emerge. In our across-trial results, learning appears to take place after approximately 15 minutes or 432 trials, at which point dampening reverses to sharpening. Had we trained the participants prior to testing, this effect would have been lost.

What is actually decoded in the "prediction decoding" analysis? The authors state that it is "decoding the predictable trailing images based on the leading images" (p.11). The associated chance level (Figure 2E) is indicated as 50%. This suggests that the classes separated by the SVM are T6 vs T7. How this was done is however unclear. For each leading image decoding the predictable trailing images should be equivalent to decoding validity (as there are only 2 possible trailing images, where one is the valid and the other the invalid image). How is it then possible that the analysis is performed separately for valid and invalid trials? Are the authors simply decoding which leading image was shown, but combine L1+L2 and L4+L5 into one class respectively? If so, this needs to be better explained in the manuscript. Moreover, the resulting decoder would in my opinion not decode the predicted image, but instead learn to dissociate the representation of L1+L2 from L4+L5, which may also explain why the time course of the prediction peaks during the leading image stimulus-response, which is rather different compared to previous studies decoding (prestimulus) predictions (e.g. Kok et al. 2017). If this is indeed the case, I find it doubtful that this analysis relates to prediction. Instead for the prediction analysis to be informative about the predicted image the authors should, in my opinion, train the decoder on the representation of trailing images and test it during the prestimulus interval.

As mentioned above, the prediction decoding analysis has been removed from the manuscript. The prediction decoding analysis was intended as a sanity check, as validity information was not yet available to participants.

Related to the point above, were the leading/trailing image categories and their mapping to L1, L2, etc. in Figure 1B fixed across subjects? I.e. "'beach' and 'barn' as 'Leading' categories would result in 'church' as a 'Trailing' category with 75% validity" (p.20) for all participants? If so, this poses additional problems for the interpretation of the analysis discussed in the point above, as it may invalidate the control analyses depicted in Figure 2E, as systematic differences and similarities in the leading image categories could account for the observed results.

Image categories and their mapping were indeed fixed across participants. While this may result in physical differences and similarities between images influencing results, counterbalancing categories across participants would not have addressed this issue. For example, had we swapped “beach” with “barn” in another participant, physical differences between images may still be reflected in the prediction decoding. On the other hand, counterbalancing categories across trials was not possible given our aim of examining the initial stages of learning over trials. Had we changed the mappings of categories throughout the experiment for each participant, we would have introduced reversal learning and nullified our ability to examine the initial stages of learning under flat priors. In any case, the prediction decoding analysis has been removed from the manuscript, as outlined above.

Why was the neutral condition L3 not used for prediction decoding? After all, if during prediction decoding both the valid and invalid image can be decoded, as suggested by the authors, we would also expect significant decoding of T8/T9 during the L3 presentation.

In the neutral condition, L3 was followed by T8 vs. T9 with 50% probability, precluding prediction decoding. While this could have served as an additional control analysis for EEG-based decoding, we have opted for removing prediction decoding from the analysis. However, in response to the other Reviewers’ comments, the neutral condition has now been included in the behavioral analysis.

The following concern may arise due to a misunderstanding of the analyses, but I found the results in Figures 2C and 2E concerning. If my interpretation is correct, then these results suggest that the leading image itself can only be decoded with ~33% accuracy (25% chance; i.e. ~8% above chance decoding). In contrast, the predicted (valid or invalid) image during the leading image presentation can be decoded with ~62% accuracy (50% chance; i.e. ~12% above chance decoding). Does this seem reasonable? Unless I am misinterpreting the analyses, it seems implausible to me that a prediction but not actually shown image can be better decoded than an on-screen image. Moreover, to my knowledge studies reporting decoding of predictions can (1) decode expectations just above chance level (e.g. Kok et al., 2017; which is expected given the nature of what is decoded) and (2) report these prestimulus effects shortly before the anticipated stimulus onset, and not coinciding with the leading image onset ~800ms before the predicted stimulus onset. For the above reasons, the key results reported in the present manuscript seem implausible to me and may suggest the possibility of problems in the training or interpretation of the decoding analysis. If I misunderstood the analyses, the analysis text needs to be refined. If I understood the analyses correctly, at the very least the authors would need to provide strong support and arguments to convince the reader that the effects are reliable (ruling out bias and explaining why predictions can be decoded better than on-screen stimuli) and sensible (in the context of previous studies showing different time-courses and results).

As explained above, we have addressed this concern by performing an additional analysis, implementing decoding based on image pixel values. Indeed we could not rule out the possibility that “prediction” decoding reflected stimulus differences between leading images.

Relatedly, the authors use the prestimulus interval (-200 ms to 0 ms before predicted stimulus onset) as the baseline period. Given that this period coincides with prestimulus expectation effects ( Kok et al., 2017) , would this not result in a bias during trailing image decoding? In other words, the baseline period would contain an anticipatory representation of the expected stimulus ( Kok et al., 2017) , which is then subtracted from the subsequent EEG signal, thereby allowing the decoder to pick up on this "negative representation" of the expected image. It seems to me that a cleaner contrast would be to use the 200ms before leading image onset as the baseline.

The analysis of trailing images aimed at testing specific hypotheses related to differences between decoding accuracy in valid vs. invalid trials. Since the baseline was by definition the same for both kinds of trials (since information about validity only appears at the onset of the trailing image), changing the baseline would not affect the results of the analysis. Valid and invalid trials would have the same prestimulus effect induced by the leading image.

Again, maybe I misunderstood the analyses, but what exactly are the statistics reported on p. 11 onward? Why is the reported Tmax identical for multiple conditions, including the difference between conditions? Without further information this seems highly unlikely, further casting doubts on the rigor of the applied methods/analyses. For example: "In the sensory decoding analysis based on leading images, decoding accuracy was above chance for both valid (Tmax= 2.76, pFWE < 0.001) and invalid trials (Tmax= 2.76, pFWE < 0.001) from 100 ms, with no significant difference between them (Tmax= 2.76, pFWE > 0.05) (Fig. 2C)" (p.11).

Thank you for bringing this to our attention. As previously mentioned, this copy error has been rectified in the revised manuscript.

Relatedly, the statistics reported below in the same paragraph also seem unusual. Specifically, the Tmax difference between valid and invalid conditions seems unexpectedly large given visual inspection of the associated figure: "The decoding accuracy of both valid (Tmax = 2.76, pFWE < 0.001) and invalid trials (Tmax = 14.903, pFWE < 0.001)" (p.12). In fact, visual inspection suggests that the largest difference should probably be observed for the valid not invalid trials (i.e. larger Tmax).

This copy error has also been rectified in the revised manuscript.

Moreover, multiple subsequent sections of the Results continue to report the exact same Tmax value. I will not list all appearances of "Tmax = 2.76" here but would recommend the authors carefully check the reported statistics and analysis code, as it seems highly unlikely that >10 contrasts have exactly the same Tmax. Alternatively, if I misunderstand the applied methods, it would be essential to better explain the utilized method to avoid similar confusion in prospective readers.

This error has also now been rectified. As mentioned above the prediction decoding analysis has been removed.

I am not fully convinced that Figures 3A/B and the associated results support the idea that early learning stages result in dampening and later stages in sharpening. The inference made requires, in my opinion, not only a significant effect in one-time bin and the absence of an effect in other bins. Instead to reliably make this inference one would need a contrast showing a difference in decoding accuracy between bins, or ideally an analysis not contingent on seemingly arbitrary binning of data, but a decrease ( or increase) in the slope of the decoding accuracy across trials. Moreover, the decoding analyses seem to be at the edge of SNR, hence making any interpretation that depends on the absence of an effect in some bins yet more problematic and implausible.

Thank you for the helpful suggestion. As previously mentioned we fitted a logarithmic model to quantify the change of the decoding benefit over trials, then found the trial index for which the change of the logarithmic fit was < 0.1 %. Given the results of this analysis and to ensure a sufficient number of trials, we focussed our further analyses on bins 1-2 . This is explained in more detail in the revised manuscript.

Relatedly, based on the literature there is no reason to assume that the dampening effect disappears with more training, thereby placing more burden of proof on the present results. Indeed, key studies supporting the dampening account (including human fMRI and MEG studies, as well as electrophysiology in non-human primates) usually seem to entail more learning than has occurred in bin 2 of the present study. How do the authors reconcile the observation that more training in previous studies results in significant dampening, while here the dampening effect is claimed to disappear with less training?

The discussion of these findings has been expanded on in the revised manuscript. As previously outlined, many of the studies supporting dampening did not explicitly test the effect of learning as they emerge, nor did they control for RS to the same extent.

The Methods section is quite bare bones. This makes an exact replication difficult or even impossible. For example, the sections elaborating on the GLM and cluster-based FWE correction do not specify enough detail to replicate the procedure. Similarly, how exactly the time points for significant decoding effects were determined is unclear (e.g., p. 11). Relatedly, the explanation of the decoding analysis, e.g. the choice to perform PCA before decoding, is not well explained in the present iteration of the manuscript. Additionally, it is not mentioned how many PCs the applied threshold on average resulted in.

Thank you for this suggestion, we have described our methods in more detail.

To me, it is unclear whether the PCA step, which to my knowledge is not the default procedure for most decoding analyses using EEG, is essential to obtain the present results. While PCA is certainly not unusual, to my knowledge decoding of EEG data is frequently performed on the sensor level as SVMs are usually capable of dealing with the (relatively low) dimensionality of EEG data. In isolation this decision may not be too concerning, however, in combination with other doubts concerning the methods and results, I would suggest the authors replicate their analyses using a conventional decoding approach on the sensory level as well.

Thank you for this suggestion, we have explained our decision to use PCA in the revised manuscript.

Several choices, like the binning and the focus on bins 1-2 seem rather post-hoc. Consequently, frequentist statistics may strictly speaking not be appropriate. This further compounds above mentioned concerns regarding the reliability of the results.

The reasoning behind our decision to focus on bins 1-2 is now explained in more detail in the revised manuscript.

A notable difference in the present study, compared to most studies cited in the introduction motivating the present experiment, is that categories instead of exemplars were predicted.

This seems like an important distinction to me, which surprisingly goes unaddressed in the Discussion section. This difference might be important, given that exemplar expectations allow for predictions across various feature levels (i.e., even at the pixel level), while category predictions only allow for rough (categorical) predictions.

The decision to use categorical predictions over exemplars lies in the issue of RS, as it is impossible to control for RS while repeating stimuli over many trials. This has been discussed in more detail in the revised manuscript.

While individually minor problems, I noticed multiple issues across several figures or associated figure texts. For example: Figure 1C only shows valid and invalid trials, but the figure text mentions the neutral condition. Why is the neutral condition not depicted but mentioned here? Additionally, the figure text lacks critical information, e.g. what the asterisk represents. The error shading in Figure 2 would benefit from transparency settings to not completely obscure the other time-courses. Increasing the figure content and font size within the figure (e.g. axis labels) would also help with legibility (e.g. consider compressing the time-course but therefore increasing the overall size of the figure). I would also recommend using more common methods to indicate statistical significance, such as a bar at the bottom of the time-course figure typically used for cluster permutation results instead of a box. Why is there no error shading in Figure 2A but all other panels? Fig 2C-F has the y-axis label "Decoding accuracy (%)" but certainly the y-axis, ranging roughly from 0.2 to 0.7, is not in %. The Figure 3 figure text gives no indication of what the error bars represent, making it impossible to interpret the depicted data. In general, I would recommend that the authors carefully revisit the figures and figure text to improve the quality and complete the information.

Thank you for the suggestions. Figure 1C now includes the neutral condition. Asterisks denote significant results. The font size in Figure 2C-E has been increased. The y-axis on Figure 2C-E has been amended to accurately reflect decoding accuracy in percentage. Figure 2A has error shading, however, the error is sufficiently small that the error shading is difficult to see. The error bars in Figure 3 have been clarified.

Given the choice of journal (eLife), which aims to support open science, I was surprised to find no indication of (planned) data or code sharing in the manuscript.

Plans for sharing code/data are now outlined in the revised manuscript.

While it is explained in sufficient detail later in the Methods section, it was not entirely clear to me, based on the method summary at the beginning of the Results section, whether categories or individual exemplars were predicted. The manuscript may benefit from clarifying this at the start of the Results section.

Thank you for this suggestion, following this and suggestions from other reviewers, the experimental paradigm and the mappings between categories has been further explained in the revised manuscript, to make it clearer that predictions are made at the categorical level.

"Unexpected trials resulted in a significantly increased neural response 150 ms after image onset" (p.9). I assume the authors mean the more pronounced negative deflection here. Interpreting this, especially within the Results section as "increased neural response" without additional justification may stretch the inferences we can make from ERP data; i.e. to my knowledge more pronounced ERPs could also reflect increased synchrony. That said, I do agree with the authors that it is likely to reflect increased sensory responses, it would just be useful to be more cautious in the inference.

Thank you for the interesting comment, this has been rephrased as a “more pronounced negative deflection” in the revised manuscript.

Why was the ERP analysis focused exclusively on Oz? Why not a cluster around Oz? For object images, we may expect a rather wide dipole.

Feuerriegel et al (2021) have outlined issues questioning the robustness of univariate analyses for ES, as such we opted for a targeted ROI approach on the channel showing peak amplitude of the visually evoked response (Fig. 2B). More details on this are in the revised manuscript.           

How exactly did the authors perform FWE? The description in the Method section does not appear to provide sufficient detail to replicate the procedure.

FWE as implemented in SPM is a cluster-based method of correcting for multiple comparisons using random field theory. We have explained our thresholding methods in more detail in the revised manuscript.

If I misunderstand the authors and they did indeed perform standard cluster permutation analyses, then I believe the results of the timing of significant clusters cannot be so readily interpreted as done here (e.g. p.11-12); see: Maris & Oostenveld 2007; Sassenhagen & Dejan 2019.

All statistics were based on FWE under random field theory assumptions (as implemented in SPM) rather than on cluster permutation tests (as implemented in e.g.  Fieldtrip)

Why did the authors choose not to perform spatiotemporal cluster permutation for the ERP results?

As mentioned above, we opted to target our ERP analyses on Oz due to controversies in the literature regarding univariate effects of ES (Feuerriegel et al., 2021).

Some results, e.g. on p.12 are reported as T29 instead of Tmax. Why?

As mentioned above, prediction decoding analyses have been removed from the manuscript.

Author Response:

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

Reviewer #1 (Public review): 

Summary: 

The paper by Lee and Ouellette explores the role of cyclic-d-AMP in chlamydial developmental progression. The manuscript uses a collection of different recombinant plasmids to up- and down-regulate cdAMP production, and then uses classical molecular and microbiological approaches to examine the effects of expression induction in each of the transformed strains. 

Strengths: 

This laboratory is a leader in the use of molecular genetic manipulation in Chlamydia trachomatis and their efforts to make such efforts mainstream is commendable. Overall, the model described and defended by these investigators is thorough and significant.

Thank you for these comments.

Weaknesses: 

The biggest weakness in the document is their reliance on quantitative data that is statistically not significant, in the interpretation of results. These challenges can be addressed in a revision by the authors. 

Thank you for these comments. We point out that, while certain RT-qPCR data may not be statistically significant, our RNAseq data indicate late genes are, as a group, statistically significantly increased when increasing c-di-AMP levels and decreased when decreasing c-di-AMP levels. We do not believe running additional experiments to “achieve” statistical significance in the RT-qPCR data is worthwhile. We hope the reviewer agrees with this assessment.

We have also included new data in this revised manuscript, which we believe further strengthens aspects of the conclusions linked to individual expression of full-length DacA isoforms. We have also quantified inclusion areas and bacterial sizes for critical strains.

Reviewer #2 (Public review): 

Summary: 

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. Chlamydia are obligate intracellular bacterial pathogens that rely on eukaryotic host cells for growth. The chlamydial life cycle depends on a cell form developmental cycle that produces phenotypically distinct cell forms with specific roles during the infectious cycle. The RB cell form replicates amplifying chlamydia numbers while the EB cell form mediates entry into new host cells disseminating the infection to new hosts. Regulation of cell form development is a critical question in chlamydia biology and pathogenesis. Chlamydia must balance amplification (RB numbers) and dissemination (EB numbers) to maximize survival in its infection niche. The main findings In this manuscript show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of the transitionary gene hctA and late gene omcB. The authors also knocked down the expression of the dacA-ybbR operon and reported a reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion. Overall, this is a very intriguing study with important implications however the data is very preliminary and the model is very rudimentary and is not well supported by the data. 

Thank you for your comments. Chlamydia is not an easy experimental system, but we have done our best to address the reviewer’s concerns in this revised submission.

Describing the significance of the findings: 

The findings are important and point to very exciting new avenues to explore the important questions in chlamydial cell form development. The authors present a model that is not quantified and does not match the data well. 

Describing the strength of evidence: 

The evidence presented is incomplete. The authors do a nice job of showing that overexpression of the dacA-ybbR operon increases c-di-AMP and that knockdown or overexpression of the catalytically dead DacA protein decreases the c-di-AMP levels. However, the effects on the developmental cycle and how they fit the proposed model are less well supported. 

dacA-ybbR ectopic expression: 

For the dacA-ybbR ectopic expression experiments they show that hctA is induced early but there is no significant change in OmcB gene expression. This is problematic as when RBs are treated with Pen (this paper) and (DOI 10.1128/MSYSTEMS.00689-20) hctA is expressed in the aberrant cell forms but these forms do not go on to express the late genes suggesting stress events can result in changes in the developmental expression kinetic profile. The RNA-seq data are a little reassuring as many of the EB/Late genes were shown to be upregulated by dacA-ybbR ectopic expression in this assay.

As the reviewer notes, we also generated RNAseq data, which validates that late gene transcripts (including sigma28 and sigma54 regulated genes) are statistically significantly increased earlier in the developmental cycle in parallel to increased c-di-AMP levels. The lack of statistical significance in the RT-qPCR data for omcB, which shows a trend of higher transcripts, is less concerning given the statistically significantly RNAseq dataset. We have reported the data from three replicates for the RT-qPCR and do not think it would be worthwhile to attempt more replicates in an attempt to “achieve” statistical significance.

We recognize that hctA may also increase during stress as noted by the Grieshaber Lab. In re-evaluating these data, we decided to remove the Penicillin-linked studies from the manuscript since they detract from the focus of the story we are trying to tell given the potential caveat the reviewer mentions.

The authors also demonstrate that this ectopic expression reduces the overall growth rate but produces EBs earlier in the cycle but overall fewer EBs late in the cycle. This observation matches their model well as when RBs convert early there is less amplification of cell numbers. 

dacA knockdown and dacA(mut) 

The authors showed that dacA knockdown and ectopic expression of the dacA mutant both reduced the amount of c-di-AMP. The authors show that for both of these conditions, hctA and omcB expression is reduced at 24 hpi. This was also partially supported by the RNA-seq data for the dacA knockdown as many of the late genes were downregulated. However, a shift to an increase in RB-only genes was not readily evident. This is maybe not surprising as the chlamydial inclusion would just have an increase in RB forms and changes in cell form ratios would need more time points.

Thank you for this comment. We agree that it is not surprising given the shift in cell forms. The reduction in hctA transcripts argues against a stress state as noted above by the reviewer, and the RNAseq data from dacA-KD conditions indicates at least that secondary differentiation has been delayed. We agree that more time points would help address the reviewer’s point, but the time and cost to perform such studies is prohibitive with an obligate intracellular bacterium.

Interestingly, the overall growth rate appears to differ in these two conditions, growth is unaffected by dacA knockdown but is significantly affected by the expression of the mutant. In both cases, EB production is repressed. The overall model they present does not support this data well as if RBs were blocked from converting into EBs then the growth rate should increase as the RB cell form replicates while the EB cell form does not. This should shift the population to replicating cells. 

We agree that it seems that perturbing c-di-AMP production by knockdown or overexpressing the mutant DacA(D164N) has different impacts on chlamydial growth. We have generated new data, which we believe addresses this. Overexpressing membrane-localized DacA isoforms is clearly detrimental to chlamydiae as noted in the manuscript. However, when we removed the transmembrane domain and expressed N-terminal truncations of these isoforms, we observed no effects of overexpression on chlamydial morphology or growth. Importantly, for the wild-type full-length or truncated isoforms, overexpressing each resulted in the same level of c-di-AMP production, further supporting that the negative effect of overexpressing the wild-type full-length is linked to its membrane localization and not c-di-AMP levels. These data have been included as new Figure 3. These data indicate that too much DacA in the membrane is disruptive and suggest that the balance of DacA to YbbR is important since overexpression of both did not result in the same phenotype. This is further described in the Discussion.

As it relates to knockdown of dacA-ybbR, we have essentially removed/reduced the amount of these proteins from the membrane and have blocked the production of c-di-AMP. This is fundamentally different from overexpression.

Overall this is a very intriguing finding that will require more gene expression data, phenotypic characterization of cell forms, and better quantitative models to fully interpret these findings. 

Reviewer #1 (Recommendations for the authors): 

There is a generally consistent set of experiments conducted with each of the mutant strains, allowing a straightforward examination of the effects of each transformant. There are a few general and specific things that need to be addressed for both the benefit of the reader and the accuracy of interpretation. The following is a list of items that need to be addressed in the document, with an overall goal of making it more readable and making the interpretations more quantitatively defended. 

Specific comments: 

(1) The manuscript overall is wordy and there are quite a few examples of text in the results that should be in the discussion (examples include lines 224-225, 248-262, 282-288, 304-308) the manuscript overall could use a careful editing for verbosity. 

Thank you for this comment. We have removed some of the indicated sentences. However, to maintain the flow and logic of the manuscript, some statements may have been preserved to help transition between sections. As far as verbosity, we have tried to be as clear as possible in our descriptions of the results to minimize ambiguity. Others who read our manuscript appreciated the thoroughness of our descriptions.

(2) There is also a trend in the document to base fact statements on qualitative and quantitative differences that do not approach statistical significance. Examples of this include the following: lines 156-158, 190-192, 198-199, 230-232, 239-242, 292-293). This is something the authors need to be careful about, as these different statistically insignificant differences may tend to multiply a degree of uncertainty across the entire manuscript. 

We have quantified inclusion areas and tried to remove instances of qualitative assessments as noted by the reviewer. In regards to some of the transcripts, we can only report the data as they are. In some cases, there are trends that are not statistically significant, but it would seem to be inaccurate to state that they were unchanged. In other cases, a two-fold or less difference in transcript levels may be statistically significant but biologically insignificant. A reader can and should make their own conclusions.

(3) Any description of inclusion or RB size being modestly different needs to be defended with microscopic quantification. 

We have quantified inclusion areas and RB sizes and tried to remove instances of qualitative assessments as noted by the reviewer.

(4) It would be very helpful to reviewers if there was a figure number added to each figure in the reviewer-delivered text. 

Added.

(5) Figure 1A: This should indicate that the genes indicated beneath each developmental form are on high (I think that is what that means). 

We have reorganized Figure 1 to better improve the flow.

(6) Figure 1B is exactly the same as the three images in Figure 8B. I would delete this in Figure 1. This relates to comment 9. 

We presented this intentionally to clearly illustrate to the reader, who may not be knowledgeable in this area, what we propose is happening in the various strains. As such, we respectfully disagree and have left this aspect of the figure unchanged.

(7) Figure 1D: It is not clear if the period in E.V has any meaning. I think this is just a typo. Also, the color coding needs to be indicated here. What do the gray bars represent? The labeling for the gene schematic for dacA-KDcom should not be directly below the first graph in D. This makes the reader think this is a label for the graph. This can be accomplished if the image in panel B is removed and the first graph in panel D is moved into B. This will make a better figure. 

We have reorganized Figure 1 to better improve the flow.

(8) Figure 2 C, G: The utility of these panels is not clear. For them to have any value, they need to be expressed in genome copies. If they are truly just a measure of chlamydia genomic DNA, they have minimal utility to the reader. There are similar panels in several other figures. 

We have reported genome copies as suggested in lieu of ng gDNA for these measurements. Importantly, it does not alter any interpretations.

(9) I am not sure about the overall utility of Figure 8. Granted, a summary of their model is useful, but the cartoons in the figure are identical or very nearly identical to model figures shown in two other publications from the same group (PMID: 39576108, 39464112) These are referenced at least tangentially in the current manuscript (Jensen paper- now published- and ref 53). Because the model has been published before, if they are to be included, there needs to be a direct comparison of the results in each of these three papers, as they basically describe the same developmental process. The model images should also be referenced directly to the first of the other papers.

This was intentional so that readers familiar with our work will see the similarities between these systems. We have added additional comments in the Discussion related to our newly published work. As an aside, Dr. Lee generated the first version of the figure that was adapted by others in the lab. It is perhaps unlucky that those other studies have been published before his work.

Author Response:

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

Reviewer #1 (Public review):

Given the importance that these coupling mechanisms have been given in theory, this is a timely and important contribution to the literature in terms of determining whether these theoretical assumptions hold true in human data.

Thank you!

I did not follow the logic behind including spindle amplitude in the meta-analysis. This is not a measure of SO-spindle coupling (which is the focus of the review), unless the authors were restricting their analysis of the amplitude of coupled spindles only. It doesn't sound like this is the case though. The effect of spindle amplitude on memory consolidation has been reviewed in another recent meta-analysis (Kumral et al, 2023, Neuropsychologia). As this isn't a measure of coupling, it wasn't clear why this measure was included in the present meta-analysis. You could easily make the argument that other spindle measures (e.g., density, oscillatory frequency) could also have been included, but that seems to take away from the overall goal of the paper which was to assess coupling.

Indeed, spindle amplitude refers to all spindle events rather than only coupled spindles. This choice was made because we recognized the challenge of obtaining relevant data from each study—only 4 out of the 23 included studies performed their analyses after separating coupled and uncoupled spindles. This inconsistency strengthens the urgency and importance of this meta-analysis to standardize the methods and measures used for future analysis on SO-SP coupling and beyond. We agree that focusing on the amplitude of coupled spindles would better reveal their relations with coupling, and we have discussed this limitation in the manuscript.

Nevertheless, we believe including spindle amplitude in our study remains valuable, as it served several purposes. First, SO-SP coupling involves the modulation between spindle amplitude and slow oscillation phase. Different studies have reported conflicting conclusions regarding how overall spindle amplitude was related to coupling as an indicator of oscillation strength overnight– some found significant correlations (e.g., Baena et al., 2023), while others did not (e.g., Roebber et al., 2022). This discrepancy highlights an indirect but potentially crucial insight into the role of spindle amplitude in coupling dynamics. Second, in studies related to SO-SP coupling, spindle amplitude is one of the most frequently reported measures along with other coupling measures that significantly correlated with oversleep memory improvements (e.g. Kurz et al., 2023; Ladenbauer et al., 2021; Niknazar et al., 2015), so we believe that including this measure can provide a more comprehensively review of the existing literature on SO-SP coupling. Third, incorporating spindle amplitude allows for a direct comparison between the measurement of coupling and individual events alone in their contribution to memory consolidation– a question that has been extensively explored in recent research. (e.g., Hahn et al., 2020; Helfrich et al., 2019; Niethard et al., 2018; Weiner et al., 2023). Finally, spindle amplitude was identified as the most important moderator for memory consolidation in Kumral et al.'s (2023) meta-analysis. By including it in our analysis, we sought to replicate their findings within a broader framework and introduce conceptual overlaps with existing reviews. Therefore, although we were not able to selectively include coupled spindles, there is still a unique relation between spindle amplitude and SO-SP coupling that other spindle measures do not have. 

Originally, we also intended to include coupling density or counts in the analysis, which seems more relevant to the coupling metrics. However, the lack of uniformity in methods used to measure coupling density posed a significant limitation. We hope that our study will encourage consistent reporting of all relevant parameters in future research, allowing future meta-analyses to incorporate these measures comprehensively. We have added this discussion to the revised version of the manuscript (p. 3) to further clarify these points.

All other citations were referenced in the manuscript.

At the end of the first paragraph of section 3.1 (page 13), the authors suggest their results "... further emphasise the role of coupling compared to isolated oscillation events in memory consolidation". This had me wondering how many studies actually test this. For example, in a hierarchical regression model, would coupled spindles explain significantly more variance than uncoupled spindles? We already know that spindle activity, independent of whether they are coupled or not, predicts memory consolidation (e.g., Kumral meta-analysis). Is the variance in overnight memory consolidation fully explained by just the coupled events? If both overall spindle density and coupling measures show an equal association with consolidation, then we couldn't conclude that coupling compared to isolated events is more important.

While primary coupling measurements, including coupling phase and strength, showed strong evidence for their associations with memory consolidation, measures of spindles, including spindle amplitude, only exhibited limited evidence (or “non-significant” effect) for their association with consolidation. These results are consistent with multiple empirical studies using different techniques (e.g., Hahn et al., 2020; Helfrich et al., 2019; Niethard et al., 2018; Weiner et al., 2023), which reported that coupling metrics are more robust predictors of consolidation and synaptic plasticity than spindle or slow oscillation metrics alone. However, we agree with the reviewer that we did not directly separate the effect between coupled and uncoupled spindles, and a more precise comparison would involve contrasting the “coupling of oscillation events” with ”individual oscillation events” rather than coupling versus isolated events.

We recognized that Kumral and colleagues’ meta-analysis reported a moderate association between spindle measures and memory consolidation (e.g., for spindle amplitude-memory association they reported an effect size of approximately r = 0.30). However, one of the advantages of our study is that we actively cooperated with the authors to obtain a large number of unreported and insignificant data relevant to our analysis, as well as separated data that were originally reported under mixed conditions. This approach decreases the risk of false positives and selective reporting of results, making the effect size more likely to approach the true value. In contrast, we found only a weak effect size of r = 0.07 with minimal evidence for spindle amplitude-memory relation. However, we agree with the reviewer that using a more conservative term in this context would be a better choice since we did not measure all relevant spindle metrics including the density.

To improve clarity in our manuscript, we have revised the statement to: “Together with other studies included in the review, our results suggest a crucial role of coupling but did not support the role of spindle events alone in memory consolidation,” and provide relevant references (p. 13). We believe this can more accurately reflect our findings and the existing literature to address the reviewer’s concern.

It was very interesting to see that the relationship between the fast spindle coupling phase and overnight consolidation was strongest in the frontal electrodes. Given this, I wonder why memory promoting fast spindles shows a centro-parietal topography? Surely it would be more adaptive for fast spindles to be maximally expressed in frontal sites. Would a participant who shows a more frontal topography of fast spindles have better overnight consolidation than someone with a more canonical centro-parietal topography? Similarly, slow spindles would then be perfectly suited for memory consolidation given their frontal distribution, yet they seem less important for memory.

Regarding the topography of fast spindles and their relationship to memory consolidation, we agree this is an intriguing issue, and we have already developed significant progress in this topic in our ongoing work, and have found evidence that participants with a more frontal topography of fast spindles show better overnight consolidation. These findings will be presented in our future publications. We share a few relevant observations: First, there are significant discrepancies in the definition of “slow spindle” in the field. Some studies defined slow spindle from 9-12 Hz (e.g. Mölle et al., 2011; Kurz et al., 2021), while others performed the event detection within a range of 11-13/14 Hz and found a frontal-dominated topography (e.g. Barakat et al., 2011; D'Atri et al., 2018). Compounding this issue, individual and age differences in spindle frequency are often overlooked, leading to challenges in reliably distinguishing between slow and fast spindles. Some studies have reported difficulty in clearly separating the two types of spindles altogether (e.g., Hahn et al., 2020). Moreover, a critical factor often ignored in past research is the propagating nature of both slow oscillations and spindles across the cortex, where spindles are coupled with significantly different phases of slow oscillations (see Figure 5). In addition, the frontal region has the strongest and most active SOs as its origin site, which may contribute to the role of frontal coupling. In contrast, not all SOs propagate from PFC to centro-parietal sites. The reviewer also raised an interesting idea that slow spindles would be perfectly suited for memory consolidation given their frontal distribution. We propose that one possible explanation is that if SOs couple exclusively with slow SPs, they may lose their ability to coordinate inter-area activity between centro-parietal and frontal regions, which could play a critical role in long-range memory transmission across hippocampus, thalamus, and prefrontal cortex. This hypothesis requires investigation in future studies. We believe a better understanding of coupling in the context of the propagation of these waves will help us better understand the observed frontal relationship with consolidation. Therefore, we believe this result supports our conclusion that coupling precision is more important than intensity, and we have addressed this in revised manuscript (pp. 15-16).

The authors rightly note the issues with multiple comparisons in sleep physiology and memory studies. Multiple comparison issues arise in two ways in this literature. First are comparisons across multiple electrodes (many studies now use high-density systems with 64+ channels). Second are multiple comparisons across different outcome variables (at least 3 ways to quantify coupling (phase, consistency, occurrence) x 2 spindle types (fast, slow). Can the authors make some recommendations here in terms of how to move the field forward, as this issue has been raised numerous times before (e.g., Mantua 2018, Sleep; Cox & Fell 2020, Sleep Medicine Reviews for just a couple of examples). Should researchers just be focusing on the coupling phase? Or should researchers always report all three metrics of coupling, and correct for multiple comparisons? I think the use of pre-registration would be beneficial here, and perhaps could be noted by the authors in the final paragraph of section 3.5, where they discuss open research practices.

There are indeed multiple methods that we can discuss, including cluster-based and non-parametric methods, etc., to correct for multiple comparisons in EEG data with spatiotemporal structures. In addition, encouraging the reporting of all tested but insignificant results, at least in supplementary materials, is an important practice that helps readers understand the findings with reduced bias. We agree with the reviewer’s suggestions and have added more information in section 3.4-3.5 (p. 17) to advocate for a standardized “template” used to report effect sizes and correct multiple comparisions in future research.

We advocate for the standardization of reporting all three coupling metrics– phase, strength, and prevalence (density, count, and/or percentage coupled). Each coupling metric captures distinct a property of the coupling process and may interact with one another (Weiner et al., 2023). Therefore, we believe it is essential to report all three metrics to comprehensively explore their different roles in the “how, what, and where” of long-distance communication and consolidation of memory. As we advance toward a deeper understanding of the relationship between memory and sleep, we hope this work establishes a standard for the standardization, transparency, and replication of relevant studies.

Reviewer #2 (Public review):

Regarding the Moderator of Age: Although the authors discuss the limited studies on the analysis of children and elders regarding age as a moderator, the figure shows a significant gap between the ages of 40 and 60. Furthermore, there are only a few studies involving participants over the age of 60. Given the wide distribution of effect sizes from studies with participants younger than 40, did the authors test whether removing studies involving participants over 60 would still reveal a moderator effect?

We agree that there is an age gap between younger and older adults, as current studies often focus on contrasting newly matured and fully aged populations to amplify the effect, while neglecting the gradual changes in memory consolidation mechanisms across the aging spectrum. We suggest that a non-linear analysis of age effects would be highly valuable, particularly when additional child and older adult data become available.

In response to the reviewer’s suggestion, we re-tested the moderation effect of age after excluding effect sizes from older adults. The results revealed a decrease in the strength of evidence for phase-memory association due to increased variability, but were consistent for all other coupling parameters. The mean estimations also remained consistent (coupling phase-memory relation: -0.005 [-0.013, 0.004], BF10 = 5.51, the strength of evidence reduced from strong to moderate; coupling strength-memory relation: -0.005 [-0.015, 0.008], BF10 = 4.05, the strength of evidence remained moderate). These findings align with prior research, which typically observed a weak coupling-memory relationship in older adults during aging (Ladenbauer et al, 2021; Weiner et al., 2023) but not during development (Hahn et al., 2020; Kurz et al., 2021; Kurz et al., 2023). Therefore, this result is not surprising to us, and there are still observable moderate patterns in the data. We have reported these additional results in the revised manuscript (pp. 6, 11), and interpret “the moderator effect of age in the phase-memory association becomes less pronounced during development after excluding the older adult data”. We believe the original findings including the older adult group remain meaningful after cautious interpretation, given that the older adult data were derived from multiple studies and different groups, and they represent the aging effects.

Reviewer #3 (Public review):

First, the authors conclude that "SO-SP coupling should be considered as a general physiological mechanism for memory consolidation". However, the reported effect sizes are smaller than what is typically considered a "small effect”.

While we acknowledge the concern about the small effect sizes reported in our study, it is important to contextualize these findings within the field of neuroscience, particularly memory research. Even in individual studies, small effect sizes are not uncommon due to the inherent complexity of the mechanisms involved and the multitude of confounding variables. This is an important factor to be considered in meta-analyses where we synthesize data from diverse populations and experimental conditions. For example, the relationship between SO-slow SP coupling and memory consolidation in older adults is expected to be insignificant.

As Funder and Ozer (2019) concluded in their highly cited paper, an effect size of r = 0.3 in psychological and related fields should be considered large, with r = 0.4 or greater likely representing an overestimation and rarely found in a large sample or a replication. Therefore, we believe r = 0.1 should not be considered as a lower bound of the small effect. Bakker et al. (2019) also advocate for a contextual interpretation of the effect size. This is particularly important in meta-analyses, where the results are less prone to overestimation compared to individual studies, and we cooperated with all authors to include a large number of unreported and insignificant results. In this context, small correlations may contain substantial meaningful information to interpret. Although we agree that effect sizes reported in our study are indeed small at the overall level, they reflect a rigorous analysis that incorporates robust evidence across different levels of moderators. Our moderator analyses underscore the dynamic nature of coupling-memory relationships, with stronger associations observed in moderator subgroups that have historically exhibited better memory performance, particularly after excluding slow spindles and older adults. For example, both the coupling phase and strength of frontal fast spindles with slow oscillations exhibited "moderate-to-large" correlations with the consolidation of different types of memory, especially in young adults, with r values ranging from 0.18 to 0.32. (see Table S9.1-9.4). We have included discussion about the influence of moderators and hierarchical structures on the dynamics of coupling-memory associations (pp. 17, 20). In addition, we have updated the conclusion to be “SO-fast SP coupling should be considered as a general physiological mechanism for memory consolidation” (p. 1).

Second, the study implements state-of-the-art Bayesian statistics. While some might see this as a strength, I would argue that it is the greatest weakness of the manuscript. A classical meta-analysis is relatively easy to understand, even for readers with only a limited background in statistics. A Bayesian analysis, on the other hand, introduces a number of subjective choices that render it much less transparent.

This kind of analysis seems not to be made to be intelligible to the average reader. It follows a recent trend of using more and more opaque methods. Where we had to trust published results a decade ago because the data were not openly available, today we must trust the results because the methods can no longer be understood with reasonable effort.

This becomes obvious in the forest plots. It is not immediately apparent to the reader how the distributions for each study represent the reported effect sizes (gray dots). Presumably, they depend on the Bayesian priors used for the analysis. The use of these priors makes the analyses unnecessarily opaque, eventually leading the reader to question how much of the findings depend on subjective analysis choices (which might be answered by an additional analysis in the supplementary information).

We appreciate the reviewer for sharing this viewpoint and we value the opportunity to clarify some key points. To address the concern about clarity, we have included more details in the methods section explaining how to interpret Bayesian statistics including priors, posteriors, and Bayes factors, making our results more accessible to those less familiar with this approach.

On the use of Bayesian models, we believe there may have been a misunderstanding. Bayesian methods, far from being "opaque" or overly complex, are increasingly valued for their ability to provide nuanced, accurate, and transparent inferences (Sutton & Abrams, 2001; Hackenberger, 2020; van de Schoot et al., 2021; Smith et al., 1995; Kruschke & Liddell, 2018). It has been applied in more than 1,200 meta-analyses as of 2020 (Hackenberger, 2020). In our study, we used priors that assume no effect (mean set to 0, which aligns with the null) while allowing for a wide range of variation to account for large uncertainties. This approach reduces the risk of overestimation or false positives and demonstrates much-improved performance over traditional methods in handling variability (Williams et al., 2018; Kruschke & Liddell, 2018). In addition, priors can also increase transparency, since all assumptions are formally encoded and open to critique or sensitivity analysis. In contrast, frequentist methods often rely on hidden or implicit assumptions such as homogeneity of variance, fixed-effects models, and independence of observations that are not directly testable. Sensitivity analyses reported in the supplemental material (Table S9.1-9.4) confirmed the robustness of our choices of priors– our results did not vary by setting different priors.

As Kruschke and Liddell (2018) described, “shrinkage (pulling extreme estimates closer to group averages) helps prevent false alarms caused by random conspiracies of rogue outlying data,” a well-known advantage of Bayesian over traditional approaches. This explains the observed differences between the distributions and grey dots in the forest plots, which is an advantage of Bayesian models in handling heterogeneity. Unlike p-values, which can be overestimated with a large sample size and underestimated with a small sample size, Bayesian methods make assumptions explicit, enabling others to challenge or refine them– an approach aligned with open science principles (van de Schoot et al., 2021). For example, a credible interval in Bayesian model can be interpreted as “there is a 95% probability that the parameter lies within the interval.”, while a confidence interval in frequentist model means “In repeated experiments, 95% of the confidence intervals will contain the true value.” We believe the former is much more straightforward and convincing for readers to interpret. We will ensure our justification for using Bayesian models is more clearly presented in the manuscript (pp. 21-23).

We acknowledge that even with these justifications, different researchers may still have discrepancies in their preferences for Bayesian and frequentist models. To increase the effort of transparent reporting, we have also reported the traditional frequentist meta-analysis results in Supplemental Material 10 to justify the robustness of our analysis, which suggested non-significant differences between Bayesian and frequentist models. We have included clearer references in the updated version of the manuscript to direct readers to the figures that report the statistics provided by traditional models.

However, most of the methods are not described in sufficient detail for the reader to understand the proceedings. It might be evident for an expert in Bayesian statistics what a "prior sensitivity test" and a "posterior predictive check" are, but I suppose most readers would wish for a more detailed description. However, using a "Markov chain Monte Carlo (MCMC) method with the no-U-turn Hamiltonian Monte Carlo (HMC) sampler" and checking its convergence "through graphical posterior predictive checks, trace plots, and the Gelman and Rubin Diagnostic", which should then result in something resembling "a uniformly undulating wave with high overlap between chains" is surely something only rocket scientists understand. Whether this was done correctly in the present study cannot be ascertained because it is only mentioned in the methods and no corresponding results are provided. 

We appreciate the reviewer’s concerns about accessibility and potential complexity in our descriptions of Bayesian methods. Our decision to provide a detailed account serves to enhance transparency and guide readers interested in replicating our study. We acknowledge that some terms may initially seem overwhelming. These steps, such as checking the MCMC chain convergence and robustness checks, are standard practices in Bayesian research and are analogous to “linearity”, “normality” and “equal variance” checks in frequentist analysis. In addition, Hamiltonian Monte Carlo (HMC) is the default algorithm Stan (the software we used to fit Bayesian models) uses to sample from the posterior distribution in Bayesian models. It is a type of MCMC method designed to be faster and more efficient than traditional sampling algorithms, especially for complex or high-dimensional models. We have added exemplary plots in the supplemental material S4.1-4.3 and the method section (pp. 21-22) to explain the results and interpretation of these convergence checks. We hope this will help address any concerns about methodological rigor.

In one point the method might not be sufficiently justified. The method used to transform circular-linear r (actually, all references cited by the authors for circular statistics use r² because there can be no negative values) into "Z_r", seems partially plausible and might be correct under the H0. However, Figure 12.3 seems to show that under the alternative Hypothesis H1, the assumptions are not accurate (peak Z_r=~0.70 for r=0.65). I am therefore, based on the presented evidence, unsure whether this transformation is valid. Also, saying that Z_r=-1 represents the null hypothesis and Z_r=1 the alternative hypothesis can be misinterpreted, since Z_r=0 also represents the null hypothesis and is not half way between H0 and H1.

First, we realized that in the title of Figures 12.2 and 12.3. “true r = 0.35” and “true r = 0.65” should be corrected as “true r_z” (note that we use r_z instead of Z_r in the revised manuscript per your suggestion). The method we used here is to first generate an underlying population that has null (0), moderate (0.35), or large (0.65) r_z correlations, then test whether the sampling distribution drawn from these populations followed a normal distribution across varying sample sizes. Nevertheless, the reviewer correctly noticed discrepancies between the reported true r_z and its sampling distribution peak. This discrepancy arises because, when generating large population data, achieving exact values close to a strong correlation like r_z = 0.65 is unlikely. We loop through simulations to generate population data and ensure their r_z values fall within a threshold. For moderate effect sizes (e.g., r_z = 0.35), this is straightforward using a narrow range (0.34 < r_z < 0.35). However, for larger effect sizes like r_z = 0.65, a wider range (0.6 < r_z < 0.7) is required. therefore sometimes the population we used to draw the sample has a r_z slightly deviated from 0.65. This remains reasonable since the main point of this analysis is to ensure that a large r_z still has a normal sampling distribution, but not focus specifically on achieving r_z = 0.65.

We acknowledge that this variability of the range used was not clearly explained in supplemental material 12 and it is not accurate to report “true r_z = 0.65”. In the revised version, we have addressed this issue by adding vertical lines to each subplot to indicate the r_z of the population we used to draw samples, making it easier to check if it aligns with the sampling peak. In addition, we have revised the title to “Sampling distributions of r_z drawn from strong correlations

(r_z = 0.6-0.7)”. We confirmed that population r_z and the peak of their sampling distribution remain consistent under both H0 and H1 in all sample sizes with n > 25, and we hope this explanation can fully resolve your concern.

We agree with the reviewer that claiming r_z = -1 represents the null hypothesis is not accurate. The circlin r_z = 0 is better analogous to Pearson’s r = 0 since both represent the mean drawn from the population under the null hypothesis. In contrast, the mean effect size under null will be positive in the raw circlin r, which is one of the important reasons for the transformation. To provide a more accurate interpretation, we updated Table 6 to describe the following strength levels of evidence: no effect (r < 0), null (r = 0), small (r = 0.1), moderate (r = 0.3), and large (r =0.5). We thank the reviewer again for their valuable feedback.

Reviewer #2 (Recommendations for the authors):

(1) There is an extra space in the Notes of Figure 1. "SW R sharp-wave ripple.".

We thank the reviewer for pointing this out. We have confirmed that the "extra space" is not an actual error but a result of how italicized Times New Roman font is rendered in the LaTeX format. We believe that the journal’s formatting process will resolve this issue.

(2) In the introduction, slow oscillations (SO) are defined with a frequency of 0.16-4 Hz, sleep spindles (SP) at 8-16 Hz, and sharp-wave ripples (SWR) at 80-300 Hz. The term "fast oscillation" (FO) is first introduced with the clarification "SPs in our case." However, on page 2, the authors state, "SO-FO coupling involving SWRs, SPs, and SOs..." There seems to be a discrepancy in the definition of FO; does it consistently refer to SPs and SWRs throughout the article?

We appreciate the reviewer’s observation regarding the potential ambiguity of the term "FO." In our manuscript, "FO" is used as a general term to describe the interaction of a "relatively faster oscillation" with a "relatively slower oscillation" in the phase-amplitude coupling mechanism, therefore it is not intended to exclusively refer to SPs or SWRs. For example, it is usually used to describe SO–SP–SWR couplings during sleep memory studies, but Theta–Alpha–Gamma couplings in wakeful memory studies. To address this confusion, we removed the phrase "SPs in our case" and explicitly use "SPs" when referring to spindles. In addition, we have replaced "fast oscillation" with "faster oscillation" to emphasize that it is used in a relative sense (p. 1), rather than to refer to a specific oscillation. Also, we only retained the term “FO” when introducing the PAC mechanism.

(3) On page 2, the first paragraph contains the phrase: "...which occur in the precise hierarchical temporal structure of SO-FO coupling involving SWRs, SPs, and SOs ..." Since "SO-FO" refers to slow and fast oscillations, it is better to maintain the order of frequencies, suggesting it as: SOs, SPs, and SWRs.

We sincerely thank the reviewer for their valuable suggestion. We have updated the sentence to maintain the correct order from the lowest to the highest frequencies in the revised version (p. 2).

(4) References should be provided:

a “Studies using calcium imaging after SP stimulation explained the significance of the precise coupling phase for synaptic plasticity.".

b. "Electrophysiology evidence indicates that the association between memory consolidation and SO-SP coupling is influenced by a variety of behavioral and physiological factors under different conditions."

c. "Since some studies found that fast SPs predominate in the centroparietal region, while slow SPs are more common in the frontal region, a significant amount of studies only extracted specific types of SPs from limited electrodes. Some studies even averaged all electrodes to estimate coupling..."

This is a great point.  These have been referenced as follows:

a. Rephrased: “Studies using calcium imaging and SP stimulation explained the significance of the precise coupling phase for synaptic plasticity.” We changed “after” to “and” to reflect that these were conducted as two separate experiments. This is a summary statement, with relevant citations provided in the following two sentences of the paragraph, including Niethard et al., 2018, and Rosanova et al., 2005. (p. 2)

b. Included diverse sources of evidence: “Electrophysiology evidence from studies included in our meta-analysis (e.g. Denis et al., 2021; Hahn et al., 2020; Mylonas et al., 2020) and others (e.g. Bartsch et al., 2019; Muehlroth et al., 2019; Rodheim et al., 2023) reported that the association between memory consolidation and SO-SP coupling is influenced by a variety of behavioral and physiological factors under different conditions.” (p. 3)

c. Added references and more details: “Since some studies found that fast SPs predominate in the centroparietal region, while slow SPs are more common in the frontal region, a significant amount of studies selectively extracted specific types of SPs from limited electrodes (e.g. Dehnavi et al., 2021; Perrault et al., 2019; Schreiner et al., 2021). Some studies even averaged all electrodes in their spectral and/or time-series analysis to estimate metrics of oscillations and their couplings (e.g. Denis et al., 2022; Mölle et al., 2011; Nicolas et al., 2022).” (p. 4)

Reviewer #3 (Recommendations for the authors):

There are a number of terms that are not clearly defined or used:

(1) SP amplitude. Does this mean only the amplitude of coupled spindles or of spindles in general?

This refers to the amplitude of spindles in general. We clarified this in the revised text (and see response to reviewer #1, point #1).

(2) The definition of a small effect

We thank the reviewer again for raising this important question. As we responded in the public review, small effect sizes are common in neuroscience and meta-analyses due to the complexity of the underlying mechanisms and the presence of numerous confounding variables and hierarchical levels. To help readers better interpret effect sizes, we changed rigid ranges to widely accepted benchmarks for effect size levels in neuroscience research: small (r=0.1), moderate (r=0.3), and large (r=0.5; Cohen, 1988). We also noted that an evidence and context-based framework will provide a more practical way to interpret the observed effect sizes compared to rigid categorizations.

(3) Can a BF10 based on experimental evidence actually be "infinite" and a probability actually be 1.00?

We appreciate the reviewer for highlighting this potential confusion. The formula used to calculate BF10 is P(data | H1) / P(data | H0). In the experimental setting with an informative prior, an ‘infinite’ BF10 value indicates that all posterior samples are overwhelmingly compatible with H1 given the data and assumptions (Cox et al., 2023; Heck et al., 2023; Ly et al., 2016). In such cases, the denominator P(data | H0) becomes vanishingly small, leading BF10 to converge to infinity. This scenario occurs when the probability of H1 converges to 1 (e.g., 0.9999999999…).

It is a well-established convention in Bayesian statistics to report the Bayes factor as "infinity" in cases where the evidence is overwhelmingly strong, and BF10 exceeds the numerical limits of the computation tools to become effectively infinite. To address this ambiguity, we added a footnote in the revised version of the manuscript to clarify the interpretation of an 'infinite' BF10 . (p. 8)

(4) Z_r should be renamed to r_z or similar. These are not Z values (-inf..+inf), but r values (-1..1).

We thank the reviewers for their suggestions. We agree that r_z would provide a clearer and more accurate interpretation, while z is more appropriate for referring to Fisher's z-transformed r (see point (5)). We have updated the notation accordingly.

(5) Also, it remains quite unclear at which points in the analyses, "r" values or "Fisher's z transformed r" values are used. Assumptions of normality should only apply to the transformed values. However, the formulas for the random effects model seem to assume normality for r values.

The correlation values were z-transformed during preprocessing to ensure normality and the correct estimation of sampling variances before running the models. The outputs were then back-transformed to raw r values only when reporting the results to help readers interpret the effect size. We mentioned this in Section 5.5.1, therefore the normality assumptions are not a concern. We have updated the notation r to z (-inf..+inf) in the formula of the random and mixed effect models in the revised version of the manuscript (p. 22).

Language

(1) Frequency. In the introduction, the authors use "frequency" when they mean something like the incidence of spindles.

We agree that the term "frequency" has been used inconsistently to describe both the incidence of events and the frequency bands of oscillations. We have replaced "frequency" with "prevalence" to refer to the incidence of coupling events where applicable (p. 3).

(2) Moderate and mediate. These two terms are usually meant to indicate two different types of causal influences.

Thanks for the reviewer’s suggestions. We agree that "moderate" is more appropriate to describe moderators in this study since it does not directly imply causality. We have replaced mediate with moderate in relevant contexts.

(3) "the moderate effect of memory task is relatively weak": "moderator effect" or "moderate effect"?

We appreciate the reviewer for pointing out this mistake. We have updated the term to "moderator effect" in Section 2.2.2 (p. 6).

(4) "in frontal regions we found a latest coupled but most precise and strong SO-fast SP coupling" Meaning?

We thank the reviewer for bringing this concern of clarity to our attention. By 'latest,' we refer to the delayed phase of SO-fast SP coupling observed in the frontal regions compared to the central and parietal regions (see Figure 5), "Precise and strong" describes the high precision and strength of phase-locking between the SO up-state and the fast SP peak in these regions. We have rephrased this sentence to be: “We found that SO-fast SP coupling in the frontal region occurred at the latest phase observed across all regions, characterized by the highest precision and strength of phase-locking.” to improve clarity (p. 9).

(5) Figure 5 and others contain angles in degrees and radians.

We appreciate the reviewer pointing out this inconsistency. We have updated the manuscript and supplementary material to consistently use radians throughout.

Reviewer #2 (Public review):

The revised manuscript by Altan et al. includes some real improvements to the visualizations and explanations of the authors' thesis statement with respect to fMRI measurements of pRF sizes. In particular, the deposition of the paper's data has allowed me to probe and refine several of my previous concerns. While I still have major concerns about how the data are presented in the current draft of the manuscript, my skepticism about data quality overall has been much alleviated. Note that this review focuses almost exclusively on the fMRI data as I was satisfied with the quality of the psychophysical data and analyses in my previous review.

Major Concerns

(I) Statistical Analysis

In my previous review, I raised the concern that the small sample size combined with the noisiness of the fMRI data, a lack of clarity about some of the statistics, and a lack of code/data likely combine to make this paper difficult or impossible to reproduce as it stands. The authors have since addressed several aspects of this concern, most importantly by depositing their data. However their response leaves some major questions, which I detail below.

First of all, the authors claim in their response to the previous review that the small sample size is not an issue because large samples are not necessary to obtain "conclusive" results. They are, of course, technically correct that a small sample size can yield significant results, but the response misses the point entirely. In fact, small samples are more likely than large samples to erroneously yield a significant result (Button et al., 2013, DOI:10.1038/nrn3475), especially when noise is high. The response by the authors cites Schwarzkopf & Huang (2024) to support their methods on this front. After reading the paper, I fail to see how it is at all relevant to the manuscript at hand or the criticism raised in the previous review. Schwarzkopf & Huang propose a statistical framework that is narrowly tailored to situations where one is already certain that some phenomenon (like the adaptation of pRF size to spatial frequency) either always occurs or never occurs. Such a framework is invalid if one cannot be certain that, for example, pRF size adapts in 98% of people but not the remaining 2%. Even if the paper were relevant to the current study, the authors don't cite this paper, use its framework, or admit the assumptions it requires in the current manuscript. The observation that a small dataset can theoretically lead to significance under a set of assumptions not appropriate for the current manuscript is not a serious response to the concern that this manuscript may not be reproducible.

To overcome this concern, the authors should provide clear descriptions of their statistical analyses and explanations of why these analyses are appropriate for the data. Ideally, source code should be published that demonstrates how the statistical tests were run on the published data. (I was unable to find any such source code in the OSF repository.) If the effects in the paper were much stronger, this level of rigor might not be strictly necessary, but the data currently give the impression of being right near the boundary of significance, and the manuscript's analyses needs to reflect that. The descriptions in the text were helpful, but I was only able to approximately reproduce the authors analyses based on these descriptions alone. Specifically, I attempted to reproduce the Mood's median tests described in the second paragraph of section 3.2 after filtering the data based on the criteria described in the final paragraph of section 3.1. I found that 7/8 (V1), 7/8 (V2), 5/8 (V3), 5/8 (V4), and 4/8 (V3A) subjects passed the median test when accounting for the (40) multiple comparisons. These results are reasonably close to those reported in the manuscript and might just differ based on the multiple comparisons strategy used (which I did not find documented in the manuscript). However, Mood's median test does not test the direction of the difference-just whether the medians are different-so I additionally required that the median sigma of the high-adapted pRFs be greater than that of the low-adapted pRFs. Surprisingly, in V1 and V3, one subject each (not the same subject) failed this part of the test, meaning that they had significant differences between conditions but in the wrong direction. This leaves 6/8 (V1), 7/8 (V2), 4/8 (V3), 5/8 (V4), and 4/8 (V3A) subjects that appear to support the authors' conclusions. As the authors mention, however, this set of analyses runs the risk of comparing different parts of cortex, so I also performed Wilcox signed-rank tests on the (paired) vertex data for which both the high-adapted and low-adapted conditions passed all the authors' stated thresholds. These results largely agreed with the median test (only 5/8 subjects significant in V1 but 6/8 in in V3A, other areas the same, though the two tests did not always agree which subjects had significant differences). These analyses were of course performed by a reviewer with a reviewer's time commitment to the project and shouldn't be considered a replacement for the authors' expertise with their own data. If the authors think that I have made a mistake in these calculations, then the best way to refute them would be to publish the source code they used to threshold the data and to perform the same tests.

Setting aside the precise values of the relevant tests, we should also consider whether 5 of 8 subjects showing a significant effect (as they report for V3, for example) should count as significant evidence of the effect? If one assumes, as a null hypothesis, that there is no difference between the two conditions in V3 and that all differences are purely noise, then a binomial test across subjects would be appropriate. Even if 6 of 8 subjects show the effect, however (and ignoring multiple comparisons), the p-value of a one-sided binomial test is not significant at the 0.05 level (7 of 8 subjects is barely significant). Of course, a more rigorous way to approach this question could be something like an ANOVA, and the authors use an ANOVA analysis of the medians in the paragraph following their use of Mood's median test. However, ANOVA assumes normality, and the authors state in the previous paragraph that they employed Mood's median test because "the distribution of the pRF sizes is zero-bounded and highly skewed" so this choice does not make sense. The Central Limits Theorem might be applied to the medians in theory, but with only 8 subjects and with an underlying distribution of pRF sizes that is non-negative, the relevant data will almost certainly not be normally distributed. These tests should probably be something like a Kruskal-Wallis ANOVA on ranks.

All of the above said, my intuition about the data is currently that there are significant changes to the adapted pRF size in V2. I am not currently convinced that the effects in other visual areas are significant, and I suspect that the paper would be improved if authors abandoned their claims that areas other than V2 show a substantial effect. Importantly, I don't think this causes the paper to lose any impact-in fact, if the authors agree with my assessments, then the paper might be improved by focusing on V2. Specifically, the authors' already discuss psychophysical work related to the perception of texture on pages 18 and 19 and link it to their results. V2 is also implicated in the perception of texture (see, for example, Freeman et al., 2013; DOI:10.1038/nn.3402; Ziemba et al., 2016, DOI:10.1073/pnas.1510847113; Ziemba et al., 2019; DOI:10.1523/JNEUROSCI.1743-19.2019) and so would naturally be the part of the visual cortex where one might predict that spatial frequency adaptation would have a strong effect on pRF size. This neatly connects the psychophysical and imaging sides of this project and could make a very nice story out of the present work.

(II) Visualizations

The manuscript's visual evidence regarding the pRF data also remains fairly weak (but I found the pRF size comparisons in the OSF repository and Figure S1 to be better evidence-more in the next paragraph). The first line of the Results section still states, "A visual inspection on the pRF size maps in Figure 4c clearly shows a difference between the two conditions, which is evident in all regions." As I mentioned in my previous review, I don't agree with this claim (specifically, that it is clear). My impression when I look at these plots is of similarity between the maps, and, where there is dissimilarity, of likely artifacts. For example, the splotch of cortex near the upper vertical meridian (ventral boundary) of V1 that shows up in yellow in the upper plot but not the lower plot also has a weirdly high eccentricity and a polar angle near the opposite vertical meridian: almost certainly not the actual tuning of that patch of cortex. If this is the clearest example subject in the dataset, then the effect looks to me to be very small and inconsistently distributed across the visual areas. That said, I'm not convinced that the problem here is the data-rather, I think it's just very hard to communicate a small difference in parameter tuning across a visual area using this kind of side-by-side figure. I think that Figure S2, though noisy (as pRF maps typically are), is more convincing than Figure 4c, personally. For what it's worth, when looking at the data myself, I found that plotting log(𝜎(H) / 𝜎(L)), which will be unstable when noise causes 𝜎(H) or 𝜎(L) to approach zero, was less useful than plotting plotting (𝜎(H) - 𝜎(L)) / (𝜎(H) + 𝜎(L)). This latter quantity will be constrained between -1 and 1 and shows something like a proportional change in the pRF size (and thus should be more comparable across eccentricity).

In my opinion, the inclusion of the pRF size comparison plots in the OSF repository and Figure S1 made a stronger case than any of the plots of the cortical surface. I would suggest putting these on log-log plots since the distribution of pRF size (like eccentricity) is approximately exponential on the cortical surface. As-is, it's clear in many plots that there is a big splotch of data in the compressed lower left corner, but it's hard to get a sense for how these should be compared to the upper right expanse of the plots. It is frequently hard to tell whether there is a greater concentration of points above or below the line of equality in the lower left corner as well, and this is fairly central to the paper's claims. My intuition is that the upper right is showing relatively little data (maybe 10%?), but these data are very emphasized by the current plots.
The authors might even want to consider putting a collection of these scatter-plots (or maybe just subject 007, or possible all subjects' pRFs on a single scatter-plot) in the main paper and using these visualizations to provide intuitive supporting for the main conclusions about the fMRI data (where the manuscript currently use Figure 4c for visual intuition).

Minor Comments

(1) Although eLife does not strictly require it, I would like to see more of the authors' code deposited along with the data (especially the code for calculating the statistics that were mentioned above). I do appreciate the simulation code that the authors added in the latest submission (largely added in response to my criticism in the previous reviews), and I'll admit that it helped me understand where the authors were coming from, but it also contains a bug and thus makes a good example of why I'd like to see more of the authors' code. If we set aside the scientific question of whether the simulation is representative of an fMRI voxel (more in Minor Comment 5, below), Figures 1A and the "AdaptaionEffectSimulated.png" file from the repository (https://osf.io/d5agf) imply that only small RFs were excluded in the high-adapted condition and only large RFs were excluded in the low-adapted condition. However, the script provided (SimlatePrfAdaptation.m: https://osf.io/u4d2h) does not do this. Lines 7 and 8 of the script set the small and large cutoffs at the 30th and 70th percentiles, respectively, then exclude everything greater than the 30th percentile in the "Large RFs adapted out" condition (lines 19-21) and exclude anything less than the 70th percentile in the "Small RFs adapted out" condition (lines 27-29). So the figures imply that they are representing 70% of the data but they are in fact representing only the most extreme 30% of the data. (Moreover, I was unable to run the script because it contains hard-coded paths to code in someone's home directory.) Just to be clear, these kinds of bugs are quite common in scientific code, and this bug was almost certainly an honest mistake.

(2) I also noticed that the individual subject scatter-plots of high versus low adapted pRF sizes on the OSF seem to occasionally have a large concentration of values on the x=0 and y=0 axes. This isn't really a big deal in the plots, but the manuscript states that "we denoised the pRF data to remove artifactual vertices where at least one of the following criteria was met: (1) sigma values were equal to or less than zero ..." so I would encourage the authors to double-check that the rest of their analysis code was run with the stated filtering.

(3) The manuscript also says that the median test was performed "on the raw pRF size values". I'm not really sure what the "raw" means here. Does this refer to pRF sizes without thresholding applied?

(4) The eccentricity data are much clearer now with the additional comments from the authors and the full set of maps; my concerns about this point have been met.

(5) Regarding the simulation of RFs in a voxel (setting aside the bug), I will admit both to hoping for a more biologically-grounded situation and to nonetheless understanding where the authors are coming from based on the provided example. What I mean by biologically-grounded: something like, assume a 2.5-mm isotropic voxel aligned to the surface of V1 at 4{degree sign} of eccentricity; the voxel would span X to Y degrees of eccentricity, and we predict Z neurons with RFs in this voxel with a distribution of RF sizes at that eccentricity from [reference], etc. eventually demonstrating a plausible pRF size change commensurate to the paper's measurements. I do think that a simulation like this would make the paper more compelling, but I'll acknowledge that it probably isn't necessary and might be beyond the scope here.

Author Response:

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

(1) It remains unclear how this stimulation protocol is proposed to enhance memory. Memories are believed to be stored by precise inputs to specific neurons and highly tuned changes in synaptic strengths. It remains unclear whether proposed neural activity generated by the stimulation reflects the activation of specific memories or generally increased activity across all classes of neurons.

Thank you for raising the important issue of the actual neurophysiological effects of non-invasive brain stimulation. Unfortunately, invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints, while studies on cadavers or rodents would not fully resolve our question. Indeed, the authors of the cited study (Mihály Vöröslakos et al., Nature Communications, 2018) highlight the impossibility of drawing definitive conclusions about the exact voltage required in the in-vivo human brain due to significant differences between rats and humans, as well as the in-vivo human brain and cadavers due to alterations in electrical conductivity that occur in postmortem tissue.

We acknowledge that further exploration of this aspect would be highly valuable, and we agree that it is worth discussing both as a technical limitation and as a potential direction for future research, we therefore modify the manuscript correspondingly. However, to address the challenge of in vivo recordings, we conducted Experiments 3 and 4, which respectively examined the neurophysiological and connectivity changes induced by the stimulation in a non-invasive manner. The observed changes in brain oscillatory activity (increased gamma oscillatory activity), cortical excitability (enhanced posteromedial parietal cortex reactivity), and brain connectivity (strengthened connections between the precuneus and hippocampi) provided evidence of the effects of our non-invasive brain stimulation protocol, further supporting the behavioral data.

Additionally, we carefully considered the issue of stimulation distribution and, in response, performed a biophysical modeling analysis and E-field calculation using the parameters employed in our study (see Supplementary Materials).

(2) The claim that effects directly involve the precuneus lacks strong support. The measurements shown in Figure 3 appear to be weak (i.e., Figure 3A top and bottom look similar, and Figure 3C left and right look similar). The figure appears to show a more global brain pattern rather than effects that are limited to the precuneus. Related to this, it would perhaps be useful to show the different positions of the stimulation apparatus. This could perhaps show that the position of the stimulation matters and could perhaps illustrate a range of distances over which position of the stimulation matters.

Thank you for your feedback. We will improve the clarity of the manuscript to better address this important aspect. Our assumption that the precuneus plays a key role in the observed effects is based on several factors:

(1) The non-invasive stimulation protocol was applied to an individually identified precuneus for each participant. Given existing evidence on TMS propagation, we can reasonably assume that the precuneus was at least a mediator of the observed effects (Ridding & Rothwell, Nature Reviews Neuroscience 2007). For further details about target identification and TMS and tACS propagation, please refer to the MRI data acquisition section in the main text and Biophysical modeling and E-field calculation section in the supplementary materials.

(2) To investigate the effects of the neuromodulation protocol on cortical responses, we conducted a whole-brain analysis using multiple paired t-tests comparing each data point between different experimental conditions. To minimize the type I error rate, data were permuted with the Monte Carlo approach and significant p-values were corrected with the false discovery rate method (see the Methods section for details). The results identified the posterior-medial parietal areas as the only regions showing significant differences across conditions.

(3) To control for potential generalized effects, we included a control condition in which TMS-EEG recordings were performed over the left parietal cortex (adjacent to the precuneus). This condition did not yield any significant results, reinforcing the cortical specificity of the observed effects.

However, as stated in the Discussion, we do not claim that precuneus activity alone accounts for the observed effects. As shown in Experiment 4, stimulation led to connectivity changes between the precuneus and hippocampus, a network widely recognized as a key contributor to long-term memory formation (Bliss & Collingridge, Nature 1993). These connectivity changes suggest that precuneus stimulation triggered a ripple effect extending beyond the stimulation site, engaging the broader precuneus-hippocampus network.

Regarding Figure 3A, it represents the overall expression of oscillatory activity detected by TMS-EEG. Since each frequency band has a different optimal scaling, the figure reflects a graphical compromise. A more detailed representation of the significant results is provided in Figure 3B. The effect sizes for gamma oscillatory activity in the delta T1 and T2 conditions were 0.52 and 0.50, respectively, which correspond to a medium effect based on Cohen’s d interpretation.

(3) Behavioral results showing an effect on memory would substantiate claims that the stimulation approach produces significant changes in brain activity. However, placebo effects can be extremely powerful and useful, and this should probably be mentioned. Also, in the behavioral results that are currently presented, there are several concerns:

a) There does not appear to be a significant effect on the STMB task.

b) The FNAT task is minimally described in the supplementary material. Experimental details that would help the reader understand what was done are not described. Experimental details are missing for: the size of the images, the duration of the image presentation, the degree of image repetition, how long the participants studied the images, whether the names and occupations were different, genders of the faces, and whether the same participant saw different faces across the different stimulation conditions. Regarding the latter point, if the same participant saw the same faces across the different stimulation conditions, then there could be memory effects across different conditions that would need to be included in the statistical analyses. If participants saw different faces across the different stimulus conditions, then it would be useful to show that the difficulty was the same across the different stimuli.

We thank you for signaling the lack in the description of FNAT task. We will add all the information required to the manuscript.

In the meantime, here we provide the answers to your questions. The size of the images 19x15cm. They were presented in the learning phase and the immediate recall for 8 seconds each, while in the delayed recall they were shown (after the face recognition phase) until the subject answered. The learning phase, where name and occupation were shown together with the faces, lasted around 2 minutes comprising the instructions. We used a different set of stimuli for each stimulation condition, for a total of 3 parallel task forms balanced across the condition and order of sessions. All the parallel forms were composed of 6 male and 6 female faces, for each sex there were 2 young adults (aged around 30 years old), 2 middle adults (aged around 50 years old), and 2 old adults (aged around 70 years old). Before the experiments, we ran a pilot study to ensure there were no differences between the parallel forms of the task. We can provide the task with its parallel form upon request. The chance level in the immediate and delayed recall is not quantifiable since the participants had to freely recall the name and the occupation without a multiple choice. In the recognition, the chance level was around 33% (since the possible answers were 3).

c) Also, if I understand FNAT correctly, the task is based on just 12 presentations, and each point in Figure 2A represents a different participant. How the performance of individual participants changed across the conditions is unclear with the information provided. Lines joining performance measurements across conditions for each participant would be useful in this regard. Because there are only 12 faces, the results are quantized in multiples of 100/12 % in Figure 3A. While I do not doubt that the authors did their homework in terms of the statistical analyses, it seems as though these 12 measurements do not correspond to a large effect size. For example, in Figure 3A for the immediate condition (total), it seems that, on average, the participants may remember one more face/name/occupation.

We will add another graph to the manuscript with lines connecting each participant's performance. Unfortunately, we were not able to incorporate it in the box-and-whisker plot.

We apologize for the lack of clarity in the description of the FNAT. As you correctly pointed out, we used the percentage based on the single association between face, name and occupation (12 in total). However, each association consisted of three items, resulting in a total of 36 items to learn and associate – we will make it more explicit in the manuscript.

In the example you mentioned, participants were, on average, able to recall three more items compared to the other conditions. While this difference may not seem striking at first glance, it is important to consider that we assessed memory performance after a single, three-minute stimulation session. Similar effects are typically observed only after multiple stimulation sessions (Koch et al., NeuroImage, 2018; Grover et al., Nature Neuroscience, 2022).

d) Block effects. If I understand correctly, the experiments were conducted in blocks. This is potentially problematic. An example study that articulates potential problems associated with block designs is described in Li et al (TPAMI 2021, https://ieeexplore.ieee.org/document/9264220). It is unclear if potential problems associated with block designs were taken into consideration.

Thank you for the interesting reference. According to this paper, in a block design, EEG or fMRI recordings are performed in response to different stimuli of a given class presented in succession. If this is the case, it does not correspond to our experimental design where both TMS-EEG and fMRI were conducted in a resting state on different days according to the different stimulation conditions.

e) In the FNAT portion of the paper, some results are statistically significant, while others are not. The interpretation of this is unclear. In Figure 3A, it seems as though the authors claim that iTBS+gtACS > iTBS+sham-tACS, but iTBS+gtACS ~ sham+sham. The interpretation of such a result is unclear. Results are also unclear when separated by name and occupation. There is only one condition that is statistically significant in Figure 3A in the name condition, and no significant results in the occupation condition. In short, the statistical analyses, and accompanying results that support the authors’ claims, should be explained more clearly.

Thank you again for your feedback. We will work on making the large amount of data we reported easier to interpret.

Hoping to have thoroughly addressed your initial concerns in our previous responses, we now move on to your observations regarding the behavioral results, assuming you were referring to Figure 2A. The main finding of this study is the improvement in long-term memory performance, specifically the ability to correctly recall the association between face, name, and occupation (total FNAT), which was significantly enhanced in both Experiments 1 and 2. However, we also aimed to explore the individual contributions of name and occupation separately to gain a deeper understanding of the results. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall. We understand that this may have caused some confusion. Therefore we will clarify this in the manuscript and consider presenting the name and occupation in a separate plot.

Regarding the stimulation conditions, your concerns about the performance pattern (iTBS+gtACS > iTBS+sham-tACS, but iTBS+gtACS ~ sham+sham) are understandable. However, this new protocol was developed precisely in response to the variability observed in behavioral outcomes following non-invasive brain stimulation, particularly when used to modulate memory functions (Corp et al., 2020; Pabst et al., 2022). As discussed in the manuscript, it is intended as a boost to conventional non-invasive brain stimulation protocols, leveraging the mechanisms outlined in the Discussion section.

Reviewer #2 (Public review):

Weaknesses:

(1) The study did not include a condition where γtACS was applied alone. This was likely because a previous work indicated that a single 3-minute γtACS did not produce significant effects, but this limits the ability to isolate the specific contribution of γtACS in the context of this target and memory function

Thank you for your comments. As you pointed out, we did not include a condition where γtACS was applied alone. This decision was based on the findings of Guerra et al. (Brain Stimulation 2018), who investigated the same protocol and reported no aftereffects. Given the substantial burden of the experimental design on patients and our primary goal of demonstrating an enhancement of effects compared to the standalone iTBS protocol, we decided to leave out this condition. However, we agree that investigating the effects of γtACS alone is an interesting and relevant aspect worthy of further exploration. In line with these observations, we will expand the discussion on this point in the study’s limitations section.

(2) The authors applied stimulation for 3 minutes, which seems to be based on prior tACS protocols. It would be helpful to present some rationale for both the duration and timing relative to the learning phase of the memory task. Would you expect additional stimulation prior to recall to benefit long-term associative memory?

Thank you for your comment and for raising this interesting point. As you correctly noted, the protocol we used has a duration of three minutes, a choice based on previous studies demonstrating its greater efficacy with respect to single stimulation from a neurophysiological point of view. Specifically, these studies have shown that the combined stimulation enhanced gamma-band oscillations and increased cortical plasticity (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Given that the precuneus (Brodt et al., Science 2018; Schott et al., Human Brain Mapping 2018), gamma oscillations (Osipova et al., Journal of Neuroscience 2006; Deprés et al., Neurobiology of Aging 2017; Griffiths et al., Trends in Neurosciences 2023), and cortical plasticity (Brodt et al., Science 2018) are all associated with encoding processes, we decided to apply the co-stimulation immediately before it to enhance the efficacy.

Regarding the question of whether stimulation could also benefit recall, the answer is yes. We can speculate that repeating the stimulation before recall might provide an additional boost. This is supported by evidence showing that both the precuneus and gamma oscillations are involved in recall processes (Flanagin et al., Cerebral Cortex 2023; Griffiths et al., Trends in Neurosciences 2023). Furthermore, previous research suggests that reinstating the same brain state as during encoding can enhance recall performance (Javadi et al., The Journal of Neuroscience 2017).

We will expand the study rationale and include these considerations in the future directions section.

(3) How was the burst frequency of theta iTBS and gamma frequency of tACS chosen? Were these also personalized to subjects' endogenous theta and gamma oscillations? If not, were increases in gamma oscillations specific to patients' endogenous gamma oscillation frequencies or the tACS frequency?

The stimulation protocol was chosen based on previous studies (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Gamma tACS sinusoid frequency wave was set at 70 Hz while iTBS consisted of ten bursts of three pulses at 50 Hz lasting 2 s, repeated every 10 s with an 8 s pause between consecutive trains, for a total of 600 pulses total lasting 190 s (see iTBS+γtACS neuromodulation protocol section). In particular, the theta iTBS has been inspired by protocols used in animal models to elicit LTP in the hippocampus (Huang et al., Neuron 2005). Consequently, neither Theta iTBS nor the gamma frequency of tACS were personalized. The increase in gamma oscillations was referred to the patient’s baseline and did not correspond to the administrated tACS frequency.

(4) The authors do a thorough job of analyzing the increase in gamma oscillations in the precuneus through TMS-EEG; however, the authors may also analyze whether theta oscillations were also enhanced through this protocol due to the iTBS potentially targeting theta oscillations. This may also be more robust than gamma oscillations increases since gamma oscillations detected on the scalp are very low amplitude and susceptible to noise and may reflect activity from multiple overlapping sources, making precise localization difficult without advanced techniques.

Thank you for the suggestion. We analyzed theta oscillations finding no changes.

(5) Figure 4: Why are connectivity values pre-stimulation for the iTBS and sham tACS stimulation condition so much higher than the dual stimulation? We would expect baseline values to be more similar.

We acknowledge that the pre-stimulation connectivity values for the iTBS and sham tACS conditions appear higher than those for the dual stimulation condition. However, as noted in our statistical analyses, there were no significant differences at baseline between conditions (p-FDR= 0.3514), suggesting that any apparent discrepancy is due to natural variability rather than systematic bias. One potential explanation for these differences is individual variability in baseline connectivity measures, which can fluctuate due to factors such as intrinsic neural dynamics, participant state, or measurement noise. Despite these variations, our statistical approach ensures that any observed post-stimulation effects are not confounded by pre-existing differences.

(6) Figure 2: How are total association scores significantly different between stimulation conditions, but individual name and occupation associations are not? Further clarification of how the total FNAT score is calculated would be helpful.

We apologize for any lack of clarity. The total FNAT score reflects the ability to correctly recall all the information associated with a person—specifically, the correct pairing of the face, name, and occupation. Participants received one point for each triplet they accurately recalled. The scores were then converted into percentages, as detailed in the Face-Name Associative Task Construction and Scoring section in the supplementary materials.

Total FNAT was the primary outcome measure. However, we also analyzed name and occupation recall separately to better understand their individual contributions. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall.

We acknowledge that this distinction may have caused some confusion. To improve clarity, we will revise the manuscript accordingly and consider presenting name and occupation recall in separate plots.

Reviewer #3 (Public review):

Weaknesses:

I want to state clearly that I think the strengths of this study far outweigh the concerns I have. I still list some points that I think should be clarified by the authors or taken into account by readers when interpreting the presented findings.

I think one of the major weaknesses of this study is the overall low sample size in all of the experiments (between n = 10 and n = 20). This is, as I mentioned when discussing the strengths of the study, partly mitigated by the within-subject design and individualized stimulation parameters. The authors mention that they performed a power analysis but this analysis seemed to be based on electrophysiological readouts similar to those obtained in experiment 3. It is thus unclear whether the other experiments were sufficiently powered to reliably detect the behavioral effects of interest. That being said, the authors do report significant effects, so they were per definition powered to find those. However, the effect sizes reported for their main findings are all relatively large and it is known that significant findings from small samples may represent inflated effect sizes, which may hamper the generalizability of the current results. Ideally, the authors would replicate their main findings in a larger sample. Alternatively, I think running a sensitivity analysis to estimate the smallest effect the authors could have detected with a power of 80% could be very informative for readers to contextualize the findings. At the very least, however, I think it would be necessary to address this point as a potential limitation in the discussion of the paper.

Thank you for the observation. As you mentioned, our power analysis was based on our previous study investigating the same neuromodulation protocol with a corresponding experimental design. The relatively small sample could be considered a possible limitation of the study which we will add to the discussion. A fundamental future step will be to replay these results on a larger population, however, to strengthen our results we performed the sensitivity analysis you suggested.

In detail, we performed a sensitivity analysis for repeated-measures ANOVA with α=0.05 and power(1-β)=0.80 with no sphericity correction. For experiment 1, a sensitivity analysis with 1 group and 3 measurements showed a minimal detectable effect size of f=0.524 with 20 participants. In our paper, the ANOVA on total FNAT immediate performance revealed an effect size of η2\=0.274 corresponding to f=0.614; the ANOVA on FNAT delayed performance revealed an effect size of η2 =0.236 corresponding to f=0.556. For experiment 2, a sensitivity analysis for total FNAT immediate performance (1 group and 3 measurements) showed a minimal detectable effect size of f=0.797 with 10 participants. In our paper, the ANOVA on total FNAT immediate performance revealed an effect size of η2 =0.448 corresponding to f=0.901. The sensitivity analysis for total FNAT delayed performance (1 group and 6 measurements) showed a minimal detectable effect size of f=0.378 with 10 participants. In our paper, the ANOVA on total FNAT delayed performance revealed an effect size of η2 =0.484 corresponding to f=0.968. Thus, the sensitivity analysis showed that both experiments were powered enough to detect the minimum effect size computed in the power analysis. We have now added this information to the manuscript and we thank the reviewer for her/his suggestion.

It seems that the statistical analysis approach differed slightly between studies. In experiment 1, the authors followed up significant effects of their ANOVAs by Bonferroni-adjusted post-hoc tests whereas it seems that in experiment 2, those post-hoc tests where "exploratory", which may suggest those were uncorrected. In experiment 3, the authors use one-tailed t-tests to follow up their ANOVAs. Given some of the reported p-values, these choices suggest that some of the comparisons might have failed to reach significance if properly corrected. This is not a critical issue per se, as the important test in all these cases is the initial ANOVA but non-significant (corrected) post-hoc tests might be another indicator of an underpowered experiment. My assumptions here might be wrong, but even then, I would ask the authors to be more transparent about the reasons for their choices or provide additional justification. Finally, the authors sometimes report exact p-values whereas other times they simply say p < .05. I would ask them to be consistent and recommend using exact p-values for every result where p >= .001.

Thank you again for the suggestions. Your observations are correct, we used a slightly different statistical depending on our hypothesis. Here are the details:

In experiment 1, we used a repeated-measure ANOVA with one factor “stimulation condition” (iTBS+γtACS; iTBS+sham-tACS; sham-iTBS+sham-tACS). Following the significant effect of this factor we performed post-hoc analysis with Bonferroni correction.

In experiment 2, we used a repeated-measures with two factors “stimulation condition” and “time”. As expected, we observed a significant effect of condition, confirming the result of experiment 1, but not of time. Thus, this means that the neuromodulatory effect was present regardless of the time point. However, to explore whether the effects of stimulation condition were present in each time point we performed some explorative t-tests with no correction for multiple comparisons since this was just an explorative analysis.

In experiment 3, we used the same approach as experiment 1. However, since we had a specific hypothesis on the direction of the effect already observed in our previous study, i.e. increase in spectral power (Maiella et al., Scientific Report 2022), our tests were 1-tailed.

For the p-values, we will correct the manuscript reporting the exact values for every result.

While the authors went to great lengths trying to probe the neural changes likely associated with the memory improvement after stimulation, it is impossible from their data to causally relate the findings from experiments 3 and 4 to the behavioral effects in experiments 1 and 2. This is acknowledged by the authors and there are good methodological reasons for why TMS-EEG and fMRI had to be collected in sperate experiments, but it is still worth pointing out to readers that this limits inferences about how exactly dual iTBS and γtACS of the precuneus modulate learning and memory.

Thank you for your comment. We fully agree with your observation, which is why this aspect has been considered in the study's limitations. To address your concern, we will further emphasize the fact that our findings do not allow precise inferences regarding the specific mechanisms by which dual iTBS and γtACS of the precuneus modulate learning and memory.

There were no stimulation-related performance differences in the short-term memory task used in experiments 1 and 2. The authors argue that this demonstrates that the intervention specifically targeted long-term associative memory formation. While this is certainly possible, the STM task was a spatial memory task, whereas the LTM task relied (primarily) on verbal material. It is thus also possible that the stimulation effects were specific to a stimulus domain instead of memory type. In other words, could it be possible that the stimulation might have affected STM performance if the task taxed verbal STM instead? This is of course impossible to know without an additional experiment, but the authors could mention this possibility when discussing their findings regarding the lack of change in the STM task.

Thank you for your insightful observation. We argue that the intervention primarily targeted long-term associative memory formation, as our findings demonstrated effects only on FNAT. However, as you correctly pointed out, we cannot exclude the possibility that the stimulation may also influence short-term verbal associative memory. We will acknowledge this potential effect when discussing the absence of significant findings in the STM task.

While the authors discuss the potential neural mechanisms by which the combined stimulation conditions might have helped memory formation, the psychological processes are somewhat neglected. For example, do the authors think the stimulation primarily improves the encoding of new information or does it also improve consolidation processes? Interestingly, the beneficial effect of dual iTBS and γtACS on recall performance was very stable across all time points tested in experiments 1 and 2, as was the performance in the other conditions. Do the authors have any explanation as to why there seems to be no further forgetting of information over time in either condition when even at immediate recall, accuracy is below 50%? Further, participants started learning the associations of the FNAT immediately after the stimulation protocol was administered. What would happen if learning started with a delay? In other words, do the authors think there is an ideal time window post-stimulation in which memory formation is enhanced? If so, this might limit the usability of this procedure in real-life applications.

Thank you for your comment and for raising these important points.

We hypothesized that co-stimulation would enhance encoding processes. Previous studies have shown that co-stimulation can enhance gamma-band oscillations and increase cortical plasticity (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Given that the precuneus (Brodt et al., Science 2018; Schott et al., Human Brain Mapping 2018), gamma oscillations (Osipova et al., Journal of Neuroscience 2006; Deprés et al., Neurobiology of Aging 2017; Griffiths et al., Trends in Neurosciences 2023), and cortical plasticity (Brodt et al., Science 2018) have all been associated with encoding processes, we decided to apply co-stimulation before the encoding phase, to boost it.

We applied the co-stimulation immediately before the learning phase to maximize its potential effects. While we observed a significant increase in gamma oscillatory activity lasting up to 20 minutes, we cannot determine whether the behavioral effects we observed would have been the same with a co-stimulation applied 20 minutes before learning. Based on existing literature, a reduction in the efficacy of co-stimulation over time could be expected (Huang et al., Neuron 2005; Thut et al., Brain Topography 2009). However, we hypothesize that multiple stimulation sessions might provide an additional boost, helping to sustain the effects over time (Thut et al., Brain Topography 2009; Koch et al., Neuroimage 2018; Koch et al., Brain 2022).

Regarding the absence of further forgetting in both stimulation conditions, we think that the clinical and demographical characteristics of the sample (i.e. young and healthy subjects) explain the almost absence of forgetting after one week.

Author response:

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

The study is well-executed and provides many interesting leads for further experimental studies, which makes it very important. One of the significant hypotheses in this context is metazoan Wnt Lipocone domain interactions with lipids, which remain to be explored.

The manuscript is generally navigable for interesting reading despite being content-rich. Overall, the figures are easy to follow.

We thank the reviewer for the thoughtful and favorable assessment.

Major comments:

I urge the authors to consider creating a first figure summarizing the broad approach and process involved in discovering the lipocone superfamily. This would help the average reader easily follow the manuscript.

It will be helpful to have the final model/synthesis figure, which provides a take-home message that combines the main deductions from Fig 1c, Fig 4, Fig 5, and Fig 6 to provide an eagle's eye view (also translating the arguments on Page 38 last para into this potential figure).

We have generated a two-part figure that synthesizes these two requests, also in line with the recommendations made by Reviewer 3. Depending on the accepting Review Commons journal, we plan to either submit this as a graphical abstract/TOC figure (as suggested by Reviewer 3) or as a single figure. We prefer starting with the first approach as it will keep our figure count the same.

Minor comments:

Fig 1C: The authors should provide a statistical estimate of the difference in transmembrane tendency scores between the "membrane" and "globular" versions of the Lipocone domains.

To address this, we calculated group-wise differences using the Kruskal-Wallis nonparametric test, followed by Dunn’s test with Bonferroni correction for a more stringent evaluation. The results of which are presented as a critical difference diagram in the new Supplementary Figure S3. The analysis is explained in the Methods section of the revised manuscript, and the statistically significant difference is mentioned in the text. This analysis identifies three groups of significantly different Lipocone families based on their transmembrane tendency: those predicted (or known) to associate with the prokaryotic membranes, those predicted to be diffusible, and a small number of families residing eukaryotic ER membranes or bacterial outer membranes.

Reviewer #2 (Evidence, reproducibility and clarity):

This is a remarkable study, one of a kind. The authors trace the entire huge superfamily containing Wnt proteins which origins remained obscure before this work. Even more amazingly, they show that Wnts originated from transmembrane enzymes. The work is masterfully executed and presented. The conclusions are strongly supported by multiple lines of evidence. Illustrations are beautifully crafted. This is an exemplary work of how modern sequence and structure analysis methods should be used to gain unprecedented insights into protein evolution and origins.

We thank the reviewer for the positive evaluation of our work.

Minor comments.

(1) In fig 1, VanZ structure looks rather different from the rest and is a more tightly packed helical bundle. It might be useful for the readers to learn more about the arguments why authors consider this family to be homologous with the rest, and what caused these structural changes in packing of the helices.

First, the geometry of an α-helix can be approximated as a cylinder, resulting in contact points that are relatively small. Fewer contact constraints can lead to structural variation in the angular orientations between the helices of an all α-helical domain, resulting in some dispersion in space of the helical axes. As a result, some of the views can be a bit confounding when presented as static 2D images. Second, of the two VanZ clades the characteristic structure similar to the other superfamily members is more easily seen in the VanZ-2 clade (as illustrated in supplementary Figure S2).    

Importantly, the membership of the VanZ domains was recovered via significant hits in our sequence analysis of the superfamily. Importantly, when the sequence alignments of the active site are compared (Figure 2), VanZ retains the conserved active site residue positions, which are predicted to reside spatially in the same location and project into an equivalent active site pocket as seen in the other families in the superfamily. Further, this sequence relationship is captured by the edges in the network in Figure 1B: multiple members of the superfamily show edges indicating significant relationships with the two VanZ families (e.g., HHSearch hits of probability greater than 90%; p<0.0001 are observed between VanZ-1 and Skillet-DUF2809, Skillet-1, Skillet-4, YfiM-1, YfiM-DUF2279, Wok, pPTDSS, and cpCone-1). Thus, they occupy relatively central locations in the sequence similarity network, indicating a consistent sequence similarity connection to multiple other families.

(2) Fig. 4 color bars before names show a functional role. How does the blue bar "described for the first time" fits into this logic? Maybe some other way to mark this (an asterisk?) could be better to resolve this sematic inconsistency.

We have shifted the blue bars into asterisks, which follow family names, now stated in the updated legend.

Reviewer #3 (Evidence, reproducibility and clarity):

The manuscript by Burroughs et al. uses informatic sequence analysis and structural modeling to define a very large, new superfamily which they dub the Lipocone superfamily, based on its function on lipid components and cone-shaped structure. The family includes known enzymatic domains as well as previously uncharacterized proteins (30 families in total). Support for the superfamily designation includes conserved residues located on the homologous helical structures within the fold. The findings include analyses that shed light on important evolutionary relationships including a model in which the superfamily originated as membrane proteins where one branch evolved into a soluble version. Their mechanistic proposals suggest possible functions for enzymes currently unassigned. There is also support for the evolutionary connection of this family with the human immune system. The work will be of interest to those in the broad areas of bioinformatics, enzyme mechanisms, and evolution. The work is technically well performed and presented.

We appreciate the positive evaluation of our work by the reviewer.

Referees cross-commenting

All the comments seem useful to me. I like Reviewer 1's suggestion for a flowchart showing the methodology. I think the summarizing figure suggested could be a TOC abstracvt, which many journals request.

To accommodate this comment (along with Reviewer 1’s comments), we have generated a two-part figure containing the methodology flowchart and the summary of findings. Combining the two provides some before-and-after symmetry to a TOC figure, while also avoiding further inflation of the figure count, which would likely be an issue at one or more of the Review Commons journals.

The authors may wish to consider the following points (page numbers from PDF for review):

(1) It would be useful in Fig 1A, either in main text or the supporting information, to also have a an accompanying topology diagram- I like the coloring of the helices to show the homology but the connections between them are hard to follow

We acknowledge the reviewer’s concern as one shared by ourselves. We have placed such a topology diagram in Figure 1A, and now refer to it at multiple points in the manuscript text.

(2) Page: 6- In the paragraph marked as an example- please call out Fig1A when the family mentioned is described (I believe SAA is described as one example)

We have added these pointers in the text, where appropriate.

(3) Page: 7- The authors state "these 'hydrophobic families' often evince a deeper phyletic distribution pattern than the less-hydrophobic families (Figure S1), implying that the ancestral version of the superfamily was likely a TM domain" there should be more explanation or information here - I am not certain from looking at FigS1 what a deeper phyletic distribution pattern means. Perhaps explaining for a single example? I also see that this important point is discussed in the conclusions- it is useful to point to the conclusion here.

Our use of the ‘deeper’ in this context is meant to convey the concept that more widely conserved families/clades (both across and within lineages) suggest an earlier emergence. In the Lipocone superfamily, this phylogenetic reasoning supports an evolutionary scenario where the membrane-inserted versions generally emerged early, while the solubilized versions, which are found in relatively fewer lineages, emerged later.

To address this objectively, we have calculated a simple phyletic distribution metric that combines the phyletic spread of a Lipocone clade with its depth within individual lineages, which is then plotted as a bargraph (Supplemental Figure S1). Briefly, this takes the width of the bar as the phyletic spread across the number of distinct taxonomic lineages and its height as a weighted mean of occurrence within each lineage (depth). The latter helps dampen the effects of sampling bias. In the resulting graph, lineages with a lower height and width are likely to have been derived later than those with a greater height and width. A detailed description clarifying this has been added to the Methods section of the revised manuscript. The results support two statements that are made in the text: 1) that the Wok and VanZ clades are the most widely and deeply represented clades in the superfamily, and 2) that the predicted transmembrane versions tend to be more widely and deeply distributed. We have also added a statement in the results with a pointer to Figure S1 to clarify this point raised by the referee.

(4) For figure 3 I would suggest instead of coloring by atom type- to color the leaving group red and the group being added blue so the reader can see where the moieties start and end in substrates and products

We have retained the atom type coloring in the figure for ease of visualizing the atom types. However, to address the reviewer’s concern, we have added dashed colored circles to highlight attacking and leaving groups in the reactions. The legend has been updated accordingly.

(5) Page: 13- The authors state "While the second copy in these versions is catalytically inactive, the H1' from the second duplicate displaces the H1 from the first copy," So this results in a "sort of domain swap" correct? It may be more clear to label both copies in Figure 3 upper right so it is easier for the reader to follow.

We have added these labels to the updated Figure S4 (formerly S3).

(6) The authors state "In addition to the fusion to the OMP β-barrel, the YfiM-DUF2279 family (Figure 5H) shows operonic associations with a secreted MltG-like peptidoglycan lytic transglycosylase (127,128), a lipid anchored cytochrome c heme-binding domain (129), a phosphoglucomutase/phosphomannomutase enzyme (130), a GNAT acyltransferase (131), a diaminopimelate (DAP) epimerase (132), and a lysozyme like enzyme (133). In a distinct operon, YfiM-DUF2279 is combined with a GT-A glycosyltransferase domain (79), a further OMP β-barrel, and a secreted PDZ-like domain fused to a ClpP-like serine protease (134,135) (Figure 5H)." this combination of enzymes sounds like those in the pathways for oligosaccharide synthesis which is cytoplasmic but the flippase acts to bring the product to the periplasm. Please make sure it is clear that these enzymes may act at different faces of the membrane.

We have made that point explicit in the revised manuscript in the paragraph following the above-quoted statement.

(7) Page: 21- the authors should remove the unpublished observations on other RDD domain or explain or cite them

The analysis of the RDD domain is a part of a distinct study whose manuscript we are currently preparing, and explaining its many ramifications would be outside the scope of this manuscript. Moreover, placing even an account of it in this manuscript would break its flow and take the focus away from the Lipocone superfamily. Further, its inclusion of the RDD story would substantially increase the size of the manuscript. However, it is commonly fused to the Lipocone domain; hence, it would be remiss if we entirely remove a reference to it. Accordingly, we retain a brief account of the RDD-fused Lipocone domains in the revised manuscript that is just sufficient to make the relevant functional case”.

(8) Page: 34- The authors state "For instance, the emergence of the outer membrane in certain bacteria was potentially coupled with the origin of the YfiM and Griddle clades (Figure 4)." I don't see origin point indicated in figure 4 (emergence of outer membrane- this may be helpful to indicate in some way- also I am not certain what the dashed circles in Fig 4 are indicating- its not in the legend?

This annotation has been added to the revised Figure 4, and the point of recruitment is indicated with a  “X” sign, along with a clarification in the legend regarding the dashed circles.

(9) In terms of the hydrophobicity analysis, it would be good to mark on the plot (Fig 1C) one or two examples of lipocone members with known structure that are transmembrane proteins as a positive control

We have added these markers (colored triangles and squares for these families to the plot.

Grammar, typos

Page: 3- abstract severance is an odd word to use for hydrolysis or cleavage

We have changed to “cleavage”.

Page: 5- "While the structure of Wnt was described over a decade prior" should read "Although the structure of ..."

Page 7 - "One family did not yield a consistent prediction for orientation"- please state which family

Page: 8 "While the ancestral pattern is noticeably degraded in the metazoan Wnt (Met-Wnt) family, it is strongly preserved in the prokaryotic Min-Wnt family." Should read "Although the ancestral..."

throughout- please replace solved with experimentally determined to be clear and avoid jargon

Please replace "TelC severs the link" with "TelC cleaves the bond "

We have made the above changes.

Page: 19- the authors state "a lipobox-containing synaptojanin superfamily phosphoesterase (125) and a secreted R-P phosphatase (126) (see Figure 6, Supplementary Data)" I was uncertain if the authors meant Fig S6 or they meant see Fig 6 and something else in supplementary data. Please fix.

In this pointer, we intended to flag the relevant gene neighborhoods in both Figures 5H and 6, as well as highlight the additional examples contained in the Supplementary Data. We have updated the point

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):*

As stated by the authors in the introduction, the RNA-binding protein Sxl is foundational to understanding sex determination in Drosophila. Sxl has been extensively studied as the master regulator of female sex determination in the soma, where it is known to initiate an alternative splicing cascade leading to the expression of DsxF. Additionally, Sxl has been shown to be responsible for keeping X chromosome dosage compensation off in females, while males hyperactivate their X chromosome. While these roles have been well defined, the authors explore an aspect of Sxl that is quite separate from its role as master regulator of female fate. They describe Sxl-RAC, a Sxl isoform that is expressed in the male and female nervous system. Using several genomic techniques, the authors conclude that the Sxl-RAC isoform associates with chromatin in a similar pattern to the RNA polymerase II/III subunit, Polr3E, and Sxl depends on Polr3E for chromatin-association. Further, neuronal loss of Sxl causes changes in lifetime and geotaxis in a similar manner as loss of Polr3E. The work is thorough and significant and should be appropriate for publication if a few issues can be addressed.

Major Concerns:*

* 1) How physiological is the Sxl chromatin-association assay? As binding interactions are concentration-dependent, how similar is Sxl-DAM expression to wt Sxl expression in neurons? In addition, does the Sxl-DAM protein function as a wt Sxl protein? Does UAS-Sxl-DAM rescue any Sxl loss phenotypes?*

Author response:

As Reviewer 3 correctly notes, Targeted DamID relies on ribosomal re-initiation (codon slippage) to produce only trace amounts of the Dam-fusion protein. By design, this results in expression levels that are significantly lower than those of the endogenous protein. As such, the experiment can be interpreted within a near–wild-type context, rather than as an overexpression model. The primary aim of this experiment was to determine whether Sxl associates with chromatin, and our dataset provides clear evidence supporting such binding.

2) Is Polr3E chromatin-association also dependent on Sxl? They should do the reciprocal experiment to their examination of Sxl chromatin-association in Polr3E knockdown. This might also help address point 1-if wt Sxl is normally required for aspects of Polr3E chromatin binding, then concerns about whether the Sxl-DAM chromatin-association is real or artifactual would be assuaged.

Author response:

This is an interesting thought, however, if Sxl were required for Polr3E recruitment to RNA Pol III, then, in most male Drosophila melanogaster cells, Polr3E would not be incorporated, and males would not be viable (as it is essential for Pol III activity). While it is possible that there could be a subtle effect on Polr3E recruitment, such an experiment, would not alter the central conclusion of our study - that Sxl is recruited to chromatin (accessory to the Pol III complex) via Polr3E.

Minor concerns:

* The observed Sxl loss of function phenotypes are somewhat subtle (although perhaps any behavior phenotype at all is a plus). Did they try any other behaviour assays-courtship, learning/memory, anything else at all to test nervous system function?*

Author response:

Given the exploratory nature of this study, we focused on broader behavioural and transcriptional assays.

While well written, it is sometimes difficult to understand how the experiment was performed or what genotypes were used without looking into the methods sections. One example is they should describe the nature of the Sxl-DAM fusion protein clearly in the results.

Author response:

We will revise these sections to improve clarity and ensure there is no confusion.

* Reviewer #1 (Significance (Required)):

This manuscript represents a dramatic change in our thinking about the action of the Sex-lethal protein. Previously, Sxl was known as the master regulator of both sex determination and dosage compensation, and performed these roles as an RNA-binding protein affecting RNA splicing and translational regulation. Here, the authors describe a sex-non-specific role of Sxl in the male and female nervous system. Further, this activity appears independent of Sxl's RNA binding activity and instead Sxl functions as a chromatin-associating protein working with the RNA pol2/3 factor Polr3E to regulate gene expression. Thus, this represents a highly significant finding. *

Reviewer #2 (Evidence, reproducibility and clarity (Required)):*

Summary: In this paper, the authors report on an unexpected activity for Sex lethal (Sxl) (a known splicing regulator that functions in sex determination and dosage compensation) in binding to chromatin. They show, using DamID, that Sxl binds to approximately the same chromatin regions as Polr3E (a subunit of RNA Pol III). They show that this binding to chromatin is unaffected by mutations in the RNA binding domains or by deletions of either N or C terminal regions of the Sxl protein. This leads the authors to conclude that Sxl must bind to chromatin through some interacting protein working through the central region of the Sxl protein. They show that Sxl binding is dependent on Polr3E function. They show that male-specific neuronal knockdown of Sxl gives similar phenotypes to knockdown of Polr3E in terms of lethality and improved negative geotaxis. They show gene expression changes with knockdown of Sxl in male adult neurons - mainly that metabolic and pigmentation genes go down in expression. They also show that expression of a previously discovered male adult specific form of Sxl (that does not have splicing activity) in the same neurons also leads to changes in gene expression, including more upregulated than downregulated tRNAs. But they don't see (or don't show) that the same tRNA genes are down with knockdown of Sxl. Nonetheless, based on these findings, they suggest that Sxl plays an important role in regulating Pol III activity through the Polr3E subunit.

Major comments:

*

*To be honest, I'm not convinced that the conclusions drawn from this study are correct. The fact that every mutant form of Sxl shows the same result from the DamID labelling is a little concerning. I would like to see independent evidence of the SxlRac protein binding chromatin. *

Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

__Author Response: __

Regarding the reviewer’s overall concerns about the legitimacy of the Sxl binding data:

1. i) The fold differences between Dam-Sxl-mutants and the Dam-only control are very robust (up to 9 log2 fold change (500-fold change)), which is higher than what we observe with most transcription factors using Targeted DamID.

2. ii) We observed that Sxl binding was significantly reduced upon knockdown of Polr3E, confirming that the signal we observe is biologically specific and not due to technical noise or background. iii) If the concern relates to potential Sxl binding in non-neuronal tissues such as salivary glands, we would like to clarify that all DamID constructs were expressed under elav-GAL4, a pan-neuronal driver. Furthermore, dissections were performed to isolate larval brains, with salivary glands carefully removed. This ensures that chromatin profiles were derived from neuronal tissue exclusively.

3. iv) Salivary gland polytene chromosome staining with a Sxl antibody in a closely related species (Drosophila virilis) show __binding of Sxl to chromatin __in both sexes (Bopp et al., 1996). We will include more text in the revised manuscript to emphasise these points.

Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

Author Response:

Prior work in Drosophila virilis (where Sxl is also required for sex determination and Sxl-RAC is conserved) has already demonstrated Sxl-chromatin association (using a full-length Sxl antibody) in salivary glands using polytene chromosome spreads (Bopp et al., 1996). Binding is observed in both sexes and across the genome, reflecting our observations. We will incorporate this into the revised discussion to support the chromatin-binding role of Sxl across species.

There is a clear and long-overlooked precedent for Sxl's alternative, sex-independent roles, findings that have been largely overshadowed by the gene’s canonical function. Our study not only validates and extends these observations but also brings much-needed attention to this understudied aspect of fundamental biology.

Bopp D, Calhoun G, Horabin JI, Samuels M, Schedl P. Sex-specific control of Sex-lethal is a conserved mechanism for sex determination in the genus Drosophila. Development. 1996 Mar;122(3):971-82. doi: 10.1242/dev.122.3.971. PMID: 8631274.

I would like to see independent evidence of the SxlRac protein binding chromatin.

* *__Author Response: __

We do not believe this is necessary:

1. i) Our data demonstrated that a large N-terminal truncation of Sxl (removing far more of the N-terminal region than is absent in Sxl-RAC) does not impair chromatin binding.
2. ii) Our deletion experiments show that it is the central domain __of Sxl that is required for chromatin association (as removal of the N-or C-terminal domain has no effect). This central domain is __unaffected in Sxl-RAC. iii) Independent Y2H experiments have shown that it is exclusively the__ RBD-1 __(RNA binding domain 1) of the central domain of Sxl that interacts with Polr3E (Dong et al., 1999). Sxl-RAC contains this region, therefore will be recruited by Polr3E.

iv) Review 3 also believes that this is not necessary (see cross-review below) and highlights the robustness of the Y2H experiments performed by Dong et al., 1999.

• *

Also, given that their DamID experiments reveal that Sxl binds half of the genes encoded in the Drosophila genome, finding that it binds around half of the tRNA genes is perhaps not surprising.

__Author Response: __

Our data show that Sxl binds to a range of Pol III-transcribed loci, and this binding pattern supports the proposed model that Sxl plays a broader regulatory role in Pol III activity. Within these Pol III targets, tRNA genes represent a specific and biologically relevant subset. The emphasis on tRNAs is not to suggest they are the exclusive or primary targets of Sxl, but rather to__ highlight a functionally important class of Pol III-transcribed elements__ that align with the model we are proposing. We will revise the text to better reflect this framing and avoid any confusion regarding the scope of Sxl’s binding profile.

*I would like to see evidence beyond citing a 1999 yeast two-hybrid study that Sxl and Polr3E directly interact with one another. *

Author response:

We do not believe this is necessary (these points were also mentioned above):

1. i) The Dong et al., 1999 study was highly comprehensive in its characterisation of Sxl binding to Polr3E.
2. ii) Our DamID data provide strong complementary evidence for this interaction: knockdown of Polr3E robustly reduces Sxl’s recruitment to chromatin, strongly supporting the relevance of the interaction in vivo. iii) Review 3 highlights the robustness of the Y2H experiments performed by Dong et al., 1999.

In my opinion, the differences in lethality observed with loss of Sxl versus control are unlikely to be meaningful given the different genetic backgrounds. The similar defects in negative geotaxis could be meaningful, but I'm unsure how often this phenotype is observed. What other class of genes affect negative geotaxis? It's a little unclear why having reduced expression of metabolic and pigment genes or of tRNAs would improve neuronal function.

Author response:

While the differences in survival were indeed subtle, they were statistically significant and thus warranted inclusion. Our primary aim in this section was to demonstrate that knockdown of Sxl or Polr3E results in comparable behavioural and transcriptional phenotypes, suggesting overlapping functional roles. In this context, we believe the data were presented transparently and effectively support our interpretation.

Regarding the negative geotaxis phenotype, we appreciate the reviewer’s interest and agree that it is both intriguing and atypical. For this reason, we performed the assay multiple times, particularly in Polr3e knockdowns, to confirm the robustness of the result. To address potential confounding variables, we carefully selected control lines that account for genetic background and transgene insertion site, including KK controls and attP40-matched lines. We also employed multiple independent RNAi lines targeting Sxl to validate the phenotype across different genetic backgrounds.

Although the observed improvement in climbing is unexpected, it is not without precedent in the RNA polymerase III field. Notably, Malik et al. (2024) demonstrated that heterozygous Polr3DEY/+ mutants exhibit a significantly delayed decline in climbing ability with age. We allude to this in the discussion and will revise the text to emphasise this connection more explicitly.

Finally, while we recognise that negative geotaxis is a relatively broad assay and thus does not pinpoint the precise cellular mechanisms involved, we interpret the phenotype as suggesting a neural basis and a functional role for Sxl in the nervous system.

One would expect that not just the same classes of genes would be affected by loss and overexpression of Sxl, but the same genes would be affected - are the same genes changing in opposite directions in the two experiments or just the same classes of genes. Likewise, are the same genes changing expression in the same direction with both Sxl and the Polr3E loss? Also, why are tRNA genes not also affected with Sxl loss. Finally, they describe the changes in gene expression as being in male adult neurons, but the sequencing was done of entire heads - so no way of knowing which cell type is showing differential gene expression.

Author response:

While we do examine gene classes, our approach also includes pairwise correlation analyses of gene expression changes between specific genotypes. Notably, we observed a significant positive correlation between Polr3e knockdowns and Sxl knockdowns, and a significant negative correlation between Sxl-RAC–expressing flies and Sxl knockdowns. Furthermore, we examined Sxl-DamID target genes within our RNA-seq datasets and found a consistent relationship between Sxl targets and genes differentially expressed in Polr3e knockdowns.

Regarding the Pol III qPCR results, we note that tRNA expression changes may require a longer duration of RNAi induction (e.g., beyond 4 days) to become apparent, especially given that phenotypic effects such as changes in lifespan and negative geotaxis only emerge after 20 days or more. It is also plausible that Sxl knockdown leads to a partial reduction in Pol III efficiency, which may not be readily detectable through bulk Pol III qPCRs. We are willing to repeat Pol III qPCRs at later timepoints to further investigate this trend.

Finally, we infer that gene expression changes observed in our RNA-seq data are of neuronal origin, as all knockdown and overexpression constructs used in this study were driven pan-neuronally using elav-/nSyb-GAL4. While we acknowledge that bulk RNA-seq does not provide cell-type resolution, tissue-specific assumptions are widely used in the field when driven by a relevant promoter.

I'm also not sure what I'm supposed to be seeing in panel 5F (or in the related supplemental figure) and if it has any meaning - If they are using the Sxl-T2A-Gal4 to drive mCherry, I think one would expect to see expression since Sxl transcripts are made in both males and in females. Also, one would expect to see active protein expression (OPP staining) in most cells of the adult male brain and I think that is what is observed, but again, I'm not sure what I'm supposed to be looking at given the absence of any arrows or brackets in the figures.

Author Response:

Due to the presence of the T2A tag and the premature stop codon in exon 3 of early male Sxl transcripts, GAL4 expression is not expected in males unless the head-specific SxlRAC isoform is produced. The aim of panel 5F is to demonstrate the spatial overlap between SxlRAC expression (as we are examining male brains) and regions of elevated protein synthesis, as detected by OPP staining.

To quantitatively assess this relationship, we performed colocalisation analysis using ImageJ, which showed a positive correlation between Sxl and OPP signal intensity, supporting this interpretation. It is also evident from our images that regions with lower levels of protein synthesis (such as the neuropil - as shown in independent studies Villalobos-Cantor et al., 2023) concurrently lack Sxl-related signal. We have highlighted regions in Fig. 5 exhibiting higher/lower levels of Sxl/OPP signal to better illustrate this relationship. We can also test the effects of knockdown/overexpression on general protein synthesis if required.

Villalobos-Cantor S, Barrett RM, Condon AF, Arreola-Bustos A, Rodriguez KM, Cohen MS, Martin I. Rapid cell type-specific nascent proteome labeling in Drosophila. Elife. 2023 Apr 24;12:e83545. doi: 10.7554/eLife.83545. PMID: 37092974; PMCID: PMC10125018.

Minor comments:

* Line 223 - 225 - I believe that it is expected that Sxl transcripts would be broadly expressed in the male and female adult, given that it is only the spliced form of the transcript that is female specific in expression. *

As explained above, the only isoform that will be ‘trapped’ by the T2A-GAL4 in males is the Sxl-RAC isoform (as the other isoforms contain premature stop codons). Our immunohistochemistry data indicate that Sxl-RAC is expressed in the male brain, specifically in neurons. Therefore, knockdown experiments in males will reduce all mRNA isoforms, of which, Sxl-RAC is the only one producing a protein.

Line 236 - 238 - Sentence doesn't make sense.

We have addressed and clarified this.

Reviewer #2 (Significance (Required)):

It would be significant to discover that a gene previously thought to function in only sex determination and dosage compensation also moonlights as a regulator of RNA polymerase III activity. Unfortunately, I am not convinced by the work presented in this study that this is the case.

My expertise is in Drosophila biology, including development, transcription, sex determination, morphogenesis, genomics, transcriptomics, DNA binding

Reviewer #3 (Evidence, reproducibility and clarity (Required)):*

Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Drosophila Sxl, widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species, is also a chromatin factor that can stimulate transcription by Pol III and Pol II of genes involved with metabolism and protein homeostasis, specifically some encoding tRNAs.

The evidence for the tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments. I have a few specific comments below, all minor.*

Scientific points: - The approach taken for the evaluation of Sxl DNA-binding activity in Fig2 is not entirely clear. I assume these are crosses of elav-Gal4 x different UAS- lines, then using males or females for UAS-Sxl-Full-Length. But what about the others? Were the experiments done in males only? This is hinted at in the main text but not explicitly indicated in the figure or the methods (at least, that I could easily find). And is this approach extended to all other experiments? Longevity? Climbing assays? Considering the role of Sxl, it may be helpful to be fastidiously systematic with this.

Author Response:

We have revised the wording to ensure greater clarity. Males were used for all survival and behavioural experiments (as only males can be leveraged for knocking down Sxl-RAC without affecting the canonical Sxl-F isoform).

- In the discussion, lines 360-61, the authors say: Indeed, knockdown of Polr3E leads to a loss of Sxl binding to chromatin, suggesting a cooperative mechanism. Maybe I am misunderstanding the authors, but when I read "cooperation" in this context I think of biochemical cooperative binding. This is possible, but I do not think a simple 'requirement' test can suggest specifically that this mechanistic feature of biochemical binding is at play. I would expect, for starters, a reciprocal requirement for binding (which is not tested), and some quantitative features that would be difficult to evaluate in vivo. I do not think cooperative binding needs to be invoked anyway, as the authors do not make any specific point or prediction about it. But if they do think this is going on, I think it would need to be referred to as a speculation.

Author Response:

We appreciate that the original wording may have been unclear and will revise the text to more accurately reflect a functional relationship, rather than implying direct cooperation.

- In lines 428-432, the authors discuss the ancestral role of Sxl and make a comparison with ELAV, in the context of an RNA-binding protein that has molecular functions beyond those of a splicing factor, considering the functions of ELAV in RNA stability and translation, and finishing with "suggesting that similar regulatory mechanisms may be at play". I do not understand this latter sentence. Which mechanisms are these? Are the authors referring to the molecular activities of ELAV and SXL? But what would be the similarity? SXL seems to have a dual capacity to bind RNA and protein interactors, which allows it to work both in chromatin-level regulation as well as post-transcriptionally in splicing; but ELAV seems rather to take advantage of its RNA binding function to make it work in multiple RNA-related contexts, all post-transcriptional. I do not see an obvious parallel beyond the fact that RNA binding proteins can function at different levels of gene expression regulation -- but I would not say this parallel are "similar regulatory mechanisms", so I find the whole comparison a bit confusing.

Author Response:

We have reduced this section, as it is largely speculative and intended to highlight potential, though indirect, links in higher organisms. Our goal was primarily to illustrate the possibility that Sxl may have an ancestral role distinct from its well-characterised function, and to suggest a potential avenue for future research into ELAV2’s involvement in chromatin or Pol III regulation.

- One aspect of the work that I find is missing in the discussion is the possibility that the simultaneous capacity of Sxl for RNA binding and Polr3E binding: are these mutually exclusive? if so, are they competitive or hierarchical? how would they be coordinated anyway?

Author Response:

This is an interesting point, and we have expanded on it further in the Discussion section.

- The only aspect of the paper where I found that one could make an experimental improvement is the claim that Sxl induces the expression of genes that have the overall effect of stimulating protein synthesis. The OPP experiment shows a correlation between the expression of Sxl and the rate of protein synthesis initiation. However, a more powerful experiment would be, rather obviously, to introduce Sxl knock-down in the same experiment, and observe whether in Sxl-expressing neurons the incorporation of OPP is reduced. I put this forth as a minor point because the tenet of the paper would not be affected by the results (though the perception of importance of the newly described function could be reinforced).

• *

Author Response:

This could be a valid experiment and we are prepared to perform it if required.

- In a similar way, it would be interesting to know whether the recruitment of Polr3E and Sxl to chromatin is co-dependent or Sxl follows Polr3E. This is also a minor point because this would possibly refine the mechanism of recruitment but does not alter the main discovery.

Author Response:

We have addressed a similar point for Reviewer 2 (see below) and will include a Discussion point for this:

If Sxl were required for Polr3E recruitment to RNA Pol III, then, in most male Drosophila melanogaster cells, Polr3E would not be incorporated, and males would not be viable (as it is essential for Pol III activity). While it is possible that there could be a subtle effect on Polr3E recruitment, such an experiment, would not alter the central conclusion of our study - that Sxl is recruited to chromatin (accessory to the Pol III complex) via Polr3E.

* Figures and reporting:

• In Figure 2, it would be helpful to see the truncation coordinate for the N and C truncations.

• In Figure 3D, genomic coordinates are missing.

• In Figure 3E, the magnitude in the Y axis is not entirely clear (at least not to me). How is the amount of binding across the genome quantified? Is this the average amplitude of normalised TaDa signal across the genome? Or only within binding intervals?

• Figure S3E-F: it would be interesting to show the degree of overlap between the downregulated genes that are also binding targets (regardless of the outcome).

• Figure 5C-E: similarly to Figure S3, it would be interesting to know how the transcriptional effects compare with the binding targets.

• Authors use Gehan-Breslow-Wilcoxon to test survival, which is a bit unusual, as it gives more weight to the early deaths (which are rare in most Drosophila longevity experiments). Is there any rationale behind this? It may be even favour their null hypothesis.*

Author response:

Thank you for the detailed feedback on our figures. We have__ incorporated__ the suggested changes.

We agree that examining the overlap between Sxl binding sites and transcriptional changes is valuable, and we aimed to highlight this in the pie charts shown in Figures S3 and S5. If the reviewer is suggesting a more explicit quantification of the proportion of Sxl-Dam targets with significant transcriptomic changes, we are happy to include this analysis in the final version of the manuscript.

As noted in the Methods, both Gehan–Breslow–Wilcoxon (GBW) and Kaplan–Meier tests were used. The significance in Figure 4a is specific to the GBW test, which we indicated by describing the effect as mild. Our focus here is not on the magnitude of survival differences, but on the consistent trends observed in both Polr3e and Sxl knockdowns.

Writing and language:*

• Introduction finishes without providing an outline of the findings (which is fine by me if that is what the authors wanted).

• In lines 361-5, the authors say "We speculate that this interaction not only facilitates Pol III transcription but may also influence chromatin architecture and RNA Pol II-driven transcription as observed with Pol III regulation in other organisms". "This interaction" refers to Polr3E-Sxl-DNA interaction and with "Pol III transcription" I presume the authors refer to transcription executed by Pol III. I am not clear about the meaning of the end of the sentence "as observed with Pol III regulation in other organisms". What is the observation, exactly? That Pol III modifies chromatin in Pol II regulated loci, or that Pol III interactors change chromatin architecture?

• DPE abbreviation is not introduced (and only used once).

• A few typos: Line 41 ...splicing of the Sxl[late] transcripts, which is [ARE?] constitutively transcribed (Keyes et al.,... Line 76 ...sexes but appears restricted to the nervous system [OF] male pupae and adults (Cline et Line 289 ...and S41). To assess any effect [ON]translational output, O-propargyl-puromycin (OPP)o Line 323 ...illustrating that the majority (72%) changes in tRNA levels [ARE] due to upregulation...hi Line 402 ...it was discovered [WE DISCOVERED] Line 792 ...Sxl across chromosomes X, 2 L/R, 3 L/R and 4. The y-axis represents the log[SYMBOL] ratio... This happens in other figure legends as well.*

Author response:

Thank you for the detailed feedback, we have clarified and incorporated the suggested changes.

**Referee Cross-commenting***

Reviewer 1 asks how physiological is the Sxl chromatin-association assay. I think the loss of association in Polr3E knock-down and the lack of association of other splicing factors goes a long way into answering this question. It is true that having positive binding data specifically for Sxl-RAC and negative binding data for a deletion mutant of the RMM domain would provide more robust conclusions (see below), but I am not sure it is completely necessary -- though this will depend on which journal the authors want to send the paper to.

I think that the comment of reviewer 1 about the levels of expression of Sxl-DAM does not apply here because of the way TaDa works - it relies on codon slippage to produce minimal amounts of the DAM fusion protein, so by construction it will be expressed at much lower levels than the endogenous protein.

Reviewer 1 also asks whether Polr3E chromatin-association is also dependent on Sxl, to round up the model and also as a way to address whether Sxl association to chromatin is real. While I agree with this on the former aim (this would be a nice-to-have), I think I disagree on the latter; there is no need for Polr3E recruitment to depend on Sxl for Sxl association to chromatin to be physiologically relevant. Polr3E is a peripheral component of Pol III and unlikely to depend on a factor of restricted expression like Sxl to interact with chromatin. The recruitment of Sxl could well be entirely 'hierarchical' and subject to Polr3E.

Revewer 2 is concerned with the fact that every mutant form of Sxl shows the same result from the DamID labelling. I have to agree with this to a point. A deletion mutant of RMM domains would address this. Microscopy evidence in salivary glands would be nice, certainly, but the system may not lend itself to this particular interaction, which might be short-lived and/or weak. I do not immediately see the relevance of the chromatin binding capacity of non-Drosophilidae Sxl -- though it might indicate that the impact of the discovery is less likely to go beyond this group.

Reviewer 2 does not find surprising that some tRNA genes (less than half) are regulated by Sxl. I think the value of that observation is just qualitative, as tRNAs are Pol III-produced transcripts, but their point is correct. A hypergeometric test could settle this.

Reviewer 2 is concerned that the evidence of direct interaction between Sxl and Polr3E is a single 1999 two-hybrid study. But that paper contains also GST pull-downs that narrow down the specific domains that mediate binding, and perform the binding in competitive salt conditions. I think it is enough. The author team, I think, are not biochemists, so finding the right collaborators and performing these experiments would take time that I am not sure is warranted.

Reviewer 2 is also concerned that the longevity assays may not be meaningful due to the difference in genetic backgrounds. This is a very reasonable concern (which I would extend to the climbing assays - any quantitative phenotype is sensitive to genetic background). However, I think the authors here may have already designed the experiment with this in mind - the controls express untargeted RNAi constructs, but I lose track of which one is control of which. This should be clarified in Methods.

Other comments are in line, I think, with what I have pointed out and I generally agree with everything else that has been said.

Reviewer #3 (Significance (Required)):

Drosophila Sxl is widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species. It is a favourite example of how splicing factors and alternative can have profound influence in biology and used cleverly in the molecular circuitry of the cell to enact elegant regulatory decisions.

In this work, Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Sxl is also a chromatin factor with an sex-independent, neuron-specific role in stimulating transcription by Pol III and Pol II, of genes involved with metabolism and protein homeostasis, including some encoding tRNAs.

This opens a large number of interesting biological questions that range from biochemistry, gene regulation or neurobiology to evolution. How is the simultaneous capacity of binding RNA and chromatin (with the same protein domain, RRM) regulated/coordinated? How did this dual activity evolve and which one is the ancestral one? How many other RRM-containin RNA-binding proteins can also bind chromatin? How is Sxl recruited to chromatin to both Pol II and Pol III targets and are they functionally related? If so, how is the coordination of cellular functions activated through different RNA polymerases taking place and what is the role of Sxl in this? What are the functional consequences to neuronal biology? Does this affect similarly all Sxl-expressing neurons?

The evidence for the central tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments.*

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

*The convincing analysis demonstrates a role for the Drosophila Sex determining gene sex lethal in controlling aspects of transcription in the nervous system independent of its role in splicing. Interaction with an RNA Pol III subunit mediating Sxl association with chromatin and similar knockdown phenotypes strongly support the role of Sxl in the regulation of neuronal metabolism. Given that Sxl is an evolutionary recent acquisition for sex determination, the study may reveal an ancestral role for Sxl.

The conclusions are well justified by the datasets presented and I have no issues with the study or the interpretation. Throughout the work is well referenced, though perhaps the authors might take a look at Zhang et al (2014) (PMID: 24271947) for an interesting evolutionary perspective for the discussion.*

Author Response:

Thank you for the thoughtful suggestion. We will be sure to incorporate the findings from Zhang et al. regarding the evolution of the sex determination pathway.

*I have some minor comments for clarification:

There is no Figure 2b, should be labelled 2 or label TaDa plots as 2b

Clarify if Fig 2 data are larval or adult *

*Larval

Fig 3d - are these replicates or female and male?

Please elaborate on tub-GAL80[ts] developmental defects

Fig 4e, are transcriptomics done with the VDRC RNAi line? The VDRC and BDSC RNAi lines exhibit different behaviours - former has "better" survival and Better negative geotaxis, the latter seems to have poorer survival but little geotaxis effect?*

*Fig S3 - volcano plot for Polr3E?

Fig S4a - legend says downregulated genes?

The discussion should at least touch on the fact that Sxl amorphs (i.e. Sxl[fP7B0] are male viable and fertile, emphasising that the newly uncovered role is not essential.*

Author Response:

We agree with the suggestions outlined in the comments and have made the appropriate revisions.

Reviewer #4 (Significance (Required)):*

A nonessential role for Sxl in the nervous system independent of sex-determination contributes to better understanding a) the evolution of sex determining mechanisms, b) the role of RNA PolIII in neuronal homeostasis and c) more widely to the neuronal aging field. I think this well-focused study reveals a hitherto unsuspected role for Sxl.*

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #3

Evidence, reproducibility and clarity

Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Drosophila Sxl, widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species, is also a chromatin factor that can stimulate transcription by Pol III and Pol II of genes involved with metabolism and protein homeostasis, specifically some encoding tRNAs.

The evidence for the tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments. I have a few specific comments below, all minor.

Scientific points:

• The approach taken for the evaluation of Sxl DNA-binding activity in Fig2 is not entirely clear. I assume these are crosses of elav-Gal4 x different UAS- lines, then using males or females for UAS-Sxl-Full-Length. But what about the others? Were the experiments done in males only? This is hinted at in the main text but not explicitly indicated in the figure or the methods (at least, that I could easily find). And is this approach extended to all other experiments? Longevity? Climbing assays? Considering the role of Sxl, it may be helpful to be fastidiously systematic with this.
• In the discussion, lines 360-61, the authors say: Indeed, knockdown of Polr3E leads to a loss of Sxl binding to chromatin, suggesting a cooperative mechanism. Maybe I am misunderstanding the authors, but when I read "cooperation" in this context I think of biochemical cooperative binding. This is possible, but I do not think a simple 'requirement' test can suggest specifically that this mechanistic feature of biochemical binding is at play. I would expect, for starters, a reciprocal requirement for binding (which is not tested), and some quantitative features that would be difficult to evaluate in vivo. I do not think cooperative binding needs to be invoked anyway, as the authors do not make any specific point or prediction about it. But if they do think this is going on, I think it would need to be referred to as a speculation.
• In lines 428-432, the authors discuss the ancestral role of Sxl and make a comparison with ELAV, in the context of an RNA-binding protein that has molecular functions beyond those of a splicing factor, considering the functions of ELAV in RNA stability and translation, and finishing with "suggesting that similar regulatory mechanisms may be at play". I do not understand this latter sentence. Which mechanisms are these? Are the authors referring to the molecular activities of ELAV and SXL? But what would be the similarity? SXL seems to have a dual capacity to bind RNA and protein interactors, which allows it to work both in chromatin-level regulation as well as post-transcriptionally in splicing; but ELAV seems rather to take advantage of its RNA binding function to make it work in multiple RNA-related contexts, all post-transcriptional. I do not see an obvious parallel beyond the fact that RNA binding proteins can function at different levels of gene expression regulation -- but I would not say this parallel are "similar regulatory mechanisms", so I find the whole comparison a bit confusing.
• One aspect of the work that I find is missing in the discussion is the possibility that the simultaneous capacity of Sxl for RNA binding and Polr3E binding: are these mutually exclusive? if so, are they competitive or hierarchical? how would they be coordinated anyway?
• The only aspect of the paper where I found that one could make an experimental improvement is the claim that Sxl induces the expression of genes that have the overall effect of stimulating protein synthesis. The OPP experiment shows a correlation between the expression of Sxl and the rate of protein synthesis initiation. However, a more powerful experiment would be, rather obviously, to introduce Sxl knock-down in the same experiment, and observe whether in Sxl-expressing neurons the incorporation of OPP is reduced. I put this forth as a minor point because the tenet of the paper would not be affected by the results (though the perception of importance of the newly described function could be reinforced).
• In a similar way, it would be interesting to know whether the recruitment of Polr3E and Sxl to chromatin is co-dependent or Sxl follows Polr3E. This is also a minor point because this would possibly refine the mechanism of recruitment but does not alter the main discovery.

Figures and reporting:

• In Figure 2, it would be helpful to see the truncation coordinate for the N and C truncations.
• In Figure 3D, genomic coordinates are missing.
• In Figure 3E, the magnitude in the Y axis is not entirely clear (at least not to me). How is the amount of binding across the genome quantified? Is this the average amplitude of normalised TaDa signal across the genome? Or only within binding intervals?
• Figure S3E-F: it would be interesting to show the degree of overlap between the downregulated genes that are also binding targets (regardless of the outcome).
• Figure 5C-E: similarly to Figure S3, it would be interesting to know how the transcriptional effects compare with the binding targets.
• Authors use Gehan-Breslow-Wilcoxon to test survival, which is a bit unusual, as it gives more weight to the early deaths (which are rare in most Drosophila longevity experiments). Is there any rationale behind this? It may be even favour their null hypothesis.

Writing and language:

• Introduction finishes without providing an outline of the findings (which is fine by me if that is what the authors wanted).
• In lines 361-5, the authors say "We speculate that this interaction not only facilitates Pol III transcription but may also influence chromatin architecture and RNA Pol II-driven transcription as observed with Pol III regulation in other organisms". "This interaction" refers to Polr3E-Sxl-DNA interaction and with "Pol III transcription" I presume the authors refer to transcription executed by Pol III. I am not clear about the meaning of the end of the sentence "as observed with Pol III regulation in other organisms". What is the observation, exactly? That Pol III modifies chromatin in Pol II regulated loci, or that Pol III interactors change chromatin architecture?
• DPE abbreviation is not introduced (and only used once).
• A few typos: Line 41 ...splicing of the Sxl[late] transcripts, which is [ARE?] constitutively transcribed (Keyes et al.,... Line 76 ...sexes but appears restricted to the nervous system [OF] male pupae and adults (Cline et Line 289 ...and S41). To assess any effect [ON]translational output, O-propargyl-puromycin (OPP)o Line 323 ...illustrating that the majority (72%) changes in tRNA levels [ARE] due to upregulation...hi Line 402 ...it was discovered [WE DISCOVERED] Line 792 ...Sxl across chromosomes X, 2 L/R, 3 L/R and 4. The y-axis represents the log[SYMBOL] ratio... This happens in other figure legends as well.

Referee Cross-commenting

Reviewer 1 asks how physiological is the Sxl chromatin-association assay. I think the loss of association in Polr3E knock-down and the lack of association of other splicing factors goes a long way into answering this question. It is true that having positive binding data specifically for Sxl-RAC and negative binding data for a deletion mutant of the RMM domain would provide more robust conclusions (see below), but I am not sure it is completely necessary -- though this will depend on which journal the authors want to send the paper to.

I think that the comment of reviewer 1 about the levels of expression of Sxl-DAM does not apply here because of the way TaDa works - it relies on codon slippage to produce minimal amounts of the DAM fusion protein, so by construction it will be expressed at much lower levels than the endogenous protein.

Reviewer 1 also asks whether Polr3E chromatin-association is also dependent on Sxl, to round up the model and also as a way to address whether Sxl association to chromatin is real. While I agree with this on the former aim (this would be a nice-to-have), I think I disagree on the latter; there is no need for Polr3E recruitment to depend on Sxl for Sxl association to chromatin to be physiologically relevant. Polr3E is a peripheral component of Pol III and unlikely to depend on a factor of restricted expression like Sxl to interact with chromatin. The recruitment of Sxl could well be entirely 'hierarchical' and subject to Polr3E.

Revewer 2 is concerned with the fact that every mutant form of Sxl shows the same result from the DamID labelling. I have to agree with this to a point. A deletion mutant of RMM domains would address this. Microscopy evidence in salivary glands would be nice, certainly, but the system may not lend itself to this particular interaction, which might be short-lived and/or weak. I do not immediately see the relevance of the chromatin binding capacity of non-Drosophilidae Sxl -- though it might indicate that the impact of the discovery is less likely to go beyond this group.

Reviewer 2 does not find surprising that some tRNA genes (less than half) are regulated by Sxl. I think the value of that observation is just qualitative, as tRNAs are Pol III-produced transcripts, but their point is correct. A hypergeometric test could settle this.

Reviewer 2 is concerned that the evidence of direct interaction between Sxl and Polr3E is a single 1999 two-hybrid study. But that paper contains also GST pull-downs that narrow down the specific domains that mediate binding, and perform the binding in competitive salt conditions. I think it is enough. The author team, I think, are not biochemists, so finding the right collaborators and performing these experiments would take time that I am not sure is warranted.

Reviewer 2 is also concerned that the longevity assays may not be meaningful due to the difference in genetic backgrounds. This is a very reasonable concern (which I would extend to the climbing assays - any quantitative phenotype is sensitive to genetic background). However I think the authors here may have already designed the experiment with this in mind - the controls expres untargeted RNAi constructs, but I lose track of which one is control of which. This should be clarified in Methods.

Other comments are in line, I think, with what I have pointed out and I generally agree with everything else that has been said.

Significance

Drosophila Sxl is widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species. It is a favourite example of how splicing factors and alternative can have profound influence in biology and used cleverly in the molecular circuitry of the cell to enact elegant regulatory decisions.

In this work, Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Sxl is also a chromatin factor with an sex-independent, neuron-specific role in stimulating transcription by Pol III and Pol II, of genes involved with metabolism and protein homeostasis, including some encoding tRNAs.

This opens a large number of interesting biological questions that range from biochemistry, gene regulation or neurobiology to evolution. How is the simultaneous capacity of binding RNA and chromatin (with the same protein domain, RRM) regulated/coordinated? How did this dual activity evolve and which one is the ancestral one? How many other RRM-containin RNA-binding proteins can also bind chromatin? How is Sxl recruited to chromatin to both Pol II and Pol III targets and are they functionally related? If so, how is the coordination of cellular functions activated through different RNA polymerases taking place and what is the role of Sxl in this? What are the functional consequences to neuronal biology? Does this affect similarly all Sxl-expressing neurons?

The evidence for the central tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments.

I am sincerely grateful to the editors and peer reviewers at MetaROR for their detailed feedback and valuable comments and suggestions. I have addressed each point below.

Handling Editor

1. However, the article’s progression and arguments, along with what it seeks to contribute to the literature need refinement and clarification. The argument for PRC is under-developed due to a lack of clarity about what the article means by scientific

communication. Clarity here might make the endorsement of PRC seem like less of a foregone conclusion.

The structure of the paper (and discussion) has changed significantly to address the feedback.

2. I strongly endorse the main theme of most of the reviews, which is that the progression and underlying justifications for this article’s arguments needs a great deal of work. In my view, this article’s main contribution seems to be the evaluation of the three peer review models against the functions of scientific communication. I say ‘seems to be’ because the article is not very clear on that and I hope you will consider clarifying what your manuscript seeks to add to the existing work in this field. In any case, if that assessment of the three models is your main contribution, that part is somewhat underdeveloped. Moreover, I never got the sense that there is clear agreement in the literature about what the tenets of scientific communication are. Note that scientific communication is a field in its own right.

I have implemented a more rigorous approach to argumentation in response. “Scientific communication” was replaced by “scholarly communication.”

3. I also agree that paper is too strongly worded at times, with limitations and assumptions in the analysis minimised or not stated. For example, all of the typologies and categories drawn could easily be reorganised and there is a high degree of subjectivity in this entire exercise. Subjective choices should be highlighted and made salient for the reader. Note that greater clarity, rigour, and humility may also help with any alleged or actual bias.

I have incorporated the conceptual framework and description of the research methodology. However, the

Discussion section reflects my personal perspective in some points, which I have explicitly highlighted to ensure clarity.

4. I agree with Reviewer 3 that the ‘we’ perspective is distracting.

This has been fixed.

5. The paragraph starting with ‘Nevertheless’ on page 2 is very long.

The text was restructured.

6. There are many points where language could be shortened for readability, for example:

Page 3: ‘decision on publication’ could be ‘publication decision’.

Page 5: ‘efficiency of its utilization’ could be ‘its efficiency’.

Page 7: ‘It should be noted…’ could be ‘Note that…’.

I have proofread the text.

7. Page 7: ‘It should be noted that..’ – this needs a reference.

This statement has been moved to the Discussion section, paraphrased, and reference added.

“It should be also noted that peer review innovations pull in opposing directions, with some aiming to increase efficiency and reduce costs, while others aim to promote rigor and increase costs

(Kaltenbrunner et al., 2022).”

8. I’m not sure that registered reports reflect a hypothetico-deductive approach (page 6). For instance, systematic reviews (even non-quantitative ones) are often published as registered reports and Cochrane has required this even before the move towards registered reports in quantitative psychology.

I have added this clarification.

9. I agree that modular publishing sits uneasily as its own chapter.

Modular publishing has been combined with registered reports into the deconstructed publication group of

models, now Section 5.1.

10. Page 14: ‘The "Publish-Review-Curate" model is universal that we expect to be the future of scientific publishing. The transition will not happen today or tomorrow, but in the next 5-10 years, the number of projects such as eLife, F1000Research, Peer Community in, or MetaROR will rapidly increase’. This seems overly strong (an example of my larger critique and that of the reviewers).

This part of the text has been rewritten.

Reviewer 1

11. For example, although Model 3 is less chance to insert bias to the readers, it also weakens the filtering function of the review system. Let’s just think about the dangers of machine-generated articles, paper-mills, p-hacked research reports and so on. Although the editors do some pre-screening for the submissions, in a world with only Model 3 peer review the literature could easily get loaded with even more ‘garbage’ than in a model where additional peers help the screening.

I think that generated text is better detected by software tools. At the same time, I tried and described the pros and cons of different models in a more balanced way in the concluding section.

12. Compared to registered reports other aspects can come to focus that Model 3 cannot cover. It’s the efficiency of researchers’ work. In the care of registered reports, Stage 1 review can still help researchers to modify or improve their research design or data collection method. Empirical work can be costly and time-consuming and post-publication review can only say that “you should have done it differently then it

would make sense”.

Thank you very much for this valuable contribution, I have added this statement at P. 11.

13. Finally, the author puts openness as a strength of Model 3. In my eyes, openness is a separate question. All models can work very openly and transparently in the right circumstances. This dimension is not an inherent part of the models.

I think that the model, providing peer reviews to all the submissions, ensures maximum transparency. However, I have made effort to make the wording more balanced and distinguish my personal perspective from the literature.

14. In conclusion, I would not make verdict over the models, instead emphasize the different functions they can play in scientific communication.

This idea has been reflected now in the concluding section.

15. A minor comment: I found that a number of statements lack references in the Introduction. I would have found them useful for statements such as “There is a point of view that peer review is included in the implicit contract of the researcher.”

Thank you for your feedback. I have implemented a more rigorous approach to argumentation in response.

Reviewer 2

16. The primary weakness of this article is that it presents itself as an 'analysis' from which they 'conclude' certain results such as their typology, when this appears clearly to be an opinion piece. In my view, this results in a false claim of objectivity which detracts from what would otherwise be an interesting and informative, albeit subjective, discussion, and thus fails to discuss the limitations of this approach.

I have incorporated the conceptual framework and description of the research methodology. However, the

Discussion section reflects my personal perspective in some points, which I have explicitly highlighted to ensure clarity.

17. A secondary weakness is that the discussion is not well structured and there are some imprecisions of expression that have the potential to confuse, at least at first.

The structure of the paper (and discussion) has changed significantly.

18. The evidence and reasoning for claims made is patchy or absent. One instance of the former is the discussion of bias in peer review. There are a multitude of studies of such bias and indeed quite a few meta-analyses of these studies. A systematic search could have been done here but there is no attempt to discuss the totality of this literature. Instead, only a few specific studies are cited. Why are these ones chosen? We have no idea. To this extent I am not convinced that the references used here are the most appropriate.

I have reviewed the existing references and incorporated additional sources. However, the study does not claim to conduct a systematic literature review; rather, it adopts an interpretative approach to literature analysis.

19. Instances of the latter are the claim that "The most well-known initiatives at the moment are ResearchEquals and Octopus" for which no evidence is provided, the claim that "we believe that journal-independent peer review is a special case of Model 3" for which no further argument is provided, and the claim that "the function of being the "supreme judge" in deciding what is "good" and "bad" science is taken on by peer review" for which neither is provided.

Thank you for your feedback. I have implemented a more rigorous approach to argumentation in response.

20. A particular example of this weakness, which is perhaps of marginal importance to the overall paper but of strong interest to this reviewer is the rather odd engagement with history within the paper. It is titled "Evolution of Peer Review" but is really focussed on the contemporary state-of-play. Section 2 starts with a short history of peer review in scientific publishing, but that seems intended only to establish what is

described as the 'traditional' model of peer review. Given that that short history had just shown how peer review had been continually changing in character over centuries - and indeed Kochetkov goes on to describe further changes - it is a little difficult to work out what 'traditional' might mean here; what was 'traditional' in 2010 was not the same as what was 'traditional' in 1970. It is not clear how seriously this history is being taken. Kochetkov has earlier written that "as early as the beginning of the 21st century, it was argued that the system of peer review is 'broken'" but of course criticisms - including fundamental criticisms - of peer review are much older than this. Overall, this use of history seems designed to privilege the

experience of a particular moment in time, that coincides with the start of the metascience reform movement.

While the paper addresses some aspects of peer review history, it does not provide a comprehensive examination of this topic. A clarifying statement to this effect has been included in the methodology section.

“… this section incorporates elements of historical analysis, it does not fully qualify as such because primary sources were not directly utilized. Instead, it functions as an interpretative literature review, and one that is intentionally concise, as a comprehensive history of peer review falls outside the scope of this research”.

21. Section 2 also demonstrates some of the second weakness described, a rather loose structure. Having moved from a discussion of the history of peer review to detail the first model, 'traditional' peer review, it then also goes on to describe the problems of this model. This part of the paper is one of the best - and best - evidenced. Given the importance of it to the main thrust of the discussion it should probably have been given more space as a Section all on its own.

This section (now Section 4) has been extended, see also previous comment.

22. Another example is Section 4 on Modular Publishing, in which Kochetkov notes "Strictly speaking, modular publishing is primarily an innovative approach for the publishing workflow in general rather than specifically for peer review."

Kochetkov says "This is why we have placed this innovation in a separate category" but if it is not an innovation in peer review, the bigger question is 'Why was it included in this article at all?'.

Modular publishing has been combined with registered reports into the deconstructed publication group of models, now Section 5.1.

23. One example of the imprecisions of language is as follows. The author also shifts between the terms 'scientific communication' and 'science communication' but, at least in many contexts familiar to this reviewer, these are not the same things, the former denoting science-internal dissemination of results through publication (which the author considers), conferences and the like (which the author specifically excludes) while the latter denotes the science-external public dissemination of scientific findings to non-technical audiences, which is entirely out of scope for this article.

Thank you for your remark. As a non- native speaker, I initially did not grasp the distinction between the terms. However, I believe the phrase ‘scholarly communication’ is the most universally applicable term. This adjustment has now been incorporated into the text.

24. A final note is that Section 3, while an interesting discussion, seems largely derivative from a typology of Waltman, with the addition of a consideration of whether a reform is 'radical' or 'incremental', based on how 'disruptive' the reform is. Given that this is inherently a subjective decision, I wonder if it might not have been more informative to consider 'disruptiveness' on a scale and plot it accordingly. This would allow for some range to be imagined for each reform as well; surely reforms might be more or less disruptive depending on how they are implemented. Given that each reform is considered against each model, it is somewhat surprising that this is not presented in a tabular or graphical form.

Ultimately, I excluded this metric due to its current reliance on purely subjective judgment. Measuring 'disruptiveness', e.g., through surveys or interviews remains a task for future research. 

25. Reconceptualize this as an opinion piece. Where systematic evidence can be drawn upon to make points, use that, but don't be afraid to just present a discussion from what is clearly a well-informed author.

I cannot definitively classify this work as an opinion piece. In fact, this manuscript synthesizes elements of a literature review, research article, and opinion essay. My idea was to integrate the strengths of all three genres.

26. Reconsider the focus on history and 'evolution' if the point is about the current state of play and evaluation of reforms (much as I would always want to see more studies on the history and evolution of peer review).

I have revised the title to better reflect the study’s scope and explicitly emphasize its focus on contemporary developments in the field.

“Peer Review at the Crossroads”

27. Consider ways in which the typology might be expanded, even if at subordinate level.

I have updated the typology and introduced the third tier, where it is applicable (see Fig.2).

Reviewer 3

28. In my view, the biggest issue with the current peer review system is the low quality of reviews, but the manuscript only mentions this fleetingly. The current system facilitates publication bias, confirmation bias, and is generally very inconsistent. I think this is partly due to reviewers’ lack of accountability in such a closed peer review system, but I would be curious to hear the author’s ideas about this, more elaborately than they provide them as part of issue 2.

I have elaborated on this issue in the footnote.

29. I’m missing a section in the introduction on what the goals of peer review are or should be. You mention issues with peer review, and these are mostly fair, but their importance is only made salient if you link them to the goals of peer review. The author does mention some functions of peer review later in the paper, but I think it would be good to expand that discussion and move it to a place earlier in the manuscript.

The functions of peer review are summarized in the first paragraph of Introduction.

30. Table 1 is intuitive but some background on how the author arrived at these categorizations would be welcome.

When is something incremental and when is something radical? Why are some innovations included but not others (e.g., collaborative peer review, see https://content.prereview.org/how-collaborative-peer-review-can-

transform-scientific-research/)?

Collaborative peer review, namely, Prereview was mentioned in the context of Model 3 (Publish-Review-Curate). However, I have extended this part of the paper.

31. “Training of reviewers through seminars and online courses is part of the strategies of many publishers. At the same time, we have not been able to find statistical data or research to assess the effectiveness of such training.” (p. 5)  There is some literature on this, although not recent. See work by Sara Schroter for example, Schroter et al., 2004; Schroter et al., 2008)

Thank you very much, I have added these studies and a few more recent ones.

32. “It should be noted that most initiatives aimed at improving the quality of peer review simultaneously increase the costs.” (p. 7) This claim needs some support. Please explicate why this typically is the case and how it should impact our evaluations of these initiatives.

I have moved this part to the Discussion section.

33. I would rephrase “Idea of the study” in Figure 2 since the other models start with a tangible output (the manuscript). This is the same for registered reports where they submit a tangible report including hypotheses, study design, and analysis plan. In the same vein, I think study design in the rest of the figure might also not be the best phrasing. Maybe the author could use the terminology used by COS (Stage 1 manuscript, and Stage 2 manuscript, see Details & Workflow tab of https://www.cos.io/initiatives/registered-reports). Relatedly, “Author submits the first version of the manuscript” in the first box after the ‘Manuscript (report)’ node maybe a confusing phrase because I think many researchers see the first version of the manuscript as the stage 1 report sent out for stage 1 review.

Thank you very much. Stage 1 and Stage 2 manuscripts look like suitable labelling solution.

34. One pathway that is not included in Figure 2 is that authors can decide to not conduct the study when improvements are required. Relatedly, in the publish- review-curate model, is revising the manuscripts based on the reviews not optional as well? Especially in the case of 3a, authors can hardly be forced to make changes even though the reviews are posted on the platform.

All the four models imply a certain level of generalization; thus, I tried to avoid redundant details. However, I have added this choice to the PRC model (now, Model 4).

35. I think the author should discuss the importance of ‘open identities’ more. This factor is now not explicitly included in any of the models, while it has been found to be one of the main characteristics of peer review systems (Ross-Hellauer, 2017).

This part has been extended.

36. More generally, I was wondering why the author chose these three models and not others. What were the inclusion criteria for inclusion in the manuscript? Some information on the underlying process would be welcome, especially when claims like “However, we believe that journal-independent peer review is a special case of Model 3 (“Publish-Review-Curate”).” are made without substantiation.

The study included four generalized models of peer review that involved some level of abstraction.

37. Maybe it helps to outline the goals of the paper a bit more clearly in the introduction. This helps the reader to know what to expect.

The Introduction has been revised including the goal and objectives.

38. The Modular Publishing section is not inherently related to peer review models, as you mention in the first sentence of that paragraph. As such, I think it would be best to omit this section entirely to maintain the flow of the paper. Alternatively, you could shortly discuss it in the discussion section but a separate paragraph seems too much from my point of view.

Modular publishing has been combined with registered reports into the fragmented publishing group of models, now in Section 5.

39. Labeling model 3 as post-publication review might be confusing to some readers. I believe many researchers see post-publication review as researchers making comments on preprints, or submitting commentaries to journals. Those activities are substantially different from the publish-review-curate model so I think it is important to distinguish between these types.

The label was changed into Publish-Review-Curate model.

40. I do not think the conclusions drawn below Table 3 logically follow from the earlier text. For example, why are “all functions of scientific communication implemented most quickly and transparently in Model 3”? It could be that the entire process takes longer in Model 3 (e.g. because reviewers need more time), so that Model 1 and Model 2 lead to outputs quicker. The same holds for the following claim: “The additional costs arising from the independent assessment of information based on open reviews are more than compensated by the emerging opportunities for scientific pluralism.” What is the empirical evidence for this? While I personally do think that Model 3 improves on Model 1, emphatic statements like this require empirical evidence. Maybe the author could provide some suggestions on how we can attain this evidence. Model 2 does have some empirical evidence underpinning its validity (see Scheel, Schijen, Lakens, 2021; Soderberg et al., 2021; Sarafoglou et al. 2022) but more meta-research inquiries into the effectiveness and cost- benefits ratio of registered reports would still be welcome in general.

The Discussion section has been substantially revised to address this point. While I acknowledge the current scarcity of empirical studies on innovative peer review models, I have incorporated a critical discussion of this methodological gap. I am grateful for the suggested literature on RRs, which I have now integrated into the relevant subsection.

41. What is the underlaying source for the claim that openness requires three conditions?

I have made effort to clarify within the text that this reflects my personal stance.

42. “If we do not change our approach, science will either stagnate or transition into other forms of communication.” (p. 2) I don’t think this claim is supported sufficiently strongly. While I agree there are important problems in peer review, I think would need to be a more in-depth and evidence-based analysis before claims like this can be made.

The sentence has been rephrased.

43. On some occasions, the author uses “we” while the study is single authored.

This has been fixed.

44. Figure 1: The top-left arrow from revision to (re-)submission is hidden

I have updated Figure 1.

45. “The low level of peer review also contributes to the crisis of reproducibility in scientific research (Stoddart, 2016).” (p. 4) I assume the author means the low quality of peer review.

This has been fixed.

46. “Although this crisis is due to a multitude of factors, the peer review system bears a significant responsibility for it.” (p. 4)

This is also a big claim that is not substantiated

I have paraphrased this sentence as

“While multiple factors drive this crisis, deficiencies in the peer review process

remain a significant contributor.” and added a footnote.

47. “Software for automatic evaluation of scientific papers based on artificial intelligence (AI) has emerged relatively recently” (p. 5) The author could add RegCheck (https://regcheck.app/) here, even though it is still in development. This tool is especially salient in light of the finding that preregistration-paper checks are rarely done as part of reviews (see Syed, 2023)

Thank you very much, I have added this information.

48. There is a typo in last box of Figure 1 (“decicion” instead of “decision”). I also found typos in the second box of Figure 2, where “screns” should be “screens”, and the author decision box where “desicion” should be “decision”

This has been fixed.

49. Maybe it would be good to mention results blinded review in the first paragraph of 3.2. This is a form of peer review where the study is already carried out but reviewers are blinded to the results. See work by Locascio (2017), Grand et al. (2018), and Woznyj et al. (2018).

Thanks, I have added this (now section 5.2)

50. Is “Not considered for peer review” in figure 3b not the same as rejected? I feel that it is rejected in the sense that neither the manuscript not the reviews will be posted on the platform.

Changed into “Rejected”

51. “In addition to the projects mentioned, there are other platforms, for example, PREreview12, which departs even more radically from the traditional review format due to the decentralized structure of work.” (p. 11) For completeness, I think it would be helpful to add some more information here, for example why exactly decentralization is a radical departure from the traditional model.

I have extended this passage.

52. “However, anonymity is very conditional - there are still many “keys” left in the manuscript, by which one can determine, if not the identity of the author, then his country, research group, or affiliated organization.” (p.11) I would opt for the neutral “their” here instead of “his”, especially given that this is a paragraph about equity and inclusion.

This has been fixed.

53. “Thus, “closeness” is not a good way to address biases.” (p. 11) This might be a straw man argument because I don’t believe researchers have argued that it is a good method to combat biases. If they did, it would be good to cite them here. Alternatively, the sentence could be omitted entirely.

I have omitted the sentence.

54. I would start the Modular Publishing section with the definition as that allows readers to interpret the other statements better.

Modular publishing has been combined with registered reports into the deconstructed publication group of

models, now in Section 5, general definition added.

55. It would be helpful if the Models were labeled (instead of using Model 1, Model 2, and Model 3) so that readers don’t have to think back what each model involved.

All the models represent a kind of generalization, which is why non-detailed labels are used. The text labels may vary depending on the context.

56. Table 2: “Decision making” for the editor’s role is quite broad, I recommend to specify and include what kind of decisions need to be made.

Changed into “Making accept/reject decisions”

57. Table 2: “Aim of review” – I believe the aim of peer review differs also within these models (see the “schools of thought” the author mentions earlier), so maybe a statement on what the review entails would be a better way to phrase this.

Changed into “What does peer review entail?”

58. Table 2: One could argue that the object of the review’ in Registered Reports is

also the manuscript as a whole, just in different stages. As such, I would phrase this differently.

Current wording fits your remark

“Manuscript in terms of study design and execution”

Reviewer 4

59. Page 3: It’s hard to get a feel for the timeline given the dates that are described. We have peer review becoming standard after WWII (after 1945), definitively established by the second half of the century, an example of obligatory peer review starting in 1976, and in crisis by the end of the 20th century. I would consider adding

examples that better support this timeline – did it become more common in specific journals before 1976? Was the crisis by the end of the 20th century something that happened over time or something that was already intrinsic to the institution? It doesn’t seem like enough time to get established and then enter crisis, but more details/examples could help make the timeline clear. Consider discussing the benefits of the traditional model of peer review.

This section has been extended.

60. Table 1 – Most of these are self- explanatory to me as a reader, but not all. I don’t know what a registered report refers to, and it stands to reason that not all of these innovations are familiar to all readers. You do go through each of these sections, but that’s not clear when I initially look at the table. Consider having a more informative caption. Additionally, the left column is “Course of changes” here but “Directions” in text. I’d pick one and go with it for consistency.

Table 1 has been replaced by Figure 2. I have also extended text descriptions, added definitions.

61. With some of these methods, there’s the ability to also submit to a regular journal. Going to a regular journal presumably would instigate a whole new round of review, which may or may not contradict the previous round of post-publication review and would increase the length of time to publication by going through both types. If someone has a goal to publish in a journal, what benefit would they get by going through the post-publication review first, given this extra time?

Some of these platforms, e.g., F1000, Lifecycle Journal, replace conventional journal publishing. Modular publishing allows for step-by-step feedback from peers.

An important advantage of RRs over other peer review models lies in their capacity to enhance research efficiency. By conducting peer review at Stage 1, researchers gain the opportunity to refine their study design or data collection protocols before empirical work begins.

Other models of review can offer critiques such as "the study should have been conducted differently" without

actionable opportunity for improvement. The key motivation for having my paper reviewed in MetaROR is the quality of peer review – I have never received so many comments, frankly! Moreover, platforms such as MetaROR usually have partnering journals.

62. There’s a section talking about institutional change (page 14). It mentions that openness requires three conditions – people taking responsibility for scientific communication, authors and reviewers, and infrastructure. I would consider adding some discussion of readers and evaluators. Readers have to be willing to accept these papers as reliable, trustworthy, and respectable to read and use the information in them.

Evaluators such as tenure committees and potential employers would need to consider papers submitted through these approaches as evidence of scientific scholarship for the effort to be worthwhile for scientists.

I have omitted these conditions and employed the Moore’s Technology Adoption Life Cycle. Thank you very much for your comment!

63. Based on this overview, which seems somewhat skewed towards the merits of these methods (conflict of interest, limited perspective on downsides to new methods/upsides to old methods), I am not quite ready to accept this effort as equivalent of a regular journal and pre-publication peer review process. I look forward to learning more about the approach and seeing this review method in action and as it develops.

The Discussion section has been substantially revised to address this point. While I acknowledge the current scarcity of empirical studies on innovative peer review models, I have incorporated a critical discussion of this methodological gap.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper concerns mechanisms of foraging behavior in C. elegans. Upon removal from food, C. elegans first executes a stereotypical local search behavior in which it explores a small area by executing many random, undirected reversals and turns called "reorientations." If the worm fails to find food, it transitions to a global search in which it explores larger areas by suppressing reorientations and executing long forward runs (Hills et al., 2004). At the population level, the reorientation rate declines gradually. Nevertheless, about 50% of individual worms appear to exhibit an abrupt transition between local and global search, which is evident as a discrete transition from high to low reorientation rate (Lopez-Cruz et al., 2019). This observation has given rise to the hypothesis that local and global search correspond to separate internal states with the possibility of sudden transitions between them (Calhoun et al., 2014). The main conclusion of the paper is that it is not necessary to posit distinct internal states to account for discrete transitions from high to low reorientation rates. On the contrary, discrete transitions can occur simply because of the stochastic nature of the reorientation behavior itself.

Strengths:

The strength of the paper is the demonstration that a more parsimonious model explains abrupt transitions in the reorientation rate.

Weaknesses:

(1) Use of the Gillespie algorithm is not well justified. A conventional model with a fixed dt and an exponentially decaying reorientation rate would be adequate and far easier to explain. It would also be sufficiently accurate - given the appropriate choice of dt - to support the main claims of the paper, which are merely qualitative. In some respects, the whole point of the paper - that discrete transitions are an epiphenomenon of stochastic behavior - can be made with the authors' version of the model having a constant reorientation rate (Figure 2f).

We apologize, but we are not sure what the reviewer means by “fixed dt”. If the reviewer means taking discrete steps in time (dt), and modeling whether a reorientation occurs, we would argue that the Gillespie algorithm is a better way to do this because it provides floating-point precision, rather than a time resolution limited by dt, which we hopefully explain in the updated text (Lines 107-192).

The reviewer is correct that discrete transitions are an epiphenomenon of stochastic behavior as we show in Figure 2f. However, abrupt stochastic jumps that occur with a constant rate do not produce persistent changes in the observed rate because it is by definition, constant. The theory that there are local and global searches is based on the observation that individual worms often abruptly change their reorientation rates. But this observation is only true for a fraction of worms. We are trying to argue that the reason why this is not observed for all, or even most worms is because these are the result of stochastic sampling, not a sudden change in search strategy.

(2) In the manuscript, the Gillespie algorithm is very poorly explained, even for readers who already understand the algorithm; for those who do not it will be essentially impossible to comprehend. To take just a few examples: in Equation (1), omega is defined as reorientations instead of cumulative reorientations; it is unclear how (4) follows from (2) and (3); notation in (5), line 133, and (7) is idiosyncratic. Figure 1a does not help, partly because the notation is unexplained. For example, what do the arrows mean, what does "*" mean?

We apologize for this, you are correct, 𝛀 is cumulative reorientations, and we have edited the text for clarity (Lines 107-192):

We apologize for the arrow notation confusion. Arrow notation is commonly used in pseudocode to indicate variable assignment, and so we used it to indicate variable assignment updates in the algorithm.

We added Figure 2a to help explain the Gillespie algorithm for people who are unfamiliar with it, but you are correct, some notation, like probabilities, were left unexplained. We have added more text to the figure legend. Hopefully this additional text, along with lines 105-190, provide better clarification.

(3) In the model, the reorientation rate dΩ⁄dt declines to zero but the empirical rate clearly does not. This is a major flaw. It would have been easy to fix by adding a constant to the exponentially declining rate in (1). Perhaps fixing this obvious problem would mitigate the discrepancies between the data and the model in Figure 2d.

You are correct that the model deviates slightly at longer times, but this result is consistent with Klein et al. that show a continuous decline of reorientations. However, we have added a constant to the model (b, Equation 2), since an infinite run length is likely not physiological.

(4) Evidence that the model fits the data (Figure 2d) is unconvincing. I would like to have seen the proportion of runs in which the model generated one as opposed to multiple or no transitions in reorientation rate; in the real data, the proportion is 50% (Lopez). It is claimed that the "model demonstrated a continuum of switching to non-switching behavior" as seen in the experimental data but no evidence is provided.

We should clarify that the 50% proportion cited by López-Cruz was based on an arbitrary difference in slopes, and by assessing the data visually (López-Cruz, Figure S2). We added a comment in the text to clarify this (Lines 76 – 78). We sought to avoid this subjective assessment by plotting the distribution of slopes and transition times produced by the method used in López-Cruz. We should also clarify by what we meant by “a continuum of switching and non-switching” behavior. Both the transition time distributions and the slope-difference distributions do not appear to be the result of two distributions (the distributions in Figure 1 are not bimodal). This is unlike roaming and dwelling on food, where two distinct distributions of behavioral metrics can be identified based on speed and angular speed (Flavell et al, 2009, Fig S2a).

Based on the advice of Reviewer #3, we have also modeled the data using different starting amounts of M (M₀). By definition, an initial value of M₀ = 1 is a two-state switching strategy; the worm either uses a reorientation rate of a (when M = 1) or b (when M = 0). As expected, this does produce a bimodal distribution of slope differences (Figure 3b), which is significantly different than the experimental distribution (Figure 3c). We have added a new section to explain this in more detail (Lines 253 – 297).

(5) The explanation for the poor fit between the model and data (lines 166-174) is unclear. Why would externally triggered collisions cause a shift in the transition distribution?

Thank you, we rewrote the text to clarify this better (Lines 227-233). There were no externally triggered collisions; 10 animals were used per experiment. They would occasionally collide during the experiment, but these collisions were excluded from the data that were provided. However, worms are also known to increase reorientations when they encounter a pheromone trail, and it is unknown (from this dataset) which orientations may have been a result of this phenomenon.

(6) The discussion of Levy walks and the accompanying figure are off-topic and should be deleted.

Thank you, we agree that this topic is tangential, and we removed it.

Reviewer #2 (Public review):

Summary:

In this study, the authors build a statistical model that stochastically samples from a timeinterval distribution of reorientation rates. The form of the distribution is extracted from a large array of behavioral data, and is then used to describe not only the dynamics of individual worms (including the inter-individual variability in behavior), but also the aggregate population behavior. The authors note that the model does not require assumptions about behavioral state transitions, or evidence accumulation, as has been done previously, but rather that the stochastic nature of behavior is "simply the product of stochastic sampling from an exponential function".

Strengths:

This model provides a strong juxtaposition to other foraging models in the worm. Rather than evoking a behavioral transition function (that might arise from a change in internal state or the activity of a cell type in the network), or evidence accumulation (which again maps onto a cell type, or the activity of a network) - this model explains behavior via the stochastic sampling of a function of an exponential decay. The underlying model and the dynamics being simulated, as well as the process of stochastic sampling, are well described and the model fits the exponential function (Equation 1) to data on a large array of worms exhibiting diverse behaviors (1600+ worms from Lopez-Cruz et al). The work of this study is able to explain or describe the inter-individual diversity of worm behavior across a large population. The model is also able to capture two aspects of the reorientations, including the dynamics (to switch or not to switch) and the kinetics (slow vs fast reorientations). The authors also work to compare their model to a few others including the Levy walk (whose construction arises from a Markov process) to a simple exponential distribution, all of which have been used to study foraging and search behaviors.

Weaknesses:

This manuscript has two weaknesses that dampen the enthusiasm for the results. First, in all of the examples the authors cite where a Gillespie algorithm is used to sample from a distribution, be it the kinetics associated with chemical dynamics, or a Lotka-Volterra Competition Model, there are underlying processes that govern the evolution of the dynamics, and thus the sampling from distributions. In one of their references, for instance, the stochasticity arises from the birth and death rates, thereby influencing the genetic drift in the model. In these examples, the process governing the dynamics (and thus generating the distributions from which one samples) is distinct from the behavior being studied. In this manuscript, the distribution being sampled is the exponential decay function of the reorientation rate (lines 100-102). This appears to be tautological - a decay function fitted to the reorientation data is then sampled to generate the distributions of the reorientation data. That the model performs well and matches the data is commendable, but it is unclear how that could not be the case if the underlying function generating the distribution was fit to the data.

Thank you, we apologize that this was not clearer. In the Lotka-Volterra model, the density of predators and prey are being modeled, with the underlying assumption that rates of birth and death are inherently stochastic. In our model, the number of reorientations are being modeled, with the assumption (based on the experiments), that the occurrence of reorientations is stochastic, just like the occurrence (birth) of a prey animal is stochastic. However, the decay in M is phenomenological, and we speculate about the nature of M later in the manuscript.

You are absolutely right that the decay function for M was fit to the population average of reorientations and then sampled to generate the distributions of the reorientation data. This was intentional to show that the parameters chosen to match the population average would produce individual trajectories with comparable stochastic “switching” as the experimental data. All we’re trying to show really is that observed sudden changes in reorientation that appear persistent can be produced by a stochastic process without resorting to binary state assignments. In Calhoun, et al 2014 it is reported all animals produced switch-like behavior, but in Klein et al, 2017 it is reported that no animals showed abrupt transitions. López-Cruz et al seem to show a mix of these results, which can easily be explained by an underlying stochastic process.

The second weakness is somewhat related to the first, in that absent an underlying mechanism or framework, one is left wondering what insight the model provides.

Stochastic sampling a function generated by fitting the data to produce stochastic behavior is where one ends up in this framework, and the authors indeed point this out: "simple stochastic models should be sufficient to explain observably stochastic behaviors." (Line 233-234). But if that is the case, what do we learn about how the foraging is happening? The authors suggest that the decay parameter M can be considered a memory timescale; which offers some suggestion, but then go on to say that the "physical basis of M can come from multiple sources". Here is where one is left for want: The mechanisms suggested, including loss of sensory stimuli, alternations in motor integration, ionotropic glutamate signaling, dopamine, and neuropeptides are all suggested: these are basically all of the possible biological sources that can govern behavior, and one is left not knowing what insight the model provides. The array of biological processes listed is so variable in dynamics and meaning, that their explanation of what governs M is at best unsatisfying. Molecular dynamics models that generate distributions can point to certain properties of the model, such as the binding kinetics (on and off rates, etc.) as explanations for the mechanisms generating the distributions, and therefore point to how a change in the biology affects the stochasticity of the process. It is unclear how this model provides such a connection, especially taken in aggregate with the previous weakness.

Providing a roadmap of how to think about the processes generating M, the meaning of those processes in search, and potential frameworks that are more constrained and with more precise biological underpinning (beyond the array of possibilities described) would go a long way to assuaging the weaknesses.

Thank you, these are all excellent points. We should clarify that in López-Cruz et al, they claim that only 50% of the animals fit a local/global search paradigm. We are simply proposing there is no need for designating local and global searches if the data don’t really support it. The underlying behavior is stochastic, so the sudden switches sometimes observed can be explained by a stochastic process where the underlying rate is slowing down, thus producing the persistently slow reorientation rate when an apparent “switch” occurs. What we hope to convey is that foraging doesn’t appear to follow a decision paradigm, but instead a gradual change in reorientations which for individual worms, can occasionally produce reorientation trajectories that appear switch-like.

As for M, you are correct, we should be more explicit, and we have added text (Lines 319-359) to expand upon its possible biological origin.

Reviewer #3 (Public review):

Summary:

This intriguing paper addresses a special case of a fundamental statistical question: how to distinguish between stochastic point processes that derive from a single "state" (or single process) and more than one state/process. In the language of the paper, a "state" (perhaps more intuitively called a strategy/process) refers to a set of rules that determine the temporal statistics of the system. The rules give rise to probability distributions (here, the probability for turning events). The difficulty arises when the sampling time is finite, and hence, the empirical data is finite, and affected by the sampling of the underlying distribution(s). The specific problem being tackled is the foraging behavior of C. elegans nematodes, removed from food. Such foraging has been studied for decades, and described by a transition over time from 'local'/'area-restricted' search'(roughly in the initial 10-30 minutes of the experiments, in which animals execute frequent turns) to 'dispersion', or 'global search' (characterized by a low frequency of turns). The authors propose an alternative to this two-state description - a potentially more parsimonious single 'state' with time-changing parameters, which they claim can account for the full-time course of these observations.

Figure 1a shows the mean rate of turning events as a function of time (averaged across the population). Here, we see a rapid transient, followed by a gradual 4-5 fold decay in the rate, and then levels off. This picture seems consistent with the two-state description. However, the authors demonstrate that individual animals exhibit different "transition" statistics (Figure 1e) and wish to explain this. They do so by fitting this mean with a single function (Equations 1-3).

Strengths:

As a qualitative exercise, the paper might have some merit. It demonstrates that apparently discrete states can sometimes be artifacts of sampling from smoothly time-changing dynamics. However, as a generic point, this is not novel, and so without the grounding in C. elegans data, is less interesting.

Weaknesses:

(1) The authors claim that only about half the animals tested exhibit discontinuity in turning rates. Can they automatically separate the empirical and model population into these two subpopulations (with the same method), and compare the results?

Thank you, we should clarify that the observation that about half the animals exhibit discontinuity was not made by us, but by López-Cruz et al. The observed fraction of 50% was based on a visual assessment of the dual regression method we described. We added text (Lines 76-79) to clarify this. To make the process more objective, we decided to simply plot the distributions of the metrics they used for this assessment to see if two distinct populations could be observed. However, the distributions of slope differences and transition times do not produce two distinct populations. Our stochastic approach, which does not assume abrupt state-transitions, also produces comparable distributions. To quantify this, we have added a section varying M₀, including setting M₀ to 1, so that the model by definition is a switch model. This model performs the worst (Lines 253-296, Figure 3).

(2) The equations consider an exponentially decaying rate of turning events. If so, Figure 2b should be shown on a semi-logarithmic scale.

We chose to not do this because this average is based on the number of discrete reorientation events observed within a 2-minute window. The range of events ranges from 0 to 6 (hence a rate of 0.5-3 min^-1), which does not span one order of magnitude. Instead, we included a heat map (Figure 1a, Figure 2b bottom panel) which shows the density that the average is based on. We hope this provides some clarity to the reader.

(3) The variables in Equations 1-3 and the methods for simulating them are not well defined, making the method difficult to follow. Assuming my reading is correct, Omega should be defined as the cumulative number of turning events over time (Omega(t)), not as a "turn" or "reorientation", which has no derivative. The relevant entity in Figure 1a is apparently <Omega (t)>, i.e. the mean number of events across a population which can be modelled by an expectation value. The time derivative would then give the expected rate of turning events as a function of time.

Thank you, you are correct. Please see response to Reviewer #1.

(4) Equations 1-3 are cryptic. The authors need to spell out up front that they are using a pair of coupled stochastic processes, sampling a hidden state M (to model the dynamic turning rate) and the actual turn events, Omega(t), separately, as described in Figure 2a. In this case, the model no longer appears more parsimonious than the original 2-state model. What then is its benefit or explanatory power (especially since the process involving M is not observable experimentally)?

Thank you, yes we see how as written this was confusing. In our response to Reviewer #1, and in the text, we added an important detail:

While reorientations are modeled as discrete events, which is observationally true, the amount of M at time t=0 is chosen to be large (M₀ = 1000), so that over the timescale of 40 minutes, the decay in M is practically continuous. This ensures that sudden changes in reorientations are not due to sudden changes in M, but due to the inherent stochasticity of reorientations.

However you are correct that if M was chosen to have a binary value of 0 or 1, then this would indeed be the two state model. We added a new section to address this (Lines 253-287, Figure 3). Unlike the experiments, the two-state model produces bimodal distributions in slope and transition times, and these distributions are significantly different than the experimental data (Figure 3).

(5) Further, as currently stated in the paper, Equations 1-3 are only for the mean rate of events. However, the expectation value is not a complete description of a stochastic system. Instead, the authors need to formulate the equations for the probability of events, from which they can extract any moment (they write something in Figure 2a, but the notation there is unclear, and this needs to be incorporated here).

Thank you, yes please see our response to Reviewer #1. We have clarified the text in Lines 105-190.

(6) Equations 1-3 have three constants (alpha and gamma which were fit to the data, and M0 which was presumably set to 1000). How does the choice of M0 affect the results?

Thank you, this is a good question. We address this in lines 253-296. Briefly, the choice of M₀ does not have a strong effect on the results, unless we set it to M₀, which by definition, creates a two-state model. This model was significantly different than the experimental data, relative to the other models (Figure 3c).

(7) M decays to near 0 over 40 minutes, abolishing omega turns by the end of the simulations. Are omega turns entirely abolished in worms after 30-40 minutes off food? How do the authors reconcile this decay with the leveling of the turning rate in Figure 1a?

Yes, Reviewer #1 recommended adding a baseline reorientation rate which we did for all models (Equation 2). However, we should also note that in Klein et al they observed a continuous decay over 50 minutes. Though realistically, it is likely not plausible that worms will produce infinitely long runs at long time points.

(8) The fit given in Figure 2b does not look convincing. No statistical test was used to compare the two functions (empirical and fit). No error bars were given (to either). These should be added. In the discussion, the authors explain the discrepancy away as experimental limitations. This is not unreasonable, but on the flip side, makes the argument inconclusive. If the authors could model and simulate these limitations, and show that they account for the discrepancies with the data, the model would be much more compelling.

To do this, I would imagine that the authors would need to take the output of their model (lists of turning times) and convert them into simulated trajectories over time. These trajectories could be used to detect boundary events (for a given size of arena), collisions between individuals, etc. in their simulations and to see their effects on the turn statistics.

Thank you, we have added dashed lines to indicate standard deviation to Figures 2b and 3a. After running the models several times, we found that some of the small discrepancies noted (like s₁-s₂ < 0 for experiments but not the model), were spurious due to these data points being <1% of the data, so we cut this from the text. To compare how similar the continuous (M₀ > 1) and discrete (M₀ = 1) models were to the experimental data, we calculated a Jensen-Shannon distance for the models, and found that the discrete model was significantly more dissimilar to the experimental data than the continuous models (Lines 289-296, Figure 3c).

(9) The other figures similarly lack any statistical tests and by eye, they do not look convincing. The exception is the 6 anecdotal examples in Figure 2e. Those anecdotal examples match remarkably closely, almost suspiciously so. I'm not sure I understood this though - the caption refers to "different" models of M decay (and at least one of the 6 examples clearly shows a much shallower exponential). If different M models are allowed for each animal, this is no longer parsimonious. Are the results in Figure 2d for a single M model? Can Figure 2e explain the data with a single (stochastic) M model?

We certainly don’t want the panels in Figure 2e to be suspicious! These comparisons were drawn from calculating the correlations between all model traces and all experimental traces, and then choosing the top hits. Every time we run the simulation, we arrive at a different set of examples. Since it was recommended we add a baseline rate, these examples will be a completely different set when we run the simulation, again.

We apologize for the confusion regarding M. Since the worms do not all start out with identical reorientation rates, we drew the initial M value from a distribution centered on M₀ to match the initial distribution of observed experimental rates (Lines 206-214). However, the decay in M (γ), as well as α and β, are the same for all in silico animals.

(10) The left axes of Figure 2e should be reverted to cumulative counts (without the normalization).

Thank you, we made this change.

(11) The authors give an alternative model of a Levy flight, but do not give the obvious alternative models:<br /> a) the 1-state model in which P(t) = alpha exp (-gamma t) dt (i.e. a single stochastic process, without a hidden M, collapsing equations 1-3 into a single equation).

b) the originally proposed 2-state model (with 3 parameters, a high turn rate, a low turn rate, and the local-to-global search transition time, which can be taken from the data, or sampled from the empirical probability distributions). Why not? The former seems necessary to justify the more complicated 2-process model, and the latter seems necessary since it's the model they are trying to replace. Including these two controls would allow them to compare the number of free parameters as well as the model results. I am also surprised by the Levy model since Levy is a family of models. How were the parameters of the Levy walk chosen?

Thank you, we removed this section completely, as it is tangential to the main point of the paper.

(12) One point that is entirely missing in the discussion is the individuality of worms. It is by now well known that individual animals have individual behaviors. Some are slow/fast, and similarly, their turn rates vary. This makes this problem even harder. Combined with the tiny number of events concerned (typically 20-40 per experiment), it seems daunting to determine the underlying model from behavioral statistics alone.

Thank you, yes we should have been more explicit in the reasoning behind drawing the initial M from a distribution (response to comment #9). We assume that not every worm starts out with the same reorientation rate, but that some start out fast (high M) and some start out slow (low M). However, we do assume M decays with the same kinetics, which seems sufficient to produce the observed phenomena. Multiple decay rates are not needed to replicate the experimental data.

(13) That said, it's well-known which neurons underpin the suppression of turning events (starting already with Gray et al 2005, which, strangely, was not cited here). Some discussion of the neuronal predictions for each of the two (or more) models would be appropriate.

Thank you, yes we will add Gray et al, but also the more detailed response to Reviewer #2 (Lines 319-359 of manuscript).

(14) An additional point is the reliance entirely on simulations. A rigorous formulation (of the probability distribution rather than just the mean) should be analytically tractable (at least for the first moment, and possibly higher moments). If higher moments are not obtainable analytically, then the equations should be numerically integrable. It seems strange not to do this.

Thank you for suggesting this. For the Levy section (which we cut) this would have been an improvement. However, since the distributions of slope differences and transition times are based on a recursive algorithm, rather than an analytical formulation, we decided to use the Jensen-Shannon divergence to compare distributions (Lines 272-296, Figure 3c) since this is a parameter-free approach.

In summary, while sample simulations do nicely match the examples in the data (of discontinuous vs continuous turning rates), this is not sufficient to demonstrate that the transition from ARS to dispersion in C. elegans is, in fact, likely to be a single 'state', or this (eq 1-3) single state. Of course, the model can be made more complicated to better match the data, but the approach of the authors, seeking an elegant and parsimonious model, is in principle valid, i.e. avoiding a many-parameter model-fitting exercise.

As a qualitative exercise, the paper might have some merit. It demonstrates that apparently discrete states can sometimes be artifacts of sampling from smoothly time-changing dynamics. However, as a generic point, this is not novel, and so without the grounding in C. elegans data, is less interesting.

Thank you, we agree that this is a generic phenomenon, which is partly why we did this. The data from López-Cruz seem to agree in part with Calhoun et al, that claim abrupt transitions occur, and Klein et al, which claim they do not occur. Since the underlying phenomenon is stochastic, we propose the mixed observations of sudden and gradual changes in search strategy are simply the result of a stochastic process, which can produce both phenomena for individual observations. We hope this work can help clarify why sudden changes in search strategy are not consistently observed. We propose a simple hypothesis that there is no change in search strategy. The reorientation rate decays in time, and due to the stochastic nature of this behavior, what appears as a sudden change for individual observations is not due to an underlying decision, but rather the result of a stochastic process.

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Reply to the reviewers

1. General Statements

• This manuscript represents a full revision incorporating all reviewer recommendations; the additional follow-up experiments and expanded analyses will be presented in dedicated subsequent manuscripts.
• Congenital dyserythropoietic anemia type I (CDA-I) is a rare hereditary disease characterized by ineffective erythropoiesis and mutations in Codanin1 and CDIN1.
• Our study reveals the structural and functional dynamics of the CDIN1-Codanin1 complex, shedding light on the molecular mechanisms of protein-protein interactions implicated in CDA-I pathology.
• The main goal of our study was to examine the interaction between CDIN1 and the C‑terminal binding domain of Codanin1 using complementary biophysical approaches.
• We quantified binding and identified interacting regions of Codanin1 and CDIN1.
• We found that CDA-I-associated mutations in interacting regions disturb CDIN1‑Codanin1 complex.
• We proposed a hypothetical molecular model of CDIN1-Codanin1 role in CDA-I hallmarks development.
• Our initial studies on BioRxiv (2023) have been cited by leading publications in the field (Jeong, Frater et al. 2025, Sedor and Shao 2025, Nature Communications) and prompted further research on this topic.

2. Point-by-point description of the revisions

*Here we provide a point-by-point reply describing the revisions already carried out and included in the transferred manuscript. *

Reply to the reviewers

Reviewer #1 – Evidence, reproducibility and clarity

This is a rigorous biophysical characterization of a protein-protein interaction relevant to CDA-1 disease. The two proteins were purified in an E. coli host but CD and DLS was performed to ensure that the purified protein is well folded. An impressive native protein EMSA was used to show a 1:1 complex. While common for protein-nucleic acid complexes, EMSAs are much more challenging with protein complexes. A higher-running complex, likely a heterotetramer was implied at higher protein concentrations. These results were supported with SEC-MALS analysis and analytic ultracentrifugation analysis. Thermophoresis and ITC were used to report a nanomolar affinity of the proteins for each other. SEC-SAXS supported the conclusions about stoichiometry and composition inferred from the earlier methods and suggested that the dimerization interface comes from CDIN1. Next HDX-MS was used to identify putative interface residues, which were then mutated in each of the proteins and assessed for binding using coimmunoprecipitation. This study uses at least 10 orthogonal biophysical and/or biochemical methodologies to characterize an important protein-protein interaction and the analysis is clear and so is the writing. I couldn't (reading it once) find any grammatical or other errors in the text or figures. This manuscript is top-quality and suitable for publication.

__Reviewer #1 – Significance __

Such detailed structural and mechanistic studies are greatly lacking in many clinical conditions for which mutations are known (unless they cause cancer, neurodegenerative disease, and so on). We need more such studies on disease topics! This study will be of interest to the hematologic diseases community.

1. Response – ____Significance

We thank Reviewer #1 for the thoughtful and encouraging evaluation of our work. We are particularly grateful for recognizing the significance of studying protein-protein interaction in the context of CDA-I disease, as well as the rigor and clarity of our biophysical and biochemical characterization.

We appreciate the reviewer's acknowledgment of the challenges associated with native protein EMSAs. We are pleased that our use of multiple orthogonal techniques was recognized as a strength of the study. We are gratified that the comprehensiveness and coherence of our data and the manuscript's clarity were well received.

We thank the reviewer for noting the broader impact of our findings on the hematologic disease community. As highlighted, there is a pressing need for a mechanistic understanding of non-oncologic, non-neurodegenerative diseases, and our studies address this gap.

We are honored by the reviewer's endorsement of our manuscript as "top-quality and suitable for publication". We value the reviewer's highly supportive and motivating feedback.

__Reviewer #2 – 1. Evidence, reproducibility and clarity __

This manuscript presents structural and biochemical characterization of the interaction between CDIN1 and the C-terminal domain of Codanin1, shedding light on a complex implicated in Congenital Dyserythropoietic Anemia Type I (CDA-I). While the authors provide valuable structural insights and identify disease-associated mutations that impair CDIN1-Codanin1 binding, I think several important concerns should be addressed to strengthen both the mechanistic claims and their functional relevance.

Contradiction Between Stoichiometry Models:

The authors propose that CDIN1 and Codanin1Cterm primarily form a heterodimer in vitro. However, this appears to contradict previous reports indicating a tetra-heteromeric arrangement. Additionally, while CDIN1 homodimerize seems confusing to me, do the authors suggest it is stable without Codanin1? This seems contrary to findings that CDIN1 is unstable in the absence of Codanin1 (Sedor, S.F., Shao, S. nature comm 2025, Swickley, G., Bloch, Y., Malka, L. et al 2020 BMC Mol and Cell Biol). These inconsistencies raise concerns about whether the observed stoichiometries are physiologically relevant or artifacts of in vitro reconstitution, especially since full-length Codanin1 was not studied.

2.1 Response ____– Consistent stoichiometry of Codanin1Cterm

We thank Reviewer #2 for raising critical points regarding the stoichiometry and physiological relevance of the CDIN1-Codanin1 interaction. The following response clarifies the rationale and interpretation in relation to previous findings.

Stoichiometry of CDIN1-Codanin1Cterm complex:

Recent Cryo-EM studies of full-length Codanin1 (Jeong, Frater et al. 2025, Sedor and Shao 2025) suggest independent internal dimerization domains (452-798 and 841-1000 amino acid residue) driving homodimer formation, with each Codanin1 monomer binding one CDIN1 via the C-terminal region (1005-1227 amino acid residue), resulting in a tetra-heteromeric complex. Therefore, the complete assembly appears as a dimer of heterodimers in the full-length context.

In our study, Codanin1 was truncated to retain only the CDIN1-binding C-terminus (1005-1227 amino acid residues), eliminating the homodimerization ability of Codanin1. Hence, in the case of truncated Codanin1Cterm, the minimal complex we observe is a 1:1 heterodimer of CDIN1-Codanin1Cterm, which is fully consistent with the equimolar stoichiometry of CDIN1-Codanin1 complex seen in the full-length structure.

Stability and oligomeric state of CDIN1 in the absence of Codanin1:

We concur with the reviewer that Sedor et al. (2025) and Swickley et al. (2020) reported decreased CDIN1 levels in cells lacking Codanin1, implying in vivo dependence of CDIN1 on Codanin1 partner for stability (Swickley, Bloch et al. 2020, Sedor and Shao 2025). The purified CDIN1 is monodisperse (Supplementary Figure 2D), exhibits thermal stability with a melting temperature of 48 °C (Supplementary Figure 2E), and displays proper folding as indicated by CD measurements (Supplementary Figure 2B). Additionally, SAXS profiles of CDIN1 correspond to AlphaFold predictions (Fig. 2B). Together, our findings indicate that the recombinant CDIN1 forms a stable conformation in vitro without Codanin1. To the best of our knowledge, no previous research has directly identified the endogenous oligomeric states of CDIN1 within cellular content.

We fully acknowledge that future analysis of the full-length Codanin1-CDIN1 assembly in a cellular context will be necessary for understanding physiological stoichiometries. As outlined in the General statements, our study focuses on the C-terminus of Codanin1 to describe the binding interface and complex biophysical properties of the CDIN-Codanin1Cterm complex.

__Reviewer #2 – ____2. Unvalidated Functional Claims: __

The manuscript identifies several CDA-I-associated mutations that disrupt CDIN1-Codanin1 interaction. However, the authors do not test how these mutations affect the biological function of the complex, particularly its role in ASF1 sequestration or histone trafficking. Given the central importance of this axis in their disease model, functional validation (e.g., ASF1 localization, histone deposition assays) is necessary to support these mechanistic conclusions.

2.2 Response – ____Hypothetical model as discussion merit

We thank the reviewer for the comment regarding the functional implications of CDA-I-associated mutations and their potential impact on ASF1 sequestration and histone trafficking hypothesized within the Discussion. We fully agree that understanding the downstream biological consequences of disrupted CDIN1-Codanin1 interaction is critical for elucidating the full molecular basis of CDA-I pathogenesis.

In the Future research directions of the Discussion, we have acknowledged and emphasized the need for follow-up studies using erythroblast cell lines to determine whether specific disease-associated mutations disrupt CDIN1-Codanin1 binding, leading to functional defects relevant to erythropoiesis and nuclear architecture typical for CDA-I disease.

However, as we respectfully note in General Statements, the main aim of the present study was to provide a rigorous biophysical characterization of the CDIN1-Codanin1Cterm interaction. Proposed cellular experiments, though relevant, are beyond the conceptual scope of the presented studies.

Reviewer #2 – ____3. Speculative and Potentially Contradictory Model:

The proposed model suggests that CDIN1 competes with ASF1 for Codanin1 binding, thereby indirectly promoting histone delivery to the nucleus. However, emerging data indicate that Codanin1, CDIN1, and ASF1 can form a stable ternary complex, calling into question this competitive binding hypothesis (Sedor, S.F., Shao, S. nature comm 2025). The authors do not acknowledge or discuss these findings, and the model in its current form may therefore be oversimplified or inaccurate.

2.3 Response – ____Hypothetical model fully aligned with current knowledge

We fully acknowledged and discussed in the current manuscript the recent findings demonstrating that Codanin1, CDIN1, and ASF1 can form a ternary complex (Sedor, S.F., Shao, S. Nature Comm. 2025; Jeong, T. K. et al. Nature Comm. 2025). Our revised model was updated accordingly to reflect the collaborative binding of Codanin1, CDIN1, and ASF1, and is presented in alignment with published data.

While earlier versions of our work published on the BioRxiv server (May 26, 2023) proposed a competitive hypothesis, the current manuscript incorporates recent literature and prior reviewer feedback to offer a refined model. We believe that the updated hypothesis suggests a plausible mechanism for how CDIN1 modulates Codanin1 function, which will be further tested in future cellular studies.

Reviewer #2 – 4. Significance:

Overall, the study adds to our structural understanding of CDIN1 and Codanin1 interactions, but the functional interpretations are currently speculative, and in some cases in conflict with existing literature. The manuscript would benefit significantly from addressing these discrepancies, incorporating relevant data on ASF1, and clarifying whether the observed assemblies reflect physiological complexes.

__2.4 Response – Significance __

We thank Reviewer #2 for the constructive feedback. As noted in General Statements, our current manuscript is primarily dedicated to defining the molecular architecture and interactions of the CDIN1–Codanin1Cterm core interface. We agree that follow-up ASF1‑dependent functional assays will be critical to fully validate observed assemblies, but these experiments lie outside the scope of the present study and are ongoing in our laboratory.

To address the reviewer's concern about possible speculative interpretation, we have:

• Used cautious language in Results and Discussion to prevent overstatement (e.g., page 31, line 754, “leads” exchanged to “may contribute” in legend of Fig. 4).
• Described in the Discussion how our results enhance and add understanding to the body of published structural data of CDIN1–Codanin1Cterm.
• Updated our hypothetical model in Fig. 4 to be fully in line with published data.
• Clearly stated that the working hypothesis is connected with a subset of CDA-I mutations (p. 31, l. 758-759, “The proposed model represents a working hypothesis relating to a subset of CDA-I mutations and is not currently substantiated by experimental evidence at the cellular level.”)
• Stated in Future research directions of Discussion that functional validation, including ASF1, will motivate future critical studies, p. 32, l. 771-773: “The ability of Codanin1 to interact with both CDIN1 and ASF1 motivates further investigation of how CDIN1 and ASF1 affect the function of full-length Codanin1, which even recent cryo-EM data has not addressed yet.”
• Highlighted the necessity of complementary in vivo studies in erythroblast cell lines to determine if CDA-I-related mutations in CDIN1-Codanin1 interaction region cause typical CDA-I phenotypes, aiming to clarify the molecular mechanisms of inherited CDA-I anemia. We state in Future research directions in Discussion, p. 32, l. 774-780: “…follow-up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding also affect ASF1 localization and cause a phenotype typical of CDA-I. In future work, additional Codanin1 mutations, including those outside the C-terminal region, should be evaluated to determine how the mutations affect ASF1’s nuclear concentration and subcellular localization. The proposed research directions will provide additional deeper insights into the underlying mechanisms of the molecular origin of inherited anemia CDA-I.” We believe that the revisions objectively clarify the significance and the limits of the current work and set the stage for the detailed functional studies to follow.

__Reviewer #3 – Evidence, reproducibility and clarity: __

Congenital Dyserythropoietic Anemia Type I (CDA I) is an autosomal recessive disorder characterized by ineffective erythropoiesis and distinctive nuclear morphology ("Swiss cheese" heterochromatin) in erythroblasts. CDA I is caused by mutations in CDAN1 and CDIN1. Codanin1, encoded by CDAN1, is part of the cytosolic ASF1-H3.1-H4-Importin-4 complex, which regulates histone trafficking to the nucleus. CDIN1 has been shown to bind the C-terminal domain of Codanin-1, but until now, pathogenic mutations had not been directly linked to the disruption of this interaction.

In this study, the authors used biophysical techniques to characterize the interaction between Codanin-1's C-terminal region (residues 1005-1227) and CDIN1, demonstrating high-affinity, equimolar binding. HDX-MS identified interaction hotspots, and disease-associated mutations in these regions disrupted complex formation. The authors propose that such disruption prevents ASF1 sequestration in the cytoplasm, thereby reducing nuclear histone levels and contributing to the chromatin abnormalities seen in CDA I.

Major Comments:

1. Use of Codanin-1 Fragment:

Most experiments were conducted using only the C-terminal 223 amino acids of Codanin-1. While this region is known to bind CDIN1, it is unclear whether its conformation is maintained in the context of the full-length protein. This could affect binding properties and structural interpretations. The authors should discuss how structural differences between the isolated C-terminus and the full-length Codanin-1 may influence the conclusions.

Response of authors ____#3

3.1 Response: Use of Codanin-1 Fragment as biding part to CDIN1

We thank the reviewer for the important observation regarding the use of the C-terminal fragment of Codanin1. As noted in the manuscript (e.g., p. 30, line 721 and p. 32, line 761), we fully acknowledge that the truncation of Codanin1 may influence its conformational dynamics or contextual folding relative to the full-length protein.

However, several lines of evidence suggest that the C-terminal 223 amino acid residues—responsible for CDIN1 binding—are structurally autonomous and have minimal intramolecular contacts with upstream regions. Published cryo-EM and biochemical data (Jeong, Frater et al. 2025, Sedor and Shao 2025), in conjunction with AlphaFold structural predictions (Fig. 2D) and our co-immunoprecipitation assays (Fig. 3F), consistently support a model wherein the CDIN1-binding region is flexible and spatially isolated from the core structural domains of Codanin1. Additionally, results from our co-immunoprecipitation assay (Fig. 3F) indicate that full-length Codanin1 and truncated Codanin1Cterm interact with CDIN1 similarly, further supporting the isolated manner of the C-terminal fragment. The available data together imply that the C-terminal fragment used in our study retains its native conformation and binding properties when expressed independently.

While our findings are confined to the interaction domain and do not reflect full-length Codanin1’s architecture, we believe the use of the C-terminal minimal fragment of Codanin1 enables precise dissection of the CDIN1-binding interface and yields mechanistic insights without introducing significant structural artifacts.

We agree with the reviewer that future work incorporating full-length Codanin1, especially in a cellular context, will be instrumental to fully characterize higher-order assembly and regulatory functions.

__Reviewer #3 – 2. ____Graphical Abstract and Domain Independence: __

The graphical abstract presents the Codanin-1 C-terminus as an independent domain, but no direct evidence is provided to support its structural autonomy in vivo.

The authors should clarify whether the C-terminal region functions as a distinct domain in the context of the full-length protein.

__3.2 Response –____ Independent C-terminal domain __

We thank the reviewer for bringing up the question of the independence of the C-terminal domain. Although direct in vivo proof of C-terminal autonomy is not yet available, published cryo-EM structures of full-length Codanin1, our biophysical characterization, and AlphaFold models all consistently indicate that the C-terminal 223 amino acid residues of Codanin1 form a structurally independent binding module. In the graphical abstract, we illustrated the C‑terminal domain as a loosely connected part of Codanin1 to highlight its independence and to emphasize the specific focus of our studies.

To articulate limitations of our studies focused on the C-terminal part of Codanin1, we stated in the Functional implications of CDA-I-related mutations in the Discussion, p. 30, l. 721-724: “However, our measurements do not exclude the possible role of the disordered regions in full-length Codanin1. For example, CDIN1 could potentially stabilize full-length Codanin1 by rearranging the disordered regions into a more condensed structure, thereby augmenting the structural stability of Codanin1.”

Reviewer #3 – 3.____Pathogenic Mutations Beyond the Binding Site:

The study highlights a triplet mutation that impairs CDIN1 binding. However, most CDA I‑associated mutations in CDAN1 are dispersed across the entire protein and may not affect CDIN1 interaction directly.

The authors should discuss alternative mechanisms by which mutations in other regions of Codanin-1 might cause disease.

3.3 Response – Pathogenic mutations outside the binding site – alternative mechanisms

We appreciate the reviewer noting that most CDA-I-associated CDAN1 mutations are outside the CDIN1-Codanin1 binding site and suggesting alternative mechanisms. In the revised Discussion, we added a paragraph on alternative pathogenic models, p. 29, l. 702-713:

"Our study centers on the CDIN1-binding C-terminus, however, most CDA-I-associated CDAN1 mutations lie elsewhere and probably act through alternative mechanisms. Mutations such as P672L and F868I in the LOBE2 (452-798 amino acid residue) and F868I in the coiled-coil (841-1000 amino acid residue) domains may disturb Codanin1 homodimerization and higher-order complex assembly, directly affecting ASF1 sequestration (Jeong, T. K. et al. Nature Comm. 2025). Other mutant variants may also interfere with ASF1 sequestration, nuclear targeting, or chromatin-remodeling functions, while destabilizing mutations may induce misfolding and proteasomal degradation. Moreover, CDA-I-associated mutations, such as R714W and R1042W, might compromise the interaction between Codanin1 and ASF1 (Ask, Jasencakova et al. 2012). Collectively, the complementary alternative pathogenic mechanisms associated with Codanin1 mutations in distal regions and mutations in CDIN1‑binding C-terminus of Codanin1 may contribute to erythroid dysfunction in CDA-I."

Reviewer #3 – 4. ____Contradictory Functional Models:

Ask et al. (EMBO J, 2012) reported that Codanin-1 depletion increases nuclear ASF1 and accelerates DNA replication. This contrasts with the current hypothesis that disruption of the Codanin-1/CDIN1 complex reduces nuclear ASF1.

The authors should attempt to reconcile this apparent contradiction, possibly by proposing a context-specific or dual-function model for Codanin-1 in histone trafficking.

3.4 Response – ____Clarified explanation of hypothetical functional model

We thank the reviewer for raising this point, which improved the clarity of our work. There is no real discrepancy between Ask et al. and our findings; both agree that Codanin1 restrains ASF1 in the cytoplasm. Ask et al. examined the complete loss of Codanin1, which abolishes cytoplasmic ASF1 sequestration and thus leads to maximal nuclear accumulation. We suggest the CDA-I-associated mutations selectively disrupt the CDIN1-Codanin1 interface, releasing ASF1 from the cytoplasm into the nucleus.

To enhance clarity, we now state in the legend of Figure 4 describing the hypothesis (p. 31, l. 752-753): "…CDA-I-associated mutations prevent CDIN1-Codanin1 complex formation, thus prevent ASF1 sequestration to cytoplasm; ASF1 remains accumulated in nucleus."

Reviewer #3 – 5. ____Conclusions and Claims:

The proposed model of CDA I pathogenesis (Fig. 4) is plausible but not yet fully supported by the available data. The authors suggest that disruption of the Codanin-1/CDIN1 interaction leads to nuclear histone depletion, but this has not been experimentally confirmed.

Claims about the general pathogenesis of CDA I should be clearly qualified as hypothetical and applicable to a subset of mutations. The presence and localization of ASF1 in the nucleus following disruption of the Codanin-1/CDIN1 complex should be tested experimentally.

3.5 Response – __Tempered ____conclusions and claims: __

We thank the reviewer for underscoring the need to temper our conclusions and to distinguish hypotheses from available results. We fully agree that our Fig. 4 model—linking disruption of the Codanin1-CDIN1 interface to nuclear histone imbalance—remains a working hypothesis, currently supported by indirect biochemical and structural data.

Accordingly, we have:

• Revised the text to explicitly state that this model is hypothetical and pertains to a subset of CDA-I-associated CDAN1 mutations. Specifically, we

• Added to the last paragraph of the section Functional implications of CDA-I-related mutations in Discussion (p. 31, l. 744-749): “In considering functional implications of our findings within available data, it is essential to qualify that mechanistic claims regarding the general pathogenesis of CDA-I remain hypothetical and are restricted to a specific subset of mutations. Furthermore, direct experimental validation, such as immunolocalization or live-cell imaging, to assess ASF1’s nuclear presence and distribution following disruption of the CDIN1-Codanin1 complex is required to substantiate the proposed model.”

• Included in the legend of Fig. 4: ”The proposed model represents a working hypothesis relating to a subset of CDA-I mutations and is not currently substantiated by experimental evidence at the cellular level.”
• Replaced any associated definitive language (e.g., “leads to”) with qualified phrasing (e.g., “may contribute to”) in the legend of Fig. 4.
• Clarified in the Discussion that direct measurement of nuclear ASF1 redistribution and histone levels following interface disruption has not yet been performed. Specifically, we added to the section Functional implications of CDA-I-related mutations in Discussion (p. 30, l. 734-735): “It should be noted, however, that direct quantification of nuclear ASF1 redistribution and histone levels after CDIN1-Codanin1 disruption has not yet been conducted.” Although experimental verification of nuclear ASF1 localization upon CDIN1-Codanin1 complex disruption falls beyond the current manuscript’s scope, we acknowledge its importance and have emphasized the need for such studies in future work within the Future research directions of the Discussion. Specifically, we concluded by stating (p. 32, l. 774-776): “Finally, follow‑up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding, also affect ASF1 localization and cause a phenotype typical of CDA-I.”

__Reviewer #3 – 6.____Broader Mutation Analysis and ASF1 Localization: __

To strengthen the link between Codanin-1/CDIN1 disruption and disease pathogenesis, it would be important to test the effects of additional CDAN1 mutations, including those outside the C-terminal region. Similarly, the impact on ASF1 nuclear concentration and localization should be directly assessed. These experiments would significantly bolster the central hypothesis. If feasible, they should be pursued or at least acknowledged as important future directions.

3.6 Response – Broader mutation analysis and ASF1 localization in future directions

We thank Reviewer #3 for emphasizing the value of a broader mutation survey and direct ASF1 localization studies. As noted above, our current manuscript is centered on delineating the molecular architecture of the CDIN1-Codanin1Cterm core interface; comprehensive mutational analyses outside the C-terminal binding region and ASF1-dependent functional assays will be critical to extend these findings but fall beyond the scope of the present work and will be the objective of our following studies. To address the reviewer’s concern, we have:

• Expanded the Future Directions section to specify that additional CDA-I-linked CDAN1 variants, including non-C-terminal mutations, and quantitative assessments of ASF1 nuclear localization will be the subject of ongoing and planned investigations. Specifically, we added (p. 32, l. 776-778):” In future work, additional Codanin1 mutations, including those outside the C-terminal region, should be evaluated to determine how the mutations affect ASF1’s nuclear concentration and subcellular localization.”

• Emphasized the need for complementary in vivo validation in erythroblast models to confirm whether the disturbance of CDIN1-Codanin1 binding recapitulates CDA-I phenotypes. We acknowledged the need for cell-line studies in future work within the Future research directions of Discussion (p. 32, l. 774-776): “Finally, follow-up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding, also affect ASF1 localization and cause a phenotype typical of CDA-I.” We believe these changes more precisely delimit the scope and significance of the current study while laying out a clear roadmap for the essential follow-up experiments.

Reviewer #3 – 7. ____Rigor and Presentation and Cross-commenting

__Minor Comments: __

• Methods and Reproducibility:

The experimental methods are well described, and the results appear reproducible.

• Presentation:

The text and figures are clear and well organized.

Referee Cross-commenting

I agree with reviewer 1 that the paper presents detailed structure study of Codanin-1 and CDIN1 protein. However, as reviewer 2 claims functional studies are missing and therefore the hypothesis regarding the pahtogenesis of CDAI is speculaltive especially with no studies regarding ASF1.

3____.7 Response ____–____ Rigor and Presentation and Cross-commenting:

We thank the reviewers for their positive appraisal of our results' reproducibility, presentation, and method descriptions. We also appreciate the cross-comment that, while our structural analysis of the CDIN1-Codanin1 complex is thorough, functional validation, particularly regarding ASF1, remains to be addressed.

As outlined above, we have revised the manuscript to:

• Emphasize that pathogenic hypotheses drawn from structural data are provisional (refer to Responses 2.2, 2.3, and 3.5).
• Include follow-up studies for ASF1 localization assays and broader mutation profiling in our Future Directions (refer to Responses 2.4, 3.5, 3.6).
• Integrate cautious language throughout to clearly delineate verified findings from model-based speculation (refer to Responses 2.4, 3.5, 3.6). The implemented adjustments ensure that the current work is positioned as a detailed structural and interaction foundation, upon which the essential functional studies will build. We believe that all extensions and clarifications fully satisfy the reviewers’ collective recommendations.

__Reviewer #3 –____ Significance: __

Nature and Significance of the Advance:

This study extends prior work (e.g., Swickley et al., BMC Mol Cell Biol 2020; Shroff et al., Biochem J 2020) on Codanin-1/CDIN1 interaction by applying high-resolution biophysical techniques to identify mutations that disrupt this complex. It provides a plausible cellular mechanism by which specific mutations may lead to CDA I through impaired histone trafficking.

Nevertheless, key question remains: How do mutations outside the Codanin-1 C-terminus contribute to the pathology?

3.8 Response – Significance:

• We thank Reviewer #3 for this important point. Although our work specifically dissects the C-terminal CDIN1-binding domain of Codanin1, we fully acknowledge that CDA-I-associated mutations throughout Codanin1 may operate via additional mechanisms. To address the additional mechanisms, we have added a new paragraph describing other possible pathogenic models to the Discussion (please refer to Response 3.3).
• We also fully acknowledged the need for systematic functional assays of non-C-terminal mutations and their impact on ASF1 localization (please refer to Response 3.6).

• We revised the text to clarify how mutations beyond the C-terminus may contribute to CDA-I pathogenesis and present the significance of our current structural analyses, biophysical characterizations, and molecular insights as a foundation for future research (please refer to Response 3.6). __Audience: __

• Molecular and cellular biologists investigating nuclear-cytoplasmic trafficking mechanisms

• Hematologists and geneticists studying rare red cell disorders
• Clinicians managing CDA I patients and researchers exploring targeted therapies __Reviewer Expertise: __

Pediatric hematologist with over 20 years of research experience in CDA I, including the initial identification of CDAN1 and the elucidation of Codanin-1's role in embryonic erythropoiesis. Not a specialist in the biophysical techniques used in this study.

References

Ask, K., Z. Jasencakova, P. Menard, Y. Feng, G. Almouzni and A. Groth (2012). "Codanin-1, mutated in the anaemic disease CDAI, regulates Asf1 function in S-phase histone supply." The EMBO Journal 31(8): 2013–2023.

Jeong, T.-K., R. C. M. Frater, J. Yoon, A. Groth and J.-J. Song (2025). "CODANIN-1 sequesters ASF1 by using a histone H3 mimic helix to regulate the histone supply." Nature Communications 16(1): 2181.

Sedor, S. F. and S. Shao (2025). "Mechanism of ASF1 engagement by CDAN1." Nature Communications 16(1): 2599.

Swickley, G., Y. Bloch, L. Malka, A. Meiri, S. Noy-Lotan, A. Yanai, H. Tamary and B. Motro (2020). "Characterization of the interactions between Codanin-1 and C15Orf41, two proteins implicated in congenital dyserythropoietic anemia type I disease." Molecular and Cell Biology 21(1).

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Reply to the reviewers

Reply to the Reviewers

I would like to thank the reviewers for their comments and interest in the manuscript and the study.

Reviewer #1

1. I would assume that there are RNA-seq and/or ChIP-seq data out there produced after knockdown of one or more of these DBPs that show directional positioning.

The directional positioning of CTCF-binding sites at chromatin interaction sites was analyzed by CRISPR experiment (Guo Y et al. Cell 2015). We found that the machine learning and statistical analysis showed the same directional bias of CTCF-binding motif sequence and RAD21-binding motif sequence at chromatin interaction sites as the experimental analysis of Guo Y et al. (lines 229-253, Figure 3b, c, d and Table 1). Since CTCF is involved in different biological functions (Braccioli L et al. Essays Biochem. 2019 ResearchGate webpage), the directional bias of binding sites may be reduced in all binding sites including those at chromatin interaction sites (lines 68-73). In our study, we investigated the DNA-binding sites of proteins using the ChIP-seq data of DNA-binding proteins and DNase-seq data. We also confirmed that the DNA-binding sites of SMC3 and RAD21, which tend to be found in chromatin loops with CTCF, also showed the same directional bias as CTCF by the computational analysis.

__2. Figure 6 should be expanded to incorporate analysis of DBPs not overlapping CTCF/cohesin in chromatin interaction data that is important and potentially more interesting than the simple DBPs enrichment reported in the present form of the figure. __

Following the reviewer's advice, I performed the same analysis with the DNA-binding sites that do no overlap with the DNA-binding sites of CTCF and cohesin (RAD21 and SMC3) (Fig. 6 and Supplementary Fig. 4). The result showed the same tendency in the distribution of DNA-binding sites. The height of a peak on the graph became lower for some DNA-binding proteins after removing the DNA-binding sites that overlapped with those of CTCF and cohesin. I have added the following sentence on lines 435 and 829: For the insulator-associated DBPs other than CTCF, RAD21, and SMC3, the DNA-binding sites that do not overlap with those of CTCF, RND21, and SMC3 were used to examine their distribution around interaction sites.

3. Critically, I would like to see use of Micro-C/Hi-C data and ChIP-seq from these factors, where insulation scores around their directionally-bound sites show some sort of an effect like that presumed by the authors - and many such datasets are publicly-available and can be put to good use here.

As suggested by the reviewer, I have added the insulator scores and boundary sites from the 4D nucleome data portal as tracks in the UCSC genome browser. The insulator scores seem to correspond to some extent to the H3K27me3 histone marks from ChIP-seq (Fig. 4a and Supplementary Fig. 3). We found that the DNA-binding sites of the insulator-associated DBPs were statistically overrepresented in the 5 kb boundary sites more than other DBPs (Fig. 4d). The direction of DNA-binding sites on the genome can be shown with different colors (e.g. red and green), but the directionality of insulator-associated DNA-binding sites is their overall tendency, and it may be difficult to notice the directionality from each binding site because the directionality may be weaker than that of CTCF, RAD21, and SMC3 as shown in Table 1 and Supplementary Table 2. We also observed the directional biases of CTCF, RAD21, and SMC3 by using Micro-C chromatin interaction data as we estimated, but the directionality was more apparent to distinguish the differences between the four directions of FR, RF, FF, and RR using CTCF-mediated ChIA-pet chromatin interaction data (lines 287 and 288).

 I found that the CTCF binding sites examined by a wet experiment in the previous study may not always overlap with the boundary sites of chromatin interactions from Micro-C assay (Guo Y et al. *Cell* 2015). The chromatin interaction data do not include all interactions due to the high sequencing cost of the assay, and include less long-range interactions due to distance bias. The number of the boundary sites may be smaller than that of CTCF binding sites acting as insulators and/or some of the CTCF binding sites may not be locate in the boundary sites. It may be difficult for the boundary location algorithm to identify a short boundary location. Due to the limitations of the chromatin interaction data, I planned to search for insulator-associated DNA-binding proteins without using chromatin interaction data in this study.

 I discussed other causes in lines 614-622: Another reason for the difference may be that boundary sites are more closely associated with topologically associated domains (TADs) of chromosome than are insulator sites. Boundary sites are regions identified based on the separation of numerous chromatin interactions. On the other hand, we found that the multiple DNA-binding sites of insulator-associated DNA-binding proteins were located close to each other at insulator sites and were associated with distinct nested and focal chromatin interactions, as reported by Micro-C assay. These interactions may be transient and relatively weak, such as tissue/cell type, conditional or lineage-specific interactions.

 Furthermore, I have added the statistical summary of the analysis in lines 372-395 as follows: Overall, among 20,837 DNA-binding sites of the 97 insulator-associated proteins found at insulator sites identified by H3K27me3 histone modification marks (type 1 insulator sites), 1,315 (6%) overlapped with 264 of 17,126 5kb long boundary sites, and 6,137 (29%) overlapped with 784 of 17,126 25kb long boundary sites in HFF cells. Among 5,205 DNA-binding sites of the 97 insulator-associated DNA-binding proteins found at insulator sites identified by H3K27me3 histone modification marks and transcribed regions (type 2 insulator sites), 383 (7%) overlapped with 74 of 17,126 5-kb long boundary sites, 1,901 (37%) overlapped with 306 of 17,126 25-kb long boundary sites. Although CTCF-binding sites separate active and repressive domains, the limited number of DNA-binding sites of insulator-associated proteins found at type 1 and 2 insulator sites overlapped boundary sites identified by chromatin interaction data. Furthermore, by analyzing the regulatory regions of genes, the DNA-binding sites of the 97 insulator-associated DNA-binding proteins were found (1) at the type 1 insulator sites (based on H3K27me3 marks) in the regulatory regions of 3,170 genes, (2) at the type 2 insulator sites (based on H3K27me3 marks and gene expression levels) in the regulatory regions of 1,044 genes, and (3) at insulator sites as boundary sites identified by chromatin interaction data in the regulatory regions of 6,275 genes. The boundary sites showed the highest number of overlaps with the DNA-binding sites. Comparing the insulator sites identified by (1) and (3), 1,212 (38%) genes have both types of insulator sites. Comparing the insulator sites between (2) and (3), 389 (37%) genes have both types of insulator sites. From the comparison of insulator and boundary sites, we found that (1) or (2) types of insulator sites overlapped or were close to boundary sites identified by chromatin interaction data.

4. The suggested alternative transcripts function, also highlighted in the manuscripts abstract, is only supported by visual inspection of a few cases for several putative DBPs. I believe this is insufficient to support what looks like one of the major claims of the paper when reading the abstract, and a more quantitative and genome-wide analysis must be adopted, although the authors mention it as just an 'observation'.

According to the reviewer's comment, I performed the genome-wide analysis of alternative transcripts where the DNA-binding sites of insulator-associated proteins are located near splicing sites. The DNA-binding sites of insulator-associated DNA-binding proteins were found within 200 bp centered on splice sites more significantly than the other DNA-binding proteins (Fig. 4e and Table 2). I have added the following sentences on lines 405 - 412: We performed the statistical test to estimate the enrichment of insulator-associated DNA-binding sites compared to the other DNA-binding proteins, and found that the insulator-associated DNA-binding sites were significantly more abundant at splice sites than the DNA-binding sites of the other proteins (Fig 4e and Table 2; Mann‒Whitney U test, p value 5. Figure 1 serves no purpose in my opinion and can be removed, while figures can generally be improved (e.g., the browser screenshots in Figs 4 and 5) for interpretability from readers outside the immediate research field.

I believe that the Figure 1 would help researchers in other fields who are not familiar with biological phenomena and functions to understand the study. More explanation has been included in the Figures and legends of Figs. 4 and 5 to help readers outside the immediate research field understand the figures.

6. Similarly, the text is rather convoluted at places and should be re-approached with more clarity for less specialized readers in mind.

Reviewer #2's comments would be related to this comment. I have introduced a more detailed explanation of the method in the Results section, as shown in the responses to Reviewer #2's comments.

Reviewer #2

1. Introduction, line 95: CTCF appears two times, it seems redundant.

On lines 91-93, I deleted the latter CTCF from the sentence "We examine the directional bias of DNA-binding sites of CTCF and insulator-associated DBPs, including those of known DBPs such as RAD21 and SMC3".

2. Introduction, lines 99-103: Please stress better the novelty of the work. What is the main focus? The new identified DPBs or their binding sites? What are the "novel structural and functional roles of DBPs" mentioned?

Although CTCF is known to be the main insulator protein in vertebrates, we found that 97 DNA-binding proteins including CTCF and cohesin are associated with insulator sites by modifying and developing a machine learning method to search for insulator-associated DNA-binding proteins. Most of the insulator-associated DNA-binding proteins showed the directional bias of DNA-binding motifs, suggesting that the directional bias is associated with the insulator.

 I have added the sentence in lines 96-99 as follows: Furthermore, statistical testing the contribution scores between the directional and non-directional DNA-binding sites of insulator-associated DBPs revealed that the directional sites contributed more significantly to the prediction of gene expression levels than the non-directional sites. I have revised the statement in lines 101-110 as follows: To validate these findings, we demonstrate that the DNA-binding sites of the identified insulator-associated DBPs are located within potential insulator sites, and some of the DNA-binding sites in the insulator site are found without the nearby DNA-binding sites of CTCF and cohesin. Homologous and heterologous insulator-insulator pairing interactions are orientation-dependent, as suggested by the insulator-pairing model based on experimental analysis in flies. Our method and analyses contribute to the identification of insulator- and chromatin-associated DNA-binding sites that influence EPIs and reveal novel functional roles and molecular mechanisms of DBPs associated with transcriptional condensation, phase separation and transcriptional regulation.

3. Results, line 111: How do the SNPs come into the procedure? From the figures it seems the input is ChIP-seq peaks of DNBPs around the TSS.

On lines 121-124, to explain the procedure for the SNP of an eQTL, I have added the sentence in the Methods: "If a DNA-binding site was located within a 100-bp region around a single-nucleotide polymorphism (SNP) of an eQTL, we assumed that the DNA-binding proteins regulated the expression of the transcript corresponding to the eQTL".

4. Again, are those SNPs coming from the different cell lines? Or are they from individuals w.r.t some reference genome? I suggest a general restructuring of this part to let the reader understand more easily. One option could be simplifying the details here or alternatively including all the necessary details.

On line 119, I have included the explanation of the eQTL dataset of GTEx v8 as follows: " The eQTL data were derived from the GTEx v8 dataset, after quality control, consisting of 838 donors and 17,382 samples from 52 tissues and two cell lines". On lines 681 and 865, I have added the filename of the eQTL data "(GTEx_Analysis_v8_eQTL.tar)".

5. Figure 1: panel a and b are misleading. Is the matrix in panel a equivalent to the matrix in panel b? If not please clarify why. Maybe in b it is included the info about the SNPs? And if yes, again, what is then difference with a.

The reviewer would mention Figure 2, not Figure 1. If so, the matrices in panels a and b in Figure 2 are equivalent. I have shown it in the figure: The same figure in panel a is rotated 90 degrees to the right. The green boxes in the matrix show the regions with the ChIP-seq peak of a DNA-binding protein overlapping with a SNP of an eQTL. I used eQTL data to associate a gene with a ChIP-seq peak that was more than 2 kb upstream and 1 kb downstream of a transcriptional start site of a gene. For each gene, the matrix was produced and the gene expression levels in cells were learned and predicted using the deep learning method. I have added the following sentences to explain the method in lines 133 - 139: Through the training, the tool learned to select the binding sites of DNA-binding proteins from ChIP-seq assays that were suitable for predicting gene expression levels in the cell types. The binding sites of a DNA-binding protein tend to be observed in common across multiple cell and tissue types. Therefore, ChIP-seq data and eQTL data in different cell and tissue types were used as input data for learning, and then the tool selected the data suitable for predicting gene expression levels in the cell types, even if the data were not obtained from the same cell types.

6. Line 386-388: could the author investigate in more detail this observation? Does it mean that loops driven by other DBPs independent of the known CTCF/Cohesin? Could the author provide examples of chromatin structural data e.g. MicroC?

As suggested by the reviewer, to help readers understand the observation, I have added Supplementary Fig. S4c to show the distribution of DNA-binding sites of "CTCF, RAD21, and SMC3" and "BACH2, FOS, ATF3, NFE2, and MAFK" around chromatin interaction sites. I have modified the following sentence to indicate the figure on line 501: Although a DNA-binding-site distribution pattern around chromatin interaction sites similar to those of CTCF, RAD21, and SMC3 was observed for DBPs such as BACH2, FOS, ATF3, NFE2, and MAFK, less than 1% of the DNA-binding sites of the latter set of DBPs colocalized with CTCF, RAD21, or SMC3 in a single bin (Fig. S4c).

 In Aljahani A et al. *Nature Communications* 2022, we find that depletion of cohesin causes a subtle reduction in longer-range enhancer-promoter interactions and that CTCF depletion can cause rewiring of regulatory contacts. Together, our data show that loop extrusion is not essential for enhancer-promoter interactions, but contributes to their robustness and specificity and to precise regulation of gene expression. Goel VY et al. *Nature Genetics* 2023 mentioned in the abstract: Microcompartments frequently connect enhancers and promoters and though loss of loop extrusion and inhibition of transcription disrupts some microcompartments, most are largely unaffected. These results suggested that chromatin loops can be driven by other DBPs independent of the known CTCF/Cohesin.

I added the following sentence on lines 569-577: The depletion of cohesin causes a subtle reduction in longer-range enhancer-promoter interactions and that CTCF depletion can cause rewiring of regulatory contacts. Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently. Furthermore, the loop extrusion is not essential for enhancer-promoter interactions, but contributes to their robustness and specificity and to precise regulation of gene expression.

 FOXA1 pioneer factor functions as an initial chromatin-binding and chromatin-remodeling factor and has been reported to form biomolecular condensates (Ji D et al. *Molecular Cell* 2024). CTCF have also found to form transcriptional condensate and phase separation (Lee R et al. *Nucleic acids research* 2022). FOS was found to be an insulator-associated DNA-binding protein in this study and is potentially involved in chromatin remodeling, transcription condensation, and phase separation with the other factors such as BACH2, ATF3, NFE2 and MAFK. I have added the following sentence on line 556: FOXA1 pioneer factor functions as an initial chromatin-binding and chromatin-remodeling factor and has been reported to form biomolecular condensates.

7. In general, how the presented results are related to some models of chromatin architecture, e.g. loop extrusion, in which it is integrated convergent CTCF binding sites?

Goel VY et al. Nature Genetics 2023 identified highly nested and focal interactions through region capture Micro-C, which resemble fine-scale compartmental interactions and are termed microcompartments. In the section titled "Most microcompartments are robust to loss of loop extrusion," the researchers noted that a small proportion of interactions between CTCF and cohesin-bound sites exhibited significant reductions in strength when cohesin was depleted. In contrast, the majority of microcompartmental interactions remained largely unchanged under cohesin depletion. Our findings indicate that most P-P and E-P interactions, aside from a few CTCF and cohesin-bound enhancers and promoters, are likely facilitated by a compartmentalization mechanism that differs from loop extrusion. We suggest that nested, multiway, and focal microcompartments correspond to small, discrete A-compartments that arise through a compartmentalization process, potentially influenced by factors upstream of RNA Pol II initiation, such as transcription factors, co-factors, or active chromatin states. It follows that if active chromatin regions at microcompartment anchors exhibit selective "stickiness" with one another, they will tend to co-segregate, leading to the development of nested, focal interactions. This microphase separation, driven by preferential interactions among active loci within a block copolymer, may account for the striking interaction patterns we observe.

 The authors of the paper proposed several mechanisms potentially involved in microcompartments. These mechanisms may be involved in looping with insulator function. Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently (Hsieh TS et al. *Nature Genetics* 2022). Among the identified insulator-associated DNA-binding proteins, Maz and MyoD1 form loops without CTCF (Xiao T et al. *Proc Natl Acad Sci USA* 2021 ; Ortabozkoyun H et al. *Nature genetics* 2022 ; Wang R et al. *Nature communications* 2022). I have added the following sentences on lines 571-575: Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently. I have included the following explanation on lines 582-584: Maz and MyoD1 among the identified insulator-associated DNA-binding proteins form loops without CTCF.

 As for the directionality of CTCF, if chromatin loop anchors have some structural conformation, as shown in the paper entitled "The structural basis for cohesin-CTCF-anchored loops" (Li Y et al. *Nature* 2020), directional DNA binding would occur similarly to CTCF binding sites. Moreover, cohesin complexes that interact with convergent CTCF sites, that is, the N-terminus of CTCF, might be protected from WAPL, but those that interact with divergent CTCF sites, that is, the C-terminus of CTCF, might not be protected from WAPL, which could release cohesin from chromatin and thus disrupt cohesin-mediated chromatin loops (Davidson IF et al. *Nature Reviews Molecular Cell Biology* 2021). Regarding loop extrusion, the 'loop extrusion' hypothesis is motivated by in vitro observations. The experiment in yeast, in which cohesin variants that are unable to extrude DNA loops but retain the ability to topologically entrap DNA, suggested that in vivo chromatin loops are formed independently of loop extrusion. Instead, transcription promotes loop formation and acts as an extrinsic motor that extends these loops and defines their final positions (Guerin TM et al. *EMBO Journal* 2024). I have added the following sentences on lines 543-547: Cohesin complexes that interact with convergent CTCF sites, that is, the N-terminus of CTCF, might be protected from WAPL, but those that interact with divergent CTCF sites, that is, the C-terminus of CTCF, might not be protected from WAPL, which could release cohesin from chromatin and thus disrupt cohesin-mediated chromatin loops. I have included the following sentences on lines 577-582: The 'loop extrusion' hypothesis is motivated by in vitro observations. The experiment in yeast, in which cohesin variants that are unable to extrude DNA loops but retain the ability to topologically entrap DNA, suggested that in vivo chromatin loops are formed independently of loop extrusion. Instead, transcription promotes loop formation and acts as an extrinsic motor that extends these loops and defines their final positions.

 Another model for the regulation of gene expression by insulators is the boundary-pairing (insulator-pairing) model (Bing X et al. *Elife* 2024) (Ke W et al. *Elife* 2024) (Fujioka M et al. *PLoS Genetics* 2016). Molecules bound to insulators physically pair with their partners, either head-to-head or head-to-tail, with different degrees of specificity at the termini of TADs in flies. Although the experiments do not reveal how partners find each other, the mechanism unlikely requires loop extrusion. Homologous and heterologous insulator-insulator pairing interactions are central to the architectural functions of insulators. The manner of insulator-insulator interactions is orientation-dependent. I have summarized the model on lines 559-567: Other types of chromatin regulation are also expected to be related to the structural interactions of molecules. As the boundary-pairing (insulator-pairing) model, molecules bound to insulators physically pair with their partners, either head-to-head or head-to-tail, with different degrees of specificity at the termini of TADs in flies (Fig. 7). Although the experiments do not reveal how partners find each other, the mechanism unlikely requires loop extrusion. Homologous and heterologous insulator-insulator pairing interactions are central to the architectural functions of insulators. The manner of insulator-insulator interactions is orientation-dependent.

8. Do the authors think that the identified DBPs could work in that way as well?

The boundary-pairing (insulator-pairing) model would be applied to the insulator-associated DNA-binding proteins other than CTCF and cohesin that are involved in the loop extrusion mechanism (Bing X et al. Elife 2024) (Ke W et al. Elife 2024) (Fujioka M et al. PLoS Genetics 2016).

 Liquid-liquid phase separation was shown to occur through CTCF-mediated chromatin loops and to act as an insulator (Lee, R et al. *Nucleic Acids Research* 2022). Among the identified insulator-associated DNA-binding proteins, CEBPA has been found to form hubs that colocalize with transcriptional co-activators in a native cell context, which is associated with transcriptional condensate and phase separation (Christou-Kent M et al. *Cell Reports* 2023). The proposed microcompartment mechanisms are also associated with phase separation. Thus, the same or similar mechanisms are potentially associated with the insulator function of the identified DNA-binding proteins. I have included the following information on line 554: CEBPA in the identified insulator-associated DNA-binding proteins was also reported to be involved in transcriptional condensates and phase separation.

9. Also, can the authors comment about the mechanisms those newly identified DBPs mediate contacts by active processes or equilibrium processes?

Snead WT et al. Molecular Cell 2019 mentioned that protein post-transcriptional modifications (PTMs) facilitate the control of molecular valency and strength of protein-protein interactions. O-GlcNAcylation as a PTM inhibits CTCF binding to chromatin (Tang X et al. Nature Communications 2024). I found that the identified insulator-associated DNA-binding proteins tend to form a cluster at potential insulator sites (Supplementary Fig. 2d). These proteins may interact and actively regulate chromatin interactions, transcriptional condensation, and phase separation by PTMs. I have added the following explanation on lines 584-590: Furthermore, protein post-transcriptional modifications (PTMs) facilitate control over the molecular valency and strength of protein-protein interactions. O-GlcNAcylation as a PTM inhibits CTCF binding to chromatin. We found that the identified insulator-associated DNA-binding proteins tend to form a cluster at potential insulator sites (Fig. 4f and Supplementary Fig. 3c). These proteins may interact and actively regulate chromatin interactions, transcriptional condensation, and phase separation through PTMs.

10. Can the author provide some real examples along with published structural data (e.g. the mentioned micro-C data) to show the link between protein co-presence, directional bias and contact formation?

Structural molecular model of cohesin-CTCF-anchored loops has been published by Li Y et al. Nature 2020. The structural conformation of CTCF and cohesin in the loops would be the cause of the directional bias of CTCF binding sites, which I mentioned in lines 539 - 543 as follows: These results suggest that the directional bias of DNA-binding sites of insulator-associated DBPs may be involved in insulator function and chromatin regulation through structural interactions among DBPs, other proteins, DNAs, and RNAs. For example, the N-terminal amino acids of CTCF have been shown to interact with RAD21 in chromatin loops.

 To investigate the principles underlying the architectural functions of insulator-insulator pairing interactions, two insulators, Homie and Nhomie, flanking the *Drosophila even skipped *locus were analyzed. Pairing interactions between the transgene Homie and the eve locus are directional. The head-to-head pairing between the transgene and endogenous Homie matches the pattern of activation (Fujioka M et al. *PLoS Genetics* 2016).

Reviewer #3

Major Comments:

1. Some of these TFs do not have specific direct binding to DNA (P300, Cohesin). Since the authors are using binding motifs in their analysis workflow, I would remove those from the analysis.

When a protein complex binds to DNA, one protein of the complex binds to the DNA directory, and the other proteins may not bind to DNA. However, the DNA motif sequence bound by the protein may be registered as the DNA-binding motif of all the proteins in the complex. The molecular structure of the complex of CTCF and Cohesin showed that both CTCF and Cohesin bind to DNA (Li Y et al. Nature 2020). I think there is a possibility that if the molecular structure of a protein complex becomes available, the previous recognition of the DNA-binding ability of a protein may be changed. Therefore, I searched the Pfam database for 99 insulator-associated DNA-binding proteins identified in this study. I found that 97 are registered as DNA-binding proteins and/or have a known DNA-binding domain, and EP300 and SIN3A do not directory bind to DNA, which was also checked by Google search. I have added the following explanation in line 257 to indicate direct and indirect DNA-binding proteins: Among 99 insulator-associated DBPs, EP300 and SIN3A do not directory interact with DNA, and thus 97 insulator-associated DBPs directory bind to DNA. I have updated the sentence in line 20 of the Abstract as follows: We discovered 97 directional and minor nondirectional motifs in human fibroblast cells that corresponded to 23 DBPs related to insulator function, CTCF, and/or other types of chromosomal transcriptional regulation reported in previous studies.

2. I am not sure if I understood correctly, by why do the authors consider enhancers spanning 2Mb (200 bins of 10Kb around eSNPs)? This seems wrong. Enhancers are relatively small regions (100bp to 1Kb) and only a very small subset form super enhancers.

As the reviewer mentioned, I recognize enhancers are relatively small regions. In the paper, I intended to examine further upstream and downstream of promoter regions where enhancers are found. Therefore, I have modified the sentence in lines 929 - 931 of the Fig. 2 legend as follows: Enhancer-gene regulatory interaction regions consist of 200 bins of 10 kbp between -1 Mbp and 1 Mbp region from TSS, not including promoter.

3. I think the H3K27me3 analysis was very good, but I would have liked to see also constitutive heterochromatin as well, so maybe repeat the analysis for H3K9me3.

Following the reviewer's advice, I have added the ChIP-seq data of H3K9me3 as a truck of the UCSC Genome Browser. The distribution of H3K9me3 signal was different from that of H3K27me3 in some regions. I also found the insulator-associated DNA-binding sites close to the edges of H3K9me3 regions and took some screenshots of the UCSC Genome Browser of the regions around the sites in Supplementary Fig. 3b. I have modified the following sentence on lines 974 - 976 in the legend of Fig. 4: a Distribution of histone modification marks H3K27me3 (green color) and H3K9me3 (turquoise color) and transcript levels (pink color) in upstream and downstream regions of a potential insulator site (light orange color). I have also added the following result on lines 356 - 360: The same analysis was performed using H3K9me3 marks, instead of H3K27me3 (Fig. S3b). We found that the distribution of H3K9me3 signal was different from that of H3K27me3 in some regions, and discovered the insulator-associated DNA-binding sites close to the edges of H3K9me3 regions (Fig. S3b).

4. I was not sure I understood the analysis in Figure 6. The binding site is with 500bp of the interaction site, but micro-C interactions are at best at 1Kb resolution. They say they chose the centre of the interaction site, but we don't know exactly where there is the actual interaction. Also, it is not clear what they measure. Is it the number of binding sites of a specific or multiple DBP insulator proteins at a specific distance from this midpoint that they recover in all chromatin loops? Maybe I am missing something. This analysis was not very clear.

The resolution of the Micro-C assay is considered to be 100 bp and above, as the human nucleome core particle contains 145 bp (and 193 bp with linker) of DNA. However, internucleosomal DNA is cleaved by endonuclease into fragments of multiples of 10 nucleotides (Pospelov VA et al. Nucleic Acids Research 1979). Highly nested focal interactions were observed (Goel VY et al. Nature Genetics 2023). Base pair resolution was reported using Micro Capture-C (Hua P et al. Nature 2021). Sub-kilobase (20 bp resolution) chromatin topology was reported using an MNase-based chromosome conformation capture (3C) approach (Aljahani A et al. Nature Communications 2022). On the other hand, Hi-C data was analyzed at 1 kb resolution. (Gu H et al. bioRxiv 2021). If the resolution of Micro-C interactions is at best at 1 kb, the binding sites of a DNA-binding protein will not show a peak around the center of the genomic locations of interaction edges. Each panel shows the number of binding sites of a specific DNA-binding protein at a specific distance from the midpoint of all chromatin interaction edges. I have modified and added the following sentences in lines 593-597: High-resolution chromatin interaction data from a Micro-C assay indicated that most of the predicted insulator-associated DBPs showed DNA-binding-site distribution peaks around chromatin interaction sites, suggesting that these DBPs are involved in chromatin interactions and that the chromatin interaction data has a high degree of resolution. Base pair resolution was reported using Micro Capture-C.

Minor Comments:

1. PIQ does not consider TF concentration. Other methods do that and show that TF concentration improves predictions (e.g., ____https://www.biorxiv.org/content/10.1101/2023.07.15.549134v2____or ____https://pubmed.ncbi.nlm.nih.gov/37486787____/). The authors should discuss how that would impact their results.

The directional bias of CTCF binding sites was identified by ChIA-pet interactions of CTCF binding sites. The analysis of the contribution scores of DNA-binding sites of proteins considering the binding sites of CTCF as an insulator showed the same tendency of directional bias of CTCF binding sites. In the analysis, to remove the false-positive prediction of DNA-binding sites, I used the binding sites that overlapped with a ChIP-seq peak of the DNA-binding protein. This result suggests that the DNA-binding sites of CTCF obtained by the current analysis have sufficient quality. Therefore, if the accuracy of prediction of DNA-binding sites is improved, although the number of DNA-binding sites may be different, the overall tendency of the directionality of DNA-binding sites will not change and the results of this study will not change significantly.

 As for the first reference in the reviewer's comment, chromatin interaction data from Micro-C assay does not include all chromatin interactions in a cell or tissue, because it is expensive to cover all interactions. Therefore, it would be difficult to predict all chromatin interactions based on machine learning. As for the second reference in the reviewer's comment, pioneer factors such as FOXA are known to bind to closed chromatin regions, but transcription factors and DNA-binding proteins involved in chromatin interactions and insulators generally bind to open chromatin regions. The search for the DNA-binding motifs is not required in closed chromatin regions.

2. DeepLIFT is a good approach to interpret complex structures of CNN, but is not truly explainable AI. I think the authors should acknowledge this.

In the DeepLIFT paper, the authors explain that DeepLIFT is a method for decomposing the output prediction of a neural network on a specific input by backpropagating the contributions of all neurons in the network to every feature of the input (Shrikumar A et al. ICML 2017). DeepLIFT compares the activation of each neuron to its 'reference activation' and assigns contribution scores according to the difference. DeepLIFT calculates a metric to measure the difference between an input and the reference of the input.

 Truly explainable AI would be able to find cause and reason, and to make choices and decisions like humans. DeepLIFT does not perform causal inferences. I did not use the term "Explainable AI" in our manuscript, but I briefly explained it in Discussion. I have added the following explanation in lines 623-628: AI (Artificial Intelligence) is considered as a black box, since the reason and cause of prediction are difficult to know. To solve this issue, tools and methods have been developed to know the reason and cause. These technologies are called Explainable AI. DeepLIFT is considered to be a tool for Explainable AI. However, DeepLIFT does not answer the reason and cause for a prediction. It calculates scores representing the contribution of the input data to the prediction.

 Furthermore, to improve the readability of the manuscript, I have included the following explanation in lines 159-165: we computed DeepLIFT scores of the input data (i.e., each binding site of the ChIP-seq data of DNA-binding proteins) in the deep leaning analysis on gene expression levels. DeepLIFT compares the importance of each input for predicting gene expression levels to its 'reference or background level' and assigns contribution scores according to the difference. DeepLIFT calculates a metric to measure the difference between an input and the reference of the input.

Author Response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review):

(1) I think the article is a little too immature in its current form. I'd recommend that the authors work on their writing. For example, the objectives of the article are not completely clear to me after reading the manuscript, composed of parts where the authors seem to focus on SGCs, and others where they study "engram" neurons without differentiating the neuronal type (Figure 5). The next version of the manuscript should clearly establish the objectives and sub-aims.

We now provide clarification for focusing on the labeling status versus the cell types in figure 5. Since figure 5 focuses on inputs to labeled pairs versus Labeledunlabeled pairs the pairs include mixed groups with GCs and SGCs. Since the question pertains to inputs rather than cell types, we did not specifically distinguish the cell types. This is now explained in the text on page 15:  “Note that since the intent was to determine the input correlation depending on labeling status of the cell pairs rather than based on cell type, we do not explicitly consider whether analyzed cell pairs included GCs or SGCs.”

(2) In addition, some results are not entirely novel (e.g., the disproportionate recruitment as well as the distinctive physiological properties of SGCs), and/or based on correlations that do not fully support the conclusions of the article. In addition to re-writing, I believe that the article would benefit from being enriched with further analyses or even additional experiments before being resubmitted in a more definitive form.

We now indicate the data comparing labeled versus unlabeled SGCs is novel. Moreover, we also highlight that (1) recruitment of SGCs has not been previously examined in Barnes Maze or Enriched Environment, (2) that our unbiased morphological analysis of SGC recruitment is more robust than subsampling of recorded neurons in prior studies and (3) that our data show that prior may have overestimated SGC recruitment to engrams. Thus, the data characterized as “not novel” are essential for appropriate analysis of behaviorally tagged neurons which is the thrust of our study.  

Reviewer #2 (Public Review):

(1) The authors conclude that SGCs are disproportionately recruited into cfos assemblies during the enriched environment and Barnes maze task given that their classifier identifies about 30% of labelled cells as SGCs in both cases and that another study using a different method (Save et al., 2019) identified less than 5% of an unbiased sample of granule cells as SGCs. To make matters worse, the classifier deployed here was itself established on a biased sample of GCs patched in the molecular layer and granule cell layer, respectively, at even numbers (Gupta et al., 2020). The first thing the authors would need to show to make the claim that SGCs are disproportionately recruited into memory ensembles is that the fraction of GCs identified as SGCs with their own classifier is significantly lower than 30% using their own method on a random sample of GCs (e.g. through sparse viral labelling). As the authors correctly state in their discussion, morphological samples from patch-clamp studies are problematic for this purpose because of inherent technical issues (i.e. easier access to scattered GCs in the molecular layer).

We now clarify, on page 9, that a trained investigator classified cell types based on predefined morphological criteria.  No automated classifiers were used to assign cell types in the current study.

(2) The authors claim that recurrent excitation from SGCs onto GCs or other SGCs is irrelevant because they did not find any connections in 32 simultaneous recordings (plus 63 in the next experiment). Without a demonstration that other connections from SGCs (e.g. onto mossy cells or interneurons) are preserved in their preparation and if so at what rates, it is unclear whether this experiment is indicative of the underlying biology or the quality of the preparation. The argument that spontaneous EPSCs are observed is not very convincing as these could equally well arise from severed axons (in fact we would expect that the vast majority of inputs are not from local excitatory cells). The argument on line 418 that SGCs have compact axons isn't particularly convincing either given that the morphologies from which they were derived were also obtained in slice preparations and would be subject to the same likelihood of severing the axon. Finally, even in paired slice recordings from CA3 pyramidal cells the experimentally detected connectivity rates are only around 1% (Guzman et al., 2016). The authors would need to record from a lot more than 32 pairs (and show convincing positive controls regarding other connections) to make the claim that connectivity is too low to be relevant.

We have conducted additional control experiments (detailed in response to Editorial comment #3), in which we replicated the results of Stefanelli et al (2016) identifying that optogenetic activation of a focal cohort of ChR2 expressing granule cells leads to robust feedback inhibition of adjacent granule cells. These control experiments demonstrate that the slice system supports the feedback inhibitory circuit which requires GC/SGC to hilar neuron synapses.

(3) Another troubling sign is the fact that optogenetic GC stimulation rarely ever evokes feedback inhibition onto other cells which contrasts with both other in vitro (e.g. Braganza et al., 2020) and in vivo studies (Stefanelli et al., 2016) studies. Without a convincing demonstration that monosynaptic connections between SGCs/GCs and interneurons in both directions is preserved at least at the rates previously described in other slice studies (e.g. Geiger et al., 1997, Neuron, Hainmueller et al., 2014, PNAS, Savanthrapadian et al., 2014, J. Neurosci), the notion that this setting could be closer to naturalistic memory processing than the in vivo experiments in Stefanelli et al. (e.g. lines 443-444) strikes me as odd. In any case, the discussion should clearly state that compromised connectivity in the slice preparation is likely a significant confound when comparing these results.

We have conducted additional control experiments (detailed in response to Editorial comment #3), in which we replicated the results of Stefanelli et al identifying that optogenetic activation of a focal cohort of ChR2 expressing granule cells leads to robust feedback inhibition of adjacent granule cells. These control experiments demonstrate that the slice system in our studies support the feedback inhibitory circuit detailed in prior studies. We also clarify that Stefanelli study labeled random neurons and did not examine natural behavioral engrams and  discuss (on page 20) the correspondence/consistency of our results with that of Braganza et al 2020.

(4) Probably the most convincing finding in this study is the higher zero-time lag correlation of spontaneous EPSCs in labelled vs. unlabeled pairs. Unfortunately, the fact that the authors use spontaneous EPSCs to begin with, which likely represent a mixture of spontaneous release from severed axons, minis, and coordinated discharge from intact axon segments or entire neurons, makes it very hard to determine the meaning and relevance of this finding. At the bare minimum, the authors need to show if and how strongly differences in baseline spontaneous EPSC rates between different cells and slices are contributing to this phenomenon. I would encourage the authors to use low-intensity extracellular stimulation at multiple foci to determine whether labelled pairs really share higher numbers of input from common presynaptic axons or cells compared to unlabeled pairs as they claim. I would also suggest the authors use conventional Cross correlograms (CCG; see e.g. English et al., 2017, Neuron; Senzai and Buzsaki, 2017, Neuron) instead of their somewhat convoluted interval-selective correlation analysis to illustrate codependencies between the event time series. The references above also illustrate a more robust approach to determining whether peaks in the CCGs exceed chance levels.

We have included data on sEPSC frequency in the recorded cell pairs (Supplemental Fig 4) and have also conducted additional experiments and present data demonstrating that labeled cell show higher sEPSC frequency and amplitude than corresponding unlabeled cells in both cell types (new Fig 5).  We also include data from new  experiments to show that over 50% of the sEPSCs represent action potential driven events (Supplemental fig 3). 

We thank the reviewer for the suggestion to explore alternative methods of analyses including CCGs to further strengthen our findings. We have now conducted CCGs on the same data set and report that “The dynamics of the cross-correlograms generated from our data sets using previously established methods to evaluate monosynaptic connectivity (Bartho et al., 2004; Senzai and Buzsaki, 2017) parallelled that of the CCP plots (Supplemental Fig. 6) illustrating that the methods similarly capture co-dependencies between event time series. We note, here, that while the CCG and CCP are qualitatively similar, the magnitude of the peaks were different, due to the sparseness of synaptic events. 

(5) Finally, one of the biggest caveats of the study is that the ensemble is labelled a full week before the slice experiment and thereby represents a latent state of a memory rather than encoding consolidation, or recall processes. The authors acknowledge that in the discussion but they should also be mindful of this when discussing other (especially in vivo) studies and comparing their results to these. For instance, Pignatelli et al 2018 show drastic changes in GC engram activity and features driven by behavioral memory recall, so the results of the current study may be very different if slices were cut immediately after memory acquisition (if that was possible with a different labelling strategy), or if animals were re-exposed to the enriched environment right before sacrificing the animal.

As noted by the reviewer, we fully acknowledge and are cognizant of the concern that slices prepared a week after labeling may not reflect ongoing encoding. Although our data show that labeled cells are reactivated in higher proportion during recall, we have discussed this caveat and will include alternative experimental strategies in the discussion.

Reviewer #3 (Public Review):

(1) Engram cells are (i) activated by a learning experience, (ii) physically or chemically modified by the learning experience, and (iii) reactivated by subsequent presentation of the stimuli present at the learning experience (or some portion thereof), resulting in memory retrieval. The authors show that exposure to Barnes Maze and the enriched environment-activated semilunar granule cells and granule cells preferentially in the superior blade of the dentate gyrus, and a significant fraction were reactivated on re-exposure. However, physical or chemical modification by experience was not tested. Experience modifies engram cells, and a common modification is the Hebbian, i.e., potentiation of excitatory synapses. The authors recorded EPSCs from labeled and unlabeled GCs and SGCs. Was there a difference in the amplitude or frequency of EPSCs recorded from labeled and unlabeled cells?

We have included data on sEPSC frequency in the recorded cell pairs (Supplemental Fig 4) and have also conducted additional experiments and report and present data demonstrating that labeled cell show higher sEPSC frequency and amplitude than corresponding unlabeled cells in both cell types (new Fig 5).  We also include data from new  experiments to show that over 50% of the sEPSCs represent action potential driven events (Supplemental fig 3).

(2) The authors studied five sequential sections, each 250 μm apart across the septotemporal axis, which were immunostained for c-Fos and analyzed for quantification. Is this an adequate sample? Also, it would help to report the dorso-ventral gradient since more engram cells are in the dorsal hippocampus. Slices shown in the figures appear to be from the dorsal hippocampus. 

We thank the reviewer for the comment. We analyzed sections along the dorsoventral gradient. As explained in the methods, there is considerable animal to animal variability in the number of labeled cells which was why we had to use matched littermate pairs in our experiments This variability could render it difficult to tease apart dorsoventral differences. 

(3) The authors investigated the role of surround inhibition in establishing memory engram SGCs and GCs. Surprisingly, they found no evidence of lateral inhibition in the slice preparation. Interneurons, e.g., PV interneurons, have large axonal arbors that may be cut during slicing.

Similarly, the authors point out that some excitatory connections may be lost in slices. This is a limitation of slice electrophysiology.

We have conducted additional control experiments (detailed in response to Editorial comment #3), in which we replicated the results of Stefanelli et al identifying that optogenetic activation of a focal cohort of ChR2 expressing granule cells leads to robust feedback inhibition of adjacent granule cells. These control experiments demonstrate that the slice system supports the feedback inhibitory circuit detailed in prior studies. 

We now discuss (page 21) that “the possibility that slice recordings lead to underestimation of feedback dendritic inhibition cannot be ruled out.”

Reviewer #1 (Recommendations for the authors):

(1) I struggle to understand the added value of the Barnes Maze data (Figures 1 and S1), since the authors then focus on the EE for practical reasons. In particular, the analysis of mouse performance (presented in supplemental Figure 1) does not seem traditional to me. For example, instead of the 3 classical exploration strategies (i.e., random, serial, direct), the authors describe 6, and assign each of these strategies a score based on vague criteria (why are "long corrected" and "focused research" both assigned a score of 0.5?). Unless I'm mistaken, no other classic parameters are described (e.g., success rate, latency, number of errors). If the authors decide to keep the BM results, I recommend better justifying its existence and adding more details, including in the method section. Otherwise, perhaps they should consider withdrawing it. Even if we had to use two different behavioral contexts, wouldn't it have made sense to use, in addition to the EE, the fear conditioning test, which is widely used in the study of engrams? Under these conditions (Stefanelli et al., 2016), the number of cells recruited after fear conditioning seems sufficient to reproduce the analyses presented in Figures 2-5 and determine whether or not lateral inhibition is dependent on the type of context (Stefanelli and colleagues suggest significant strong lateral inhibition during fear conditioning, whereas the data from Dovek and colleagues suggest quite the opposite after exposure to EE).

The Barnes Maze data was included to evaluate the DG ensemble activation during a dentate dependent non-fear based behavioral task. This is now introduced and explained in the results. We have now included plots of the primary latency and number of errors in finding the escape hole to confirm the improvement over time (Supplemental Fig. 1). We specifically used the BUNS analysis to evaluate the use of spatial strategy and show that by day 6, day of tamoxifen induction, the mice are using a spatial strategy for navigation. Our approach to evaluate exploration strategy is based on criteria published in Illouz et al 2016. This is now detailed in the methods on page 25. We hope that  the inclusion of the supplemental data and revisions to methods and results address the concerns regarding Barnes Maze experiments. 

Regarding Stefanelli et al., 2016, please note that the study adopted random labeling of neurons using a CaMKII promotor driven reporter expression which they activated during spatial exploration of fear conditioning behaviors. As such labeled neurons in the Stefanelli study were NOT behaviorally driven, rather they were optically activated. This is now clarified in the text. The main drive for our study was to evaluate behaviorally tagged neurons which is novel, distinct from the Stefanelli study, and, we would argue, more behaviorally realistic and relevant.

Additionally, the lateral inhibition observed in Stafanelli et al was in response to activation of GCs labeled by virally mediate CAMKII-driven ChR2 expression. Using a similar labeling approach, new control data presented in Supplemental fig. 3 show that we are fully able to replicate the lateral inhibition observed by Stefanalli et al. These control experiments further suggest that the sparse and distributed GC/SGC ensembles activated during non-aversive behavioral tasks may not be sufficient to elicit robust lateral inhibition as has been observed when a random population of adjacent neurons are activated. Our findings are also consistent with observations by Barganza et al., 2020. This is now Discussed on page 21.

(2) The authors recorded sEPSCs received by recruited and non-recruited GCs and SGCs after EE exposure. However, it appears that they studied them very little, apart (from a temporal correlation analysis (Figure 5). Yet it would be interesting to determine whether or not the four neuronal populations possess different synaptic properties. 

What is the frequency and amplitude of sEPSCs in GCs and SGCs recruited or not after EE exposure? Similarly, can the author record the sIPSCs received by dentate gyrus engram and non-engram GCs and SGCs? If so, what is their frequency and amplitude?

As suggested by the editorial comment #2, we how include data on the frequency and amplitude of the sEPSCs in GCs and SGCs used in our analysis of figure 5. Given the low numbers of unlabeled SGCs and labeled GCs in our paired recordings (Supplemental Fig. 5), we choose not to use this data set for analysis of cell-type and labeling based differences in EPSC parameters. However, we have previously reported that sIPSC frequency is higher in SGCs than in GCs. Additionally, we have identified that sEPSC frequency in SGCs is higher than in GC (Dovek et al, in preprint, DOI: 10.1101/2025.03.14.643192).  

To specifically address reviewer concerns, we have conducted new recorded EPSCs in a cohort of labeled and unlabeled GCs and SGCs and present data demonstrating that labeled cell show higher sEPSC frequency and amplitude than corresponding unlabeled cells in both cell types (new Fig 5). These experiments were conducted in TRAP2-tdT labeled cells which were not stable in cesium based recordings. As such we, we deferred the IPSC analysis for later and restricted analysis to sEPSCs for this study. 

(3) Previous data showed that dentate gyrus neurons that are recruited or not in a given context could exhibit distinct morphological characteristics (Pléau et al. 2021) and biochemical content (Penk expression, Erwin et al., 2020). In order to enrich the electrophysiological data presented in Figure 2, could the authors take advantage of the biocytin filling to perform a morphological and biochemical comparison of the different neuronal types (i.e., GCs and SGCs recruited or not after EE)?

Thank you for this suggestion. Unfortunately, detailed morphometry and biochemical analysis on labeled and unlabeled neurons was not conducted as part of this study as our focus was on circuit differences. In our experience, unless the sections are imaged soon after staining, the sections are suboptimal for detailed morphological reconstruction and analysis. Our ongoing studies suggest that PENK is an activity marker and not a selective marker for SGCs and we are undertaking transcriptomic analysis to identify molecular differences between GCs and SGCs. We respectfully submit that these experiments are outside the scope of this study.

(4) Figures 3 and 4 show only schematic diagrams and representative data. No quantification is shown. Instead of pie charts showing the identity of each pair (which I find unnecessary), I'll use pie charts representing the % of each pair in which an excitatory or inhibitory drive was recorded (with the corresponding n).

Please note that we did not observe evoked synaptic potentials in any except one pair precluding the possibility of quantification. However, we submit that it is important for the readers to have information on the number of pairs and the types of pre-post synaptic pairs in which the connections were tested.

(5) Figure 3: Given that GCs form very few recurrences in non-pathological conditions, it hardly surprises me that they form few or no local glutamatergic connections. In contrast, this result surprises me more for SGCs, whose axons form collaterals in the dentate gyrus granular and molecular layers (Williams et al., 2007; Save et al., 2019). To control the reliability of their conditions, could the authors check whether SGCs do indeed form connections with hilar mossy cells, as has been reported in the past? To test whether this lack of interconnectivity is specific to neurons belonging to the same engram (or not), could the authors test whether or not the stimulation of labeled GCs/SGCs (via membrane depolarization or even optogenetics) generates EPSCs in unlabeled GCs?

As suggested by the reviewer, we have examined whether widefield optical activation of all labeled neurons including GCs and SGCs lead to EPSCs in unlabeled GCs (63 cells tested). However, we did not observe eEPSCs. This data is presented on page 13, (Fig 4F) in the results and discussed on page 20. Since the wide field stimulation should activate terminals and lead to release even if the axon is severed, our data suggest the glutamatergic drive from SGC to GC may be limited.

As noted above, we have demonstrated the presence of lateral inhibition consistent with data in Stefanelli et al in our new supplementary figure 3. We have also shown that sustained SGC firing upon perforant path stimulations is associated with sustained firing in hilar interneurons (Afrasiabi et al., 2022) indicating presence of the SGC to hilar connectivity in our slice preparation. Therefore, we choose not to undertake challenging 2P guided paired recording of SGCs and mossy cells adjacent to SGC axon terminals reported in Williams et al 2007 to replicate the 9%  SGC to MC synaptic connections. These 2P guided slice physiology studies are outside the technical scope of our study.

(6) Figure 4: The results are relatively in contradiction with the strong lateral inhibition reported in the past (Stefanelli et al., 2016), but the experimental conditions are different in the two studies. Stimulation of a single labeled GC or SGC may not be sufficient to activate an inhibitory neuron, and for the latter to inhibit an unlabeled GC or SGC. Is it possible to measure the sIPSCs received by unlabelled neurons during optogenetic stimulation of all labelled neurons? Could the authors verify whether under their experimental conditions GCs and SGCs do indeed form connections with interneurons, as reported before? Finally, Stefanelli and colleagues (2016) suggest that lateral inhibition is provided by dendrites- targeting somatostatin interneurons. If the authors are recording in the soma, could they underestimate more distal inhibitory inputs? If so, could they record the dendrites of unlabeled neurons?

Our new control data (Supplementary Fig. 3) using an AAV mediated CAMKII promotor driven random expression of ChR2 on GCs, similar to Stefanelli et al (2016) demonstrates our ability replicate the lateral inhibition observed by Stefanalli et al. (2016). Thus, our findings more accurately represent lateral inhibition supported by a sparse behaviorally labeled cohort than findings of Stefanelli et al based on randomly labeled neurons. This is now discussed on page 22-23. We respectfully submit that dendritic recordings are outside the scope of the current study.

We also discuss the possibility that somatic recordings may under sample dendritic inhibitory inputs on page 23 “the possibility that slice recordings lead to underestimation of feedback dendritic inhibition cannot be ruled out.”

(7) Figure 5: For ease of reading, I would substantially simplify the Results section related to Figure 5, keeping only the main general points of the analysis and the results themselves. The details of the analysis strategy, and the justification for the choices made, are better placed in the Method section (I advise against "data not shown").

We thank the reviewer for the suggestion to improve accessibility of the results and have moved text related to justification of strategy and controls to the methods. We have also removed references to data not shown.

(8) Figure 5: why do the authors no longer discriminate between GCs and SGCs?

Since figure 5 focuses on inputs to labeled pairs versus labeled-unlabeled pairs the pairs include mixed groups with GCs and SGCs. Since the question pertains to inputs rather than cell types, we did not specifically distinguish the cell types. This is now explained in the text on page 15.

(9) Figure 5: I would like to know more about the temporally connected inputs and their implication in context-dependent recruitment of dentate gyrus neurons. What could be the origin of the shared input received by the neurons recruited after EE exposure? For example, do labeled neurons receive more (temporally correlated or not) inputs from the entorhinal cortex (or any other upstream brain region) than unlabeled neurons? Is there any way (e.g., PP stimulation or any kind of manipulation) to test the causal relationship between temporally correlated input and the context-dependent recruitment of a given neuron?

We appreciate the reviewer’s comments on the need to examine the source and nature of the correlated inputs to behaviorally labeled neurons. However, the suggested experiments are nontrivial as artificial stimulation of afferent fibers is unlikely to be selective for labeled and unlabeled cells. Given the complexities in design, implementation and interpretation of these experiments we respectfully submit that these are outside the scope of the current study.

Reviewer #2 (Recommendations for the authors):

There are a few minor issues limiting the extent of interpretations of the data:

(1) Only about 7% of the 'engram' cells are re-activated one week after exposure (line 147), it is unclear how meaningful this assembly is given the high number of cells that may either be labelled unrelated to the EE or no longer be part of the memory-related ensemble.

We now discuss (page 22-23) that the % labeling is consistent with what has been observed in the DG 1 week after fear conditioning (DeNardo et al., 2019) and discuss the caveat that all labeled cells may not represent an engram.  

(2) Line 215: The wording '32 pairwise connections examined' suggests that there actually were synaptic connections, would recommend altering the wording to 'simultaneously recorded cells examined' to avoid confusion.

Revised as suggested

Reviewer #2 (Public review):

In this valuable manuscript, Lin et al attempt to examine the role of long non coding RNAs (lncRNAs) in human evolution, through a set of population genetics and functional genomics analyses that leverage existing datasets and tools. Although the methods are incomplete and at times inadequate, the results nonetheless point towards a possible contribution of long non coding RNAs to shaping humans, and suggest clear directions for future, more rigorous study.

Comments on revisions:

I thank the authors for their revision and changes in response to previous rounds of comments. As it had been nearly two years since I last saw the manuscript, I reread the full text to familiarise myself again with the findings presented. While I appreciate the changes made and think they have strengthened the manuscript, I still find parts of it a bit too speculative or hyperbolic. In particular, I think claims of evolutionary acceleration and adaptation require more careful integration with existing human/chimpanzee genetics and functional genomics literature. For example:

Line 155: "About 5% of genes have significant sequence differences in humans and chimpanzees," This statement needs a citation, and a definition of what is meant by 'significant', especially as multiple lines below instead mention how it's not clear how many differences matter, or which of them, etc.

line 187: "Notably, 97.81% of the 105141 strong DBSs have counterparts in chimpanzees, suggesting that these DBSs are similar to HARs in evolution and have undergone human-specific evolution." I do not see any support for the inference here. Identifying HARs and acceleration relies on a far more thorough methodology than what's being presented here. Even generously, pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee.

line 210: "Based on a recent study that identified 5,984 genes differentially expressed between human-only and chimpanzee-only iPSC lines (Song et al., 2021), we estimated that the top 20% (4248) genes in chimpanzees may well characterize the human-chimpanzee differences" I do not agree with the rationale for this claim, and do not agree that it supports the cutoff of 0.034 used below. I also find that my previous concerns with the very disparate numbers of results across the three archaics have not been suitably addressed.

I also think that there is still too much of a tendency to assume that adaptive evolutionary change is the only driving force behind the observed results in the results. As I've stated before, I do not doubt that lncRNAs contribute in some way to evolutionary divergence between these species, as do other gene regulatory mechanisms; the manuscript leans down on it being the sole, or primary force, however, and that requires much stronger supporting evidence. Examples include, but are not limited to:

line 230: "These results reveal when and how HS lncRNA-mediated epigenetic regulation influences human evolution." This statement is too speculative.

Line 268: "yet the overall results agree well with features of human evolution." What does this mean? This section is too short and unclear.

Line 325: "and form 198876 HS lncRNA-DBS pairs with target transcripts in all tissues." This has not been shown in this paper - sequence based analyses simply identify the *potential* to form pairs.

Line 423: "Our analyses of these lncRNAs, DBSs, and target genes, including their evolution and interaction, indicate that HS lncRNAs have greatly promoted human evolution by distinctly rewiring gene expression." I do not agree that this conclusion is supported by the findings presented - this would require significant additional evidence in the form of orthogonal datasets.

I also return briefly to some of my comments before, in particular on the confounding effects of gene length and transcript/isoform number. In their rebuttal the authors argued that there was no need to control for this, but this does in fact matter. A gene with 10 transcripts that differ in the 5' end has 10 times as many chances of having a DBS than a gene with only 1 transcript, or a gene with 10 transcripts but a single annotated TSS. When the analyses are then performed at the gene level, without taking into account the number of transcripts, this could introduce a bias towards genes with more annotated isoforms. Similarly, line 246 focuses on genes with "SNP numbers in CEU, CHB, YRI are 5 times larger than the average." Is this controlled for length of the DBS? All else being equal a longer DBS will have more SNPs than a shorter one. It is therefore not surprising that the same genes that were highlighted above as having 'strong' DBS, where strength is impacted by length, show up here too.

Author Response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review):

Summary

While DNA sequence divergence, differential expression, and differential methylation analysis have been conducted between humans and the great apes to study changes that "make us human", the role of lncRNAs and their impact on the human genome and biology has not been fully explored. In this study, the authors computationally predict HSlncRNAs as well as their DNA Binding sites using a method they have developed previously and then examine these predicted regions with different types of enrichment analyses. Broadly, the analysis is straightforward and after identifying these regions/HSlncRNAs the authors examined their effects using different external datasets.

I no longer have any concerns about the manuscript as the authors have addressed my comments in the first round of review.

We thank the reviewer for the valuable comments, which have helped us improve the manuscript.

Reviewer #2 (Public Review):

Lin et al attempt to examine the role of lncRNAs in human evolution in this manuscript. They apply a suite of population genetics and functional genomics analyses that leverage existing data sets and public tools, some of which were previously built by the authors, who clearly have experience with lncRNA binding prediction. However, I worry that there is a lack of suitable methods and/or relevant controls at many points and that the interpretation is too quick to infer selection. While I don't doubt that lncRNAs contribute to the evolution of modern humans, and certainly agree that this is a question worth asking, I think this paper would benefit from a more rigorous approach to tackling it.

I thank the authors for their revisions to the manuscript; however, I find that the bulk of my comments have not been addressed to my satisfaction. As such, I am afraid I cannot say much more than what I said last time, emphasising some of my concerns with regards to the robustness of some of the analyses presented. I appreciate the new data generated to address some questions, but think it could be better incorporated into the text - not in the discussion, but in the results.

We thank the reviewer for the careful reading and valuable comments. In this round of revision, we address the two main concerns: (1) there is a lack of suitable methods and/or relevant controls at many points, and (2) the interpretation is too quick to infer selection. Based on these comments, we have carefully revised all sections of the manuscript, including the Introduction, Results, Discussion, and Materials and Methods.

In addition, we have performed two new analyses. Based on the two analyses, we have added one figure and two sections to Results, two sections to Materials and Methods, one figure to Supplementary Notes, and two tables to Supplementary Tables. These results were obtained using new methods and provided more support to the main conclusion.

To be more responsible, we re-look into the comments made in the first round and respond to them further. The following are point-to-point responses to comments.

Since many of the details in the Responses-To-Comments are available in published papers and eLife publishes Responses-To-Comments, we do not greatly revise supplementary notes to avoid ostensibly repeating published materials.

“lack of suitable methods and/or relevant controls”.

We carefully chose the methods, thresholds, and controls in the study; now, we provide clearer descriptions and explanations.

(1) We have expanded the last paragraph in Introduction to briefly introduce the methods, thresholds, and controls.

(2) In many places in Results and Materials and Methods, revisions are made to describe and justify methods, thresholds, and controls.

(3) Some methods, thresholds, and controls have good consensus, such as FDR and genome-wide background, but others may not, such as the number of genes that greatly differ between humans and chimpanzees. Now, we describe our reasons for the latter situation. For example, we explain that “About 5% of genes have significant sequence differences in humans and chimpanzees, but more show expression differences due to regulatory sequences. We sorted target genes by their DBS affinity and, to be prudential, chose the top 2000 genes (DBS length>252 bp and binding affinity>151) and bottom 2000 genes (DBS length<60 bp but binding affinity>36) to conduct over-representation analysis”.

(4) We also carefully choose proper words to make descriptions more accurate.

Responses to the suggestion “new data generated could be better incorporated into the text”.

(1) We think that this sentence “The occurrence of HS lncRNAs and their DBSs may have three situations – (a) HS lncRNAs preceded their DBSs, (b) HS lncRNAs and their DBSs co-occurred, (c) HS lncRNAs succeeded their DBSs. Our results support the third situation and the rewiring hypothesis”, previously in Discussion, should be better in section 2.3. We have revised it and moved it into the second paragraph of section 2.3.

(2) Our two new analyses generated new data, and we describe them in Results.

(3) It is possible to move more materials from Supplementary Notes to the main text, but it is probably unnecessary because the main text currently has eight sub-sections, two tables, and four figures.

Responses to the comment “the interpretation is too quick to infer selection”.

(1) When using XP-CLR, iSAFE, Tajima's D, Fay-Wu's H, the fixation index (Fst), and linkage disequilibrium (LD) to detect selection signals, we used the widely adopted parameters and thresholds but did not mention this clearly in the original manuscript. Now, in the first sentence of the second paragraph of section 2.4, we add the phrase “with widely-used parameters and thresholds” (more details are available in section 4.7 and Supplementary Notes).

(2) It is not the first time we used these tests. Actually, we used these tests in two other studies (Tang et al. Uncovering the extensive trade-off between adaptive evolution and disease susceptibility. Cell Rep. 2022; Tang et al. PopTradeOff: A database for exploring population-specificity of adaptive evolution, disease susceptibility, and drug responsiveness. Comput Struct Biotechnol J. 2023). In this manuscript, section 2.5 and section 4.12 describe how we use these tests to detect signals and infer selection. We also cite the above two published papers from which the reader can obtain more details.

(3) Also, in section 2.4, we stress that “Signals in considerable DBSs were detected by multiple tests, indicating the reliability of the analysis”.

To further respond to the comments of “lack of suitable methods” and “this paper would benefit from a more rigorous approach to tackling it”, we have performed two new analyses. The results of the new analyses agree well with previous results and provide new support for the main conclusion. The result of section 2.5 is novel and interesting.

We write in Discussion “Two questions are how mouse-specific lncRNAs specifically rewire gene expression in mice and how human- and mouse-specific rewiring influences the cross-species transcriptional differences”. To investigate whether the rewiring of gene expression by HS lncRNA in humans is accidental in evolution, we have made further genomic and transcriptomic analyses (Lin et al. Intrinsically linked lineage-specificity of transposable elements and lncRNAs reshapes transcriptional regulation species- and tissue-specifically. doi: https://doi.org/10.1101/2024.03.04.583292). To verify the obtained conclusions, we analyzed the spermatogenesis data from multiple species and obtained supporting evidence (not published).

I note some specific points that I think would benefit from more rigorous approaches, and suggest possible ways forward for these.

Much of this work is focused on comparing DNA binding domains in human-unique long-noncoding RNAs and DNA binding sites across the promoters of genes in the human genome, and I think the authors can afford to be a bit more methodical/selective in their processing and filtering steps here. The article begins by searching for orthologues of human lncRNAs to arrive at a set of 66 human-specific lncRNAs, which are then characterised further through the rest of the manuscript. Line 99 describes a binding affinity metric used to separate strong DBS from weak DBS; the methods (line 432) describe this as being the product of the DBS or lncRNA length times the average Identity of the underlying TTSs. This multiplication, in fact, undoes the standardising value of averaging and introduces a clear relationship between the length of a region being tested and its overall score, which in turn is likely to bias all downstream inference, since a long lncRNA with poor average affinity can end up with a higher score than a short one with higher average affinity, and it's not quite clear to me what the biological interpretation of that should be. Why was this metric defined in this way?

(1) Using RNA:DNA base-pairing rules, other DBS prediction programs return just DBSs with lengths. Using RNA:DNA base-pairing rules and a variant of Smith-Waterman local alignment, LongTarget returns DBSs with lengths and identity values together with DBDs (local alignment makes DBDs and DBSs predicted simultaneously). Thus, instead of measuring lncRNA/DNA binding based on DBS length, we measure lncRNA/DNA binding based on both DBS length and DBD/DBS identity (simply called identity, which is the percentage of paired nucleotides in the RNA and DNA sequences). This allows us to define “binding affinity”. One may think that binding affinity is a more complex function of length and identity. But, according to in vitro studies (see the review Abu Almakarem et al. 2012 and citations therein, and see He et al. 2015 and citations therein), the strength of a triplex is determined by all paired nucleotides (i.e., triplet). Thus, binding affinity=length * identity is biologically reasonable.

(2) Further, different from predicting DBS upon individual base-pairing rules such as AT-G and CG-C, LongTarget integrates base-pairing rules into rulesets, each covering A, T, C, and G (see the two figures below, which are from He et al 2015). This makes every nucleotide in the RNA and DNA sequences comparable and allows the computation of identity.

(3) On whether LongTarget may predict unreasonably long DBSs. Three technical features of LongTarget make this highly unlikely (and more unlikely than other programs). The three features are (a) local alignment, (b) gap penalty, and (c) TT penalty (He et al. 2015).

(4) Some researchers may think that a higher identity threshold (e.g., 0.8 or even higher) makes the predicted DBSs more reliable. This is not true. To explore plausible identity values, we analyzed the distribution of Kcnq1ot1’s DBSs in the large Kcnq1 imprinting region (which contains many known imprinted genes). We found that a high threshold for identity (e.g., 0.8) will make DBSs in many known imprinted genes fail to be predicted. Upon our analysis of many lncRNAs and upon early in vitro experiments, plausible identity values range from 0.4 to 0.8.

(5) Is it necessary or advisable to define an identity threshold? Since identity values from 0.4 to 0.8 are plausible and identity is a property of a DBS but does not reflect the strength of the whole triplex, it is more reasonable to define a threshold for binding affinity to control predicted DBSs. As explained above, binding affinity = length*identity is a reasonable measure of the strength of a triplex. The default threshold is 60, and given an identity of 0.6 in many triplexes, a DBS with affinity=60 is about 100 bp. Compared with TF binding sites (TFBS), 100 bp is quite long. As we explain in the main text, “taking a DBS of 147 bp as an example, it is extremely unlikely to be generated by chance (p < 8.2e-19 to 1.5e-48)”.

(6) How to validate predicted DBSs? Validation faces these issues. (a) DBDs are predicted on the genome level, but target transcripts are expressed in different tissues and cells. So, no single transcriptomic dataset can validate all predicted DBSs of a lncRNA. No matter using what techniques and what cells, only a small portion of predicted DBSs can be experimentally captured (validated). (b) The resolution of current experimental techniques is limited; thus, experimentally identified DBSs (i.e., “peaks”) are much longer than computationally predicted DBSs. (c) Experimental results contain false positives and false negatives. So, validation (or performance evaluation) should also consider the ROC curves (Wen et al. 2022).

(7) As explained above, a long DBS may have a lower binding affinity than a short DBS. A biological interpretation is that the long DBS may accumulate mutations that decrease its binding ability gradually.

There is also a strong assumption that identified sites will always be bound (line 100), which I disagree is well-supported by additional evidence (lines 109-125). The authors show that predicted NEAT1 and MALAT1 DBS overlap experimentally validated sites for NEAT1, MALAT1, and MEG3, but this is not done systematically, or genome-wide, so it's hard to know if the examples shown are representative, or a best-case scenario.

(1) We did not make this assumption. Apparently, binding depends on multiple factors, including co-expression of genes and specific cellular context.

(2) On the second issue, “this is not done systematically, or genome-wide”. We did genome-wide but did not show all results (supplementary fig 2 shows three genomic regions, which are impressively good). In Wen et al. 2022, we describe the overall results.

It's also not quite clear how overlapping promoters or TSS are treated - are these collapsed into a single instance when calculating genome-wide significance? If, eg, a gene has five isoforms, and these differ in the 3' UTR but their promoter region contains a DBS, is this counted five times, or one? Since the interaction between the lncRNA and the DBS happens at the DNA level, it seems like not correcting for this uneven distribution of transcripts is likely to skew results, especially when testing against genome-wide distributions, eg in the results presented in sections 5 and 6. I do not think that comparing genes and transcripts putatively bound by the 40 HS lncRNAs to a random draw of 10,000 lncRNA/gene pairs drawn from the remaining ~13500 lncRNAs that are not HS is a fair comparison. Rather, it would be better to do many draws of 40 non-HS lncRNAs and determine an empirical null distribution that way, if possible actively controlling for the overall number of transcripts (also see the following point).

(1) We predicted DBSs in the promoter region of 179128 Ensembl-annotated transcripts and did not merge DBSs (there is no need to merge them). If multiple transcripts share the same TSS, they may share the same DBS, which is natural.

(2) If the DBSs of multiple transcripts of a gene overlap, the overlap does not raise a problem for lncRNA/DNA binding analysis in specific tissues because usually only one transcript is expressed in a tissue. Therefore, there is no such situation “If, e.g., a gene has five isoforms, and these differ in the 3' UTR but their promoter region contains a DBS, is this counted five times, or one?”

(3) It is unclear to us what “it seems like not correcting for this uneven distribution of transcripts is likely to skew results” means. Regarding testing against genome-wide distributions, statistically, it is beneficial to make many rounds of random draws genome-wide, but this will take a huge amount of time. Since more variables demand more rounds of drawing, to our knowledge, this is not widely practiced in large-scale transcriptomic data analyses.

(4) If the difference (result) is small thus calls for rigorous statistical testing, making many rounds of random draws genome-wide is necessary. In our results, “45% of these pairs show a significant expression correlation in specific tissues (Spearman's |rho| >0.3 and FDR <0.05). In contrast, when randomly sampling 10000 pairs of lncRNAs and protein-coding transcripts genome-wide, the percent of pairs showing this level of expression correlation (Spearman's |rho| >0.3 and FDR <0.05) is only 2.3%”.

Thresholds for statistical testing are not consistent, or always well justified. For instance, in line 142 GO testing is performed on the top 2000 genes (according to different rankings), but there's no description of the background regions used as controls anywhere, or of why 2000 genes were chosen as a good number to test? Why not 1000, or 500? Are the results overall robust to these (and other) thresholds? Then line 190 the threshold for downstream testing is now the top 20% of genes, etc. I am not opposed to different thresholds in principle, but they should be justified.

(1) We used the g:Profiler program to perform over-representation analysis to identify enriched GO terms. This analysis is used to determine what pre-defined gene sets (GO terms) are more present (over-represented) in a list of “interesting” genes than what would be expected by chance. Specifically, this analysis is often used to examine whether the majority of genes in a pre-defined gene set fall in the extremes of a list: the top and bottom of the list, for example, may correspond to the largest differences in expression between the two cell types. g:Profiler always takes the whole genome as the reference; that is why we did not mention the whole genome reference. We now add in section 2.2 “(with the whole genome as the reference)”.

(2) Why choosing 2000 but not 2500 genes is somewhat subjective. We now explain that “About 5% of genes have significant sequence differences in humans and chimpanzees, but more show expression differences due to regulatory sequences. We sorted target genes by their DBS affinity and, to be prudential, chose the top 2000 genes (DBS length>252 bp and binding affinity>151) and bottom 2000 genes (DBS length<60 bp but binding affinity>36) to conduct over-representation analysis”.

Likewise, comparing Tajima's D values near promoters to genome-wide values is unfair, because promoters are known to be under strong evolutionary constraints relative to background regions; as such it is not surprising that the results of this comparison are significant. A fairer comparison would attempt to better match controls (eg to promoters without HS lncRNA DBS, which I realise may be nearly impossible), or generate empirical p-values via permutation or simulation.

We used these tests to detect selection signals in DBSs but not in the whole promoter regions. Using promoters without HS lncRNA DBS as the control also has risks because promoter regions contain other kinds of regulatory sequences.

There are huge differences in the comparisons between the Vindija and Altai Neanderthal genomes that to me suggest some sort of technical bias or the such is at play here. e.g. line 190 reports 1256 genes to have a high distance between the Altai Neanderthal and modern humans, but only 134 Vindija genes reach the same threshold of 0.034. The temporal separation between the two specimens does not seem sufficient to explain this difference, nor the difference between the Altai Denisovan and Neanderthal results (2514 genes for Denisovan), which makes me wonder if it is a technical artefact relating to the quality of the genome builds? It would be worth checking.

We feel it is hard to know whether or not the temporal separation between these specimens is sufficient to explain the differences because many details of archaic humans and their genomes remain unknown and because mechanisms determining genotype-phenotype relationships remain poorly known. After 0.034 was determined, these numbers of genes were determined accordingly. We chose parameters and thresholds that best suit the most important requirements, but these parameters and thresholds may not best suit other requirements; this is a problem for all large-scale studies.     

Inferring evolution: There are some points of the manuscript where the authors are quick to infer positive selection. I would caution that GTEx contains a lot of different brain tissues, thus finding a brain eQTL is a lot easier than finding a liver eQTL, just because there are more opportunities for it. Likewise, claims in the text and in Tables 1 and 2 about the evolutionary pressures underlying specific genes should be more carefully stated. The same is true when the authors observe high Fst between groups (line 515), which is only one possible cause of high Fst - population differentiation and drift are just as capable of giving rise to it, especially at small sample sizes.

(1) We add in Discussion that “Finally, not all detected signals reliably indicate positive selection”.

(2) Our results are that more signals are detected in CEU and CHB than in YRI; this agrees all population genetics studies and implies that our results are not wrongly biased because more samples and larger samples were obtained from CEU and CHB.

Author Response:

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

Reviewer #1 (Public review):

Summary:

The manuscript of Odermatt et al. investigates the volatiles released by two species of Desmodium plants and the response of herbivores to maize plants alone or in combination with these species. The results show that Desmodium releases volatiles in both the laboratory and the field. Maize grown in the laboratory also released volatiles, in a similar range. While female moths preferred to oviposit on maize, the authors found no evidence that Desmodium volatiles played a role in lowering attraction to or oviposition on maize.

Strengths:

The manuscript is a response to recently published papers that presented conflicting results with respect to whether Desmodium releases volatiles constitutively or in response to biotic stress, the level at which such volatiles are released, and the behavioral effect it has on the fall armyworm. These questions are relevant as Desmodium is used in a textbook example of pest-suppressive sustainable intercropping technology called push-pull, which has supported tens of thousands of smallholder farmers in suppressing moth pests in maize. A large number of research papers over more than two decades have implied that Desmodium suppresses herbivores in push-pull intercropping through the release of large amounts of volatiles that repel herbivores. This premise has been questioned in recent papers. Odermatt et al. thus contribute to this discussion by testing the role of odors in oviposition choice. The paper confirms that ovipositing FAW preferred maize, and also confirmed that odors released from Desmodium appeared not important in their bioassays.

The paper is a welcome addition to the literature and adds quality headspace analyses of Desmodium from the laboratory and the field. Furthermore, the authors, some of whom have since long contributed to developing push-pull, also find that Desmodium odors are not significant in their choice between maize plants. This advances our knowledge of the mechanisms through which push-pull suppresses herbivores, which is critically important to evolving the technique to fit different farming systems and translating this mechanism to fit with other crops and in other geographical areas.

Thank you for your careful assessment of our manuscript.

Weaknesses:

Below I outline the major concerns:

(1) Clear induction of the experimental plants, and lack of reflective discussion around this: from literature data and previous studies of maize and Desmodium, it is clear that the plants used in this study, particularly the Desmodium, were induced. Maize appeared to be primarily manually damaged, possibly due to sampling (release of GLV, but little to no terpenoids, which is indicative of mostly physical stress and damage, for example, one of the coauthor's own paper Tamiru et al. 2011), whereas Desmodium releases a blend of many compounds (many terpenoids indicative of herbivore induction). Erdei et al. also clearly show that under controlled conditions maize, silver leaf and green leaf Desmodium release volatiles in very low amounts. While the condition of the plants in Odermatt et al. may be reflective of situations in push-pull fields, the authors should elaborate on the above in the discussion (see comments) such that the readers understand that the plant's condition during the experiments. This is particularly important because it has been assumed that Desmodium releases typical herbivore-induced volatiles constitutively, which is not the case (see Erdei et al. 2024). This reflection is currently lacking in the manuscript.

We acknowledge the need for a more reflective discussion on the possible causes of volatile emission due to physical damage. Although the field plants were carefully handled, it is possible that some physical stress may have contributed to the release of volatiles, such as green leaf volatiles (GLVs). We ensured the revised manuscript reflects this nuanced interpretation (lines 282 – 286). However, we also explained more clearly that our aim was to capture the volatile emission of plants used by farmers under realistic conditions and moth responses to these plants, not to be able to attribute the volatile emission to a specific cause (lines 115 – 117). We revised relevant passages throughout the results and discussion to ensure that we do not make any claims about the reason for volatile emissions, and that our claims regarding these plants and their headspace being representative of the system as practiced by farmers are supported. In the revised manuscript we provide a new supplementary table S2 that additionally shows the classification of the identified substances, which also shows that the majority of the substances that were found in the headspace of the sampled plants of Desmodium intortum or Desmodium incanum are monoterpenes, sesquiterpenes, or aromatic compounds, and not GLVs (that are typically emitted following damage).

(2) Lack of controls that would have provided context to the data: The experiments lack important controls that would have helped in the interpretation:

2a The authors did not control the conditions of the plants. To understand the release of volatiles and their importance in the field, the authors should have included controlled herbivory in both maize and Desmodium. This would have placed the current volatile profiles in a herbivory context. Now the volatile measurements hang in midair, leading to discussions that are not well anchored (and should be rephrased thoroughly, see eg lines 183-188). It is well known that maize releases only very low levels of volatiles without abiotic and biotic stressors. However, this changes upon stress (GLVs by direct, physical damage and eg terpenoids upon herbivory, see above). Erdei et al. confirm this pattern in Desmodium. Not having these controls, means that the authors need to put the data in the context of what has been published (see above).

We appreciate this concern. Our study aimed to capture the real-world conditions of push-pull fields, where Desmodium and maize grow in natural environments without the direct induction of herbivory for experimental purposes (lines 115 – 117). We agree that in further studies it would be important to carry out experiments under different environmental conditions, including herbivore damage. However, this was not within the scope of the present study.

2b It would also have been better if the authors had sampled maize from the field while sampling Desmodium. Together with the above point (inclusion of herbivore-induced maize and Desmodium), the levels of volatile release by Desmodium would have been placed into context.

We acknowledge that sampling maize and other intercrop plants, such as edible legumes, alongside Desmodium in the push-pull field would have allowed us to make direct comparisons of the volatile profiles of different plants in the push-pull system under shared field conditions. Again, this should be done in future experiments but was beyond the scope of the present study. Due to the amount of samples we could handle given cost and workload, we chose to focus on Desmodium because there is much less literature on the volatile profiles of field-grown Desmodium than maize plants in the field: we are aware of one study attempting to measure field volatile profiles from Desmodium intortum (Erdei et al. 2024) and no study attempting this for Desmodium incanum. We pointed out this justification for our focus on Desmodium in the manuscript (lines 435 - 439). Additionally, we suggested in the discussion that future studies should measure volatile profiles from all plants commonly used in push-pull systems alongside Desmodium (lines 267 – 269).

2c To put the volatiles release in the context of push-pull, it would have been important to sample other plants which are frequently used as intercrop by smallholder farmers, but which are not considered effective as push crops, particularly edible legumes. Sampling the headspace of these plants, both 'clean' and herbivore-induced, would have provided a context to the volatiles that Desmodium (induced) releases in the field - one would expect unsuccessful push crops to not release any of these 'bioactive' volatiles (although 'bioactive' should be avoided) if these odors are responsible for the pest suppressive effect of Desmodium. Many edible intercrops have been tested to increase the adoption of push-pull technology but with little success.

We very much agree that such measurements are important for the longer-term research program in this field. But again, for the current study this would have exploded the size of the required experiment. Regarding bioactivity, we have been careful to use the phrase "potentially bioactive" solely when referring to findings from the literature (lines 99–103), in order to avoid making any definitive claims about our own results.

Because of the lack of the above, the conclusions the authors can draw from their data are weakened. The data are still valuable in the current discussion around push-pull, provided that a proper context is given in the discussion along the points above.

We think our revisions made the specific aims of this study more explicit and help to avoid misleading claims.

(3) 'Tendency' of the authors to accept the odor hypothesis (i.e. that Desmodium odors are responsible for repelling FAW and thereby reduce infestation in maize under push-pull management) in spite of their own data: The authors tested the effects of odor in oviposition choice, both in a cage assay and in a 'wind tunnel'. From the cage experiments, it is clear that FAW preferred maize over Desmodium, confirming other reports (including Erdei et al. 2024). However, when choosing between two maize plants, one of which was placed next to Desmodium to which FAW has no tactile (taste, structure, etc), FAW chose equally. Similarly in their wind tunnel setup (this term should not be used to describe the assay, see below), no preference was found either between maize odor in the presence or absence of Desmodium. This too confirms results obtained by Erdei et al. (but add an important element to it by using Desmodium plants that had been induced and released volatiles, contrary to Erdei et al. 2024). Even though no support was found for repellency by Desmodium odors, the authors in many instances in the manuscript (lines 30-33, 164-169, 202, 279, 284, 304-307, 311-312, 320) appear to elevate non-significant tendencies as being important. This is misleading readers into thinking that these interactions were significant and in fact confirming this in the discussion. The authors should stay true to their own data obtained when testing the hypothesis of whether odors play a role in the pest-suppressive effect of push-pull.

We appreciate this feedback and agree that we may have overstated claims that could not be supported by strict significance tests. However, we believe that non-significant tendencies can still provide valuable insights. In the revised version of the manuscript, we ensured a clear distinction between statistically significant findings and non-significant trends and remove any language that may imply stronger support for the odor hypothesis than what the data show in all the lines that were mentioned.

(4) Oviposition bioassay: with so many assays in close proximity, it is hard to certify that the experiments are independent. Please discuss this in the appropriate place in the discussion.

We have pointed this out in the submitted manuscript in lines 275 – 279. Furthermore, we included detailed captions to figure 4 - supporting figure 3 & figure 4 - supporting figure 4. We are aware that in all such experiments there is a danger of between-treatment interference, which we pointed out for our specific case. We stated that with our experimental setup we tried to minimize interference between treatments by spacing and temporal staggering. We would like to point out that this common caveat does not invalidate experimental designs when practicing replication and randomization. We assume that insects are able to select suitable oviposition sites in the background of such confounding factors under realistic conditions.

(5) The wind tunnel has a number of issues (besides being poorly detailed):

5a. The setup which the authors refer to as a 'wind tunnel' does not qualify as a wind tunnel. First, there is no directional flow: there are two flows entering the setup at opposite sides. Second, the flow is way too low for moths to orient in (in a wind tunnel wind should be presented as a directional cue. Only around 1.5 l/min enters the wind tunnel in a volume of 90 l approximately, which does not create any directional flow. Solution: change 'wind tunnel' throughout the text to a dual choice setup /assay.)

We agree with these criticisms and changed the terminology accordingly from ‘wind tunnel’ to ‘dual choice assay’. We have now conducted an additional experiment which we called ‘no-choice assay’ that provides conditions closer to a true wind tunnel. The setup of the added experiment features an odor entry point at only one side of the chamber to create a more directional airflow. Each treatment (maize alone, maize + D. intortum, maize + D. incanum, and a control with no plants) was tested separately, with only one treatment conducted per evening to avoid cross-contamination, as described in the methods section of the no-choice assay.

5b. There is no control over the flows in the flight section of the setup. It is very well possible that moths at the release point may only sense one of the 'options'. Please discuss this.

We added this to the discussion (lines 369 – 374). The new no-choice assays also address this concern by using a setup with laminar flow.

5c. Too low a flow (1,5 l per minute) implies a largely stagnant air, which means cross-contamination between experiments. An experiment takes 5 minutes, but it takes minimally 1.5 hours at these flows to replace the flight chamber air (but in reality much longer as the fresh air does not replace the old air, but mixes with it). The setup does not seem to be equipped with e.g. fans to quickly vent the air out of the setup. See comments in the text. Please discuss the limitations of the experimental setup at the appropriate place in the discussion.

We added these limitations to the discussion and addressed these concerns with new experiments (see answer 5a).

5d. The stimulus air enters through a tube (what type of tube, diameter, length, etc) containing pressurized air (how was the air obtained into bags (type of bag, how is it sealed?), and the efflux directly into the flight chamber (how, nozzle?). However, it seems that there is no control of the efflux. How was leakage prevented, particularly how the bags were airtight sealed around the plants? 

We added the missing information to the methods and provided details about types of bags, manufacturers, and pre-treatments in the method section. In short, PTFE tubes connected bagged plants to the bioassay setup and air was pumped in at an overpressure, so leakage was not eliminated but contamination from ambient air was avoided.

5e. The plants were bagged in very narrowly fitting bags. The maize plants look bent and damaged, which probably explains the GLVs found in the samples. The Desmodium in the picture (Figure 5 supplement), which we should assume is at least a representative picture?) appears to be rather crammed into the bag with maize and looks in rather poor condition to start with (perhaps also indicating why they release these volatiles?). It would be good to describe the sampling of the plants in detail and explain that the way they were handled may have caused the release of GLVs.

We included a more detailed description of the plant handling and bagging processes to the methods to clarify how the plants were treated during the dual-choice and the no-choice assays reported in the revised manuscript. We politely disagree that the maize plants were damaged and the Desmodium plants not representative of those encountered in the field. The plants were grown in insect-proof screen houses to prevent damage by insects and carefully curved without damaging them to fit into the bag. The Desmodium plant pictured was D. incanum, which has sparser foliage and smaller leaves than D. intortum.

(6) Figure 1 seems redundant as a main figure in the text. Much of the information is not pertinent to the paper. It can be used in a review on the topic. Or perhaps if the authors strongly wish to keep it, it could be placed in the supplemental material.

We think that Figure 1 provides essential information about the push-pull system and the FAW. To our knowledge, this partly contradictory evidence so far has not been synthesized in the literature. We realize that such a figure would more commonly be provided in a review article, but we do not think that the small number of studies on this topic so far justify a stand-alone review. Instead, the introduction to our manuscript includes a brief review of these few studies, complemented by the visual summary provided in Figure 1 and a detailed supplementary table.

Reviewer #2 (Public review):

Based on the controversy of whether the Desmodium intercrop emits bioactive volatiles that repel the fall armyworm, the authors conducted this study to assess the effects of the volatiles from Desmodium plants in the push-pull system on behavior of FAW oviposition. This topic is interesting and the results are valuable for understanding the push-pull system for the management of FAW, the serious pest. The methodology used in this study is valid, leading to reliable results and conclusions. I just have a few concerns and suggestions for improvement of this paper:

(1) The volatiles emitted from D. incanum were analyzed and their effects on the oviposition behavior of FAW moth were confirmed. However, it would be better and useful to identify the specific compounds that are crucial for the success of the push-pull system.

We fully agree that identifying specific volatile compounds responsible for the push-pull effect would provide valuable insights into the underlying mechanisms of the system. However, the primary focus of this study was to address the still unresolved question whether Desmodium emits detectable or “significant” amounts of volatiles at all under field conditions, and the secondary aim was to test whether we could demonstrate a behavioral effect of Desmodium headspace on FAW moths. Before conducting our experiments, we carefully considered the option of using single volatile compounds and synthetic blends in bioassays. We decided against this because we judged that the contradictory evidence in the literature was not a sufficient basis for composing representative blends. Furthermore, we think it is an important first step to test f. or behavioral responses to the headspaces of real plants. We consider bioassays with pure compounds to be important for confirmation and more detailed investigation in future studies. There was also contradictory evidence in the literature regarding moth responses to plants. We thus opted to focus on experiments with whole plants to maintain ecological relevance.

(2) That would be good to add "symbols" of significance in Figure 4 (D).

We report the statistical significance of the parameters in Figure 4 (D) in Table 3, which shows the mixed model applied for oviposition bioassays. While testing significance between groups is a standard approach, we used a more robust model-based analysis to assess the effects of multiple factors simultaneously. We provided a cross-reference to Table 3 from the figure description of Figure 4 (D) for readers to easily find the statistical details.

(3) Figure A is difficult for readers to understand.

Unfortunately, it is not entirely clear which specific figure is being referred to as "Figure A" in this comment. We tried to keep our figures as clear as possible.

(4) It will be good to deeply discuss the functions of important volatile compounds identified here with comparison with results in previous studies in the discussion better.

Our study does not provide strong evidence that specific volatiles from Desmodium plants are important determinants of FAW oviposition or choice in the push-pull system. Therefore, we prefer to refrain from detailed discussions of the potential importance of individual compounds. However, in the revised version, we provide an additional table S2 which identifies the overlap with volatiles previously reported from Desmodium, as only the total numbers are summarized in the discussion of the submitted paper.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The points raised are largely self-explanatory as to what needs to be done to fully resolve them. At a minimum the text needs to be seriously revised to:

(1) reflect the data obtained.

(2) reflect on the limitations of their experimental setup and data obtained.

(3) put the data obtained and its limitations in what these tell us and particularly what not. Ideally, additional headspace measurements are taken, including from herbivory and 'clean' maize and Desmodium (in which there is better control of biotic and abiotic stress), as well as other crops commonly planted as companion crops with maize (but none of them reducing pest pressure).

Thank you for this summary. Please see our detailed responses above.

In addition to the main points of critique provided above, I have provided additional comments in the text (https://elife-rp.msubmit.net/elife-rp_files/2024/07/18/00134767/00/134767_0_attach_28_25795_convrt.pdf). These elaborate on the above points and include some new ones too. These are the major points of critique, which I hope the authors can address.

Thank you very much for these detailed comments.

Reviewer #2 (Recommendations for the authors):

It is important to note that the original push-pull system was developed against stemborers and involved Napier grass (still used) around the field, which attracts stemborer moths, and Molasses grass as the intercrop that repels the moths and attracts parasitoids. Later, Molasses grass was replaced by desmodiums because it is a legume that fixes nitrogen and therefore can increase nitrate levels in the soil, but most importantly because it prevents germination of the parasitic Striga weed. The possible repellent effect of desmodium on pests and attraction of natural enemies was never properly tested but assumed, probably to still be able to use the push-pull terminology. This "mistake" should be recognized here and in future publications. It is a real pity that the controversy over the repellent effect of desmodium distracts from the amazing success of the push-pull system, also against the fall armyworm.

We thank the reviewer for pointing out these issues, which are part of the reason for our Figure 1 and why we would like to keep it. We have described this development of the system in the introduction to better present the push-pull system. Our aim in Figure 1 and Table S1 is to highlight both the evidence of the system's success, and the gaps in our understanding, regarding specifically control of damage from the FAW.

Reviewer #1 (Public review):

Summary:

This paper addresses an important and topical issue: how temporal context, at various time scales, affects various psychophysical measures, including reaction times, accuracy, and localization. It offers interesting insights, with separate mechanisms for different phenomena, which are well discussed.

Strengths:

The paradigm used is original and effective. The analyses are rigorous.

Weaknesses:

Here I make some suggestions for the authors to consider. Most are stylistic, but the issue of precision may be important.

(1) The manuscript is quite dense, with some concepts that may prove difficult for the non-specialist. I recommend spending a few more words (and maybe some pictures) describing the difference between task-relevant and task-irrelevant planes. Nice technique, but not instantly obvious. Then we are hit with "stimulus-related", which definitely needs some words (also because it is orthogonal to neither of the above).

(2) While I understand that the authors want the three classical separations, I actually found it misleading. Firstly, for a perceptual scientist to call intervals in the order of seconds (rather than milliseconds), "micro" is technically coming from the raw prawn. Secondly, the divisions are not actually time, but events: micro means one-back paradigm, one event previously, rather than defined by duration. Thirdly, meso isn't really a category, just a few micros stacked up (and there's not much data on this). And macro is basically patterns, or statistical regularities, rather than being a fixed time. I think it would be better either to talk about short-term and long-term, which do not have the connotations I mentioned. Or simply talk about "serial dependence" and "statistical regularities". Or both.

(3) More serious is the issue of precision. Again, this is partially a language problem. When people use the engineering terms "precision" and "accuracy" together, they usually use the same units, such as degrees. Accuracy refers to the distance from the real position (so average accuracy gives bias), and precision is the clustering around the average bias, usually measured as standard deviation. Yet here accuracy is percent correct: also a convention in psychology, but not when contrasting accuracy with precision, in the engineering sense. I suggest you change "accuracy" to "percent correct". On the other hand, I have no idea how precision was defined. All I could find was: "mixture modelling was used to estimate the precision and guess rate of reproduction responses, based on the concentration (k) and height of von Mises and uniform distributions, respectively". I do not know what that means.

(4) Previous studies show serial dependence can increase bias but decrease scatter (inverse precision) around the biased estimate. The current study claims to be at odds with that. But are the two measures of precision relatable? Was the real (random) position of the target subtracted from each response, leaving residuals from which the inverse precision was calculated? (If so, the authors should say so..) But if serial dependence biases responses in essentially random directions (depending on the previous position), it will increase the average scatter, decreasing the apparent precision.

(5) I suspect they are not actually measuring precision, but location accuracy. So the authors could use "percent correct" and "localization accuracy". Or be very clear what they are actually doing.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1:

(1) Developmental time series:

It was not entirely clear how this experiment relates to the rest of the manuscript, as it does not compare any effects of transport within or across species.

Implemented Changes:  

The importance of species arrival timing for community assembly is addressed in both the introduction and discussion. To accommodate the reviewer’s concerns and further emphasize this point, we have added a clarifying sentence to the results section and included an illustrative example with supporting literature in the discussion.

Results: Clarifying the timing of initial microbial colonization is essential for determining whether and how priority effects mediate community assembly of vertically transmitted microbes in early life, or whether these microbes arrive into an already established microbial landscape. We used non-sterile frogs of our captive laboratory colony (…)

Discussion: For example, early microbial inoculation has been shown to increase the relative abundance of beneficial taxa such as Janthinobacterium lividum (Jones et al., 2024), whereas efforts to introduce the same probiotic into established adult communities have not led to long-term persistence (Bletz, 2013; Woodhams et al., 2016).  

(2) Cross-foster experiment:

The "heterospecific transport" tadpoles were manually brushed onto the back of the surrogate frog, while the "biological transport" tadpoles were picked up naturally by the parent. It is a little challenging to interpret the effect of caregiver species since it is conflated with the method of attachment to the parent. I noticed that the uptake of Os-associated microbes by Os-transported tadpoles seemed to be higher than the uptake of Rv-associated microbes by Rv-associated tadpoles (comparing the second box from the left to the rightmost boxplot in panel S2C). Perhaps this could be a technical artifact if manual attachment to Os frogs was more efficient than natural attachment to Rv frogs.

I was also surprised to see so much of the tadpole microbiome attributed to Os in tadpoles that were not transported by Os frogs (25-50% in many cases). It suggests that SourceTracker may not be effectively classifying the taxa.

Implemented Changes:  

Methods (Study species, reproductive strategies and life history): Oophaga sylvatica (Os) (Funkhouser, 1956; CITES Appendix II, IUCN Conservation status: Near Threatened) is a large, diurnal poison frog (family Dendrobatidae) inhabiting lowland and submontane rainforests in Colombia and Ecuador. While male Os care for the clutch of up to seven eggs, females transport 1-2 tadpoles at a time to water-filled leaf axils where tadpoles complete their development (Pašukonis et al., 2022; Silverstone, 1973; Summers, 1992). Notably, females return regularly to these deposition sites to provision their offspring with unfertilized eggs.

Discussion: Most poison frogs transport tadpoles on their backs, but the mechanism of adherence remains unclear. Similar to natural conditions, tadpoles that are experimentally placed onto a caregiver’s back also gradually adhere to the dorsal skin, where they remain firmly attached for several hours as the adult navigates dense terrain. Although transport durations were standardized, species-specific factors- such as microbial density at the contact site, microbial taxa identity, and skin physiology such as moisture -could influence microbial transmission between the transporting frog and the tadpole. While these differences may have contributed to varying transmission efficacies observed between the two frog species in our experiment, none of these factors should compromise the correct microbial source assignment. We thus conclude that transporting frogs serve as a source of microbiota for transported tadpoles. However, further studies on species-specific physiological traits and adherence mechanisms are needed to clarify what modulates the efficacy of microbial transmission during transport, both under experimental and natural conditions.  

Methods (Vertical transmission): Cross-fostering tadpoles onto non-parental frogs has been used previously to study navigation in poison frogs (Pašukonis et al., 2017). According to our experience, successful adherence to both parent and heterospecific frogs depends on the developmental readiness of tadpoles, which must have retracted their gills and be capable of hatching from the vitelline envelope through vigorous movement. Another factor influencing cross-fostering success is the docility of the frog during initial attachment, as erratic movements easily dislodge tadpoles before adherence is established. Rv are small, jumpy frogs that are easily stressed by handling, making experimental fostering of tadpoles—even their own— impractical. Therefore, we favored an experimental design where tadpoles initiate natural transport and parental frogs pick them up with a 100% success rate. We chose the poison frog Os as foster frogs because adults are docile, parental care in this species involves transporting tadpoles, and skin microbial communities differ from Rv- a critical prerequisite for our SourceTracker analysis. The use of the docile Os as the foster species enabled a 100% cross-fostering success rate, with no notable differences in adherence strength after six hours.

Methods (Sourcetracker Analysis): To assess training quality, we evaluated model selfassignment using source samples. We selected the model trained on a dataset rarefied to the read depth of the adult frog sample with the lowest read count (48162 reads), as it showed the best overall self-assignment performance, whereas models trained on datasets rarefied to the lowest overall read depth performed worse. Unlike studies using technical replicates, our source samples represent distinct biological individuals and sampling timepoints, where natural microbiome variability is expected within each source category. Consequently, we considered self-assignment rates above 70% acceptable. All source samples were correctly assigned to their respective categories (Rv, Os, or control), but with varying proportions of reads assigned as 'Unknown'. Adult frog sources were reliably selfidentified with high confidence (Os: 97.2% median, IQR = 1.4; Rv: 76.3% median, IQR = 38.1). Adult R. variabilis frogs displayed a higher proportion of 'Unknown' assignments compared to O. sylvatica, likely reflecting greater biological variability among individuals and/or a higher proportion of rare taxa not well captured in the training set. The control tadpole source showed lower self-assignment accuracy (median = 30.5%, IQR = 17.1), as expected given the low microbial biomass of these samples, which resulted in low read depth. Low readdepth limits the information available to inform the iterative updating steps in Gibbs sampling and reduces confidence in source assignments. We therefore verified the robustness of our results by performing the second Sourcetracker analysis as described above, training the model only on adult sources and assigning all tadpoles, including lowbiomass controls, as sinks (as described above). Self-assignment rates for the second training set varied (O. sylvatica: 79.2% median, IQR = 29; R. variabilis: 96.6% median, IQR = 3.7), while results remained consistent across analyses, supporting the reliability of our findings.

(3) Cross-species analysis:

Like the developmental time series, this analysis doesn't really address the central question of the manuscript. I don't think it is fair for the authors to attribute the difference in diversity to parental care behavior, since the comparison only includes n=2 transporting species and n=1 non-transporting species that differ in many other ways. I would also add that increased diversity is not necessarily an expectation of vertical transmission. The similarity between adults and tadpoles is likely a more relevant outcome for vertical transmission, but the authors did not find any evidence that tadpole-adult similarity was any higher in species with tadpole transport. In fact, tadpoles and adults were more similar in the non-transporting species than in one of the transporting species (lines 296-298), which seems to directly contradict the authors' hypothesis. I don't see this result explained or addressed in the Discussion.

To address the reviewer’s concerns, we implemented the following changes:  

Results:

We rephrased the following sentence from the results part:  

“These variations may therefore be linked to differing reproductive traits: Af and Rv lay terrestrial egg clutches and transport hatchlings to water, whereas Ll, a non-transporting species, lays eggs directly in water.”

To read

“These variations may therefore reflect differences in life history traits among the three species.”

We moved the information on differing reproductive strategies into the Discussion, where it contributes to a broader context alongside other life history traits that may influence community diversity.

Discussion (1): We added to our discussion that increased microbial diversity was not an expected outcome of vertical transmission.

“However, increased microbial diversity is not a known outcome of vertical transmission, and further studies across a broader range of transporting and non-transporting species are needed to assess the role of transport in shaping diversity of tadpole-associated microbial communities.”

Discussion (2): Likewise, communities associated with adults and tadpoles of transporting species were no more similar than those of non-transporting species. While poison frog tadpoles do acquire caregiver-specific microbes during transport, most of these microbes do not persist on the tadpoles' skin long-term. This pattern can likely be attributed to the capacity of tadpole skin- and gut microbiota to flexibly adapt to environmental changes (Emerson & Woodley, 2024; Santos et al., 2023; Scarberry et al., 2024). It may also reflect the limited compatibility of skin microbiota from terrestrial adults with aquatic habitats or tadpole skin, which differs structurally from that of adults (Faszewski et al., 2008). As a result, many transmitted microbes are probably outcompeted by microbial taxa continuously supplied by the aquatic environment. Interestingly, microbial communities of the non-transporting Ll were more similar to their adult counterparts than those of poison frogs. This pattern might reflect differences in life history among the species. While adult Ll commonly inhabit the rock pools where their tadpoles develop, adults of the two poison frog species visit tadpole nurseries only sporadically for deposition. These differences in habitat use may result in adult Ll hosting skin microbiota that are better adapted to aquatic environments as compared to Rv and Af. Additionally, their presence in the tadpoles’ habitat could make Ll a more consistent source of microbiota for developing tadpoles.

(4) Field experiment: The rationale and interpretation of the genus-level network are not clear, and the figure is not legible. What does it mean to "visualize the microbial interconnectedness" or to be a "central part of the community"? The previous sentences in this paragraph (lines 337-343) seem to imply that transfer is parent-specific, but the genuslevel network is based on the current adult frogs, not the previous generation of parents that transported them. So it is not clear that the distribution or co-distribution of these taxa provides any insight into vertical transmission dynamics.

Implemented Changes:  

We appreciate the reviewer’s close reading and understand how the inclusion of the network visualization without further clarification may have led to confusion. To clarify, the network was constructed from all adult frogs in the population, including—but not limited to—the parental frogs examined in the field experiment. We do not make any claims about the origin of the microbial taxa found on parental frogs. Rather, our aim was to illustrate how genera retained on tadpoles (following potential vertical transmission) contribute to the skin microbial communities of adult frogs of this population beyond just the parental individuals. This finding supports the observation that these retained taxa are generally among the most abundant in adult frogs. However, since this information is already presented in Table S8 and the figure is not essential to the main conclusions, we have removed Supplementary Figure S5 and the accompanying sentence: “A genus-level network constructed from 44 adult frogs shows that the retained genera make up a central part of the community of adult Rv in wild populations (Fig. S5).” We have adjusted the Methods section accordingly.

Reviewer #2:

I did not find any major weaknesses in my review of this paper. The work here could potentially benefit from absolute abundance levels for shared ASVs between adults and tadpoles to more thoroughly understand the influences of vertical transmission that might be masked by relative abundance counts. This would only be a minor improvement as I think the conclusions from this work would likely remain the same, however.

In response to the reviewer’s suggestion, we estimated the absolute abundance of specific ASVs for all samples of tadpoles in which Sourcetracker identified shared ASVs between adults and tadpoles. The resulting scaled absolute abundance values (in copies/μL and copies per tadpole) are provided in Table S10, and a description of the method has been incorporated into the revised Methods section of the manuscript. To support the robustness of this approach in our dataset, we additionally designed an ASV-specific system for ASV24902-Methylocella. Candidate primers were assessed for specificity by performing local BLASTn alignments against the full set of ASV sequences identified in the respective microbial communities of tadpoles. We optimized the annealing temperature via gradient PCR and confirmed primer specificity through Sanger sequencing of the PCR product (Forward: 5′–GAGCACGTAGGCGGATCT–3′ Reverse: 5′–GGACTACNVGGGTWTCTAAT–3′). Using this approach, we confirmed that the relative abundance of ASV24902 (18.05% in the amplicon sequencing data) closely matched its proportion of the absolute 16S rRNA copy number in transported tadpole 6 (18.01%). While we intended to quantify all shared ASVs, we were limited to this single target due to insufficient material for optimizing the assays. As this particular ASV was also detected in the water associated with the same tadpole, we chose not to include this confirmation in the manuscript. Nevertheless, the close match supports the reliability of our approach for scaling absolute abundances in this dataset.

Results: Absolute abundances of shared ASVs likely originating from the parental source pool (as identified by Sourcetracker) after one month of growth ranged from 7804 to 172326 copies per tadpole (Table S10).

Methods: Quantitative analysis of 16S rRNA copy numbers with digital PCR (dPCR)

Absolute abundances were estimated for ASVs that were shared between tadpoles after a one-month growth period and their respective caregivers, and for which Sourcetracker analysis identified the caregiver as a likely source of microbiota. We followed the quantitative sequencing framework described by Barlow et al. (2020), measuring total microbial load via digital PCR (dPCR) with the same universal 16S rRNA primers used to amplify the v4 region in our sequencing dataset. Absolute 16S rRNA copy numbers obtained from dPCR were then multiplied by the relative abundances from our amplicon sequencing dataset to calculate ASV-specific scaled absolute abundances. All dPCR reactions were carried out on a QIAcuity Digital PCR System (Qiagen) using Nanoplates with a 8.5K partition configuration, using the following cycling program: 95°C for 2 minutes, 40 cycles of 95°C for 30 seconds and 52°C for 30 seconds and 72°C for 1 minute, followed by 1 cycle of 40°C for 5 minutes. Reactions were prepared using the QIAcuity EvaGreen PCR Kit (Qiagen, Cat. No. 250111) with 2 µL of DNA template per reaction, following the manufacturer's protocol, and included a negative no-template control and a cleaned and sequenced PCR product as positive control. Samples were measured in triplicates and serial dilutions were performed to ensure accurate quantification. Data were processed with the QIAcuity Software Suite (v3.1.0.0). The threshold was set based on the negative and positive controls in 1D scatterplots. We report mean copy numbers per microliter with standard deviations, correcting for template input, dPCR reaction volume, and dilution factor. Mean copy numbers per tadpole were additionally calculated by accounting for the DNA extraction (elution) volume.  

Recommendations for the authors:

Reviewer #1:

(1) Figure 1b summarizes the ddPCR data as a binary (detected/not detected), but this contradicts the main text associated with this figure, which describes bacteria as present, albeit in low abundances, in unhatched embryos (lines 145-147). Could the authors keep the diagram of tadpole development, which I find very useful, but add the ddPCR data from Figure S1c instead of simply binarizing it as present/absent?

We appreciate the reviewer’s positive feedback on the clarity of the figure. We agree that presenting the ddPCR data in a more quantitative manner provides a more accurate representation of bacterial abundance across developmental stages. In response, we have retained the developmental diagram, as suggested, and replaced the binary (detected/not detected) information in Figure 1B with rounded mean values for each stage. To complement this, we have included mean values and standard deviations in Table S1. The corresponding text in the main manuscript and legends has been revised accordingly to reflect these changes.  

(2) More information about the foster species, Oophaga sylvatica, would be helpful. Are they sympatric with Rv? Is their transporting behavior similar to that of Rv?

We thank the reviewer for this helpful comment. In response, we have added further details on the biology and parental care behavior of Oophaga sylvatica, including information on its distribution range. The species does not overlap with Ranitomeya variabilis at the specific study site where the field work was conducted, although the species are sympatric in other countries. These additions have been incorporated into the Methods section under "Study species, reproductive strategies, and life history."  

(3) Plotting the proportion of each tadpole microbiome attributed to R. variabilis and the proportion attributed to O. sylvatica on the same plot is confusing, as these points are nonindependent and there is no way for the reader to figure out which points originated from the same tadpole. I would suggest replacing Figure 1D with Figure S2C, which (if I understand correctly) displays the same data, but is separated according to source.

We agree with the reviewer that Figure S2C allows for clearer interpretation of our results. In response, we implemented the suggested change and replaced Figure 1D with the alternative visualization previously shown in Figure S2C, which displays the same data separated by source. To provide readers with a complementary overview of the full dataset, we have retained the original combined plot in the supplementary material as Figure S2D.

(4) On the first read, I found the use of "transport" in the cross-fostering experiment confusing until I understood that they weren't being transported "to" anywhere in particular, just carried for 6 hours. A change of phrasing might help readers here.

We acknowledge the reviewer’s concern and have replaced “transported” with “carried” to avoid confusion for readers who may be unfamiliar with the behavioral terminology. However, because “transport” is the term widely used by specialists to describe this behavior, we now introduce it in the context of the experimental design with the following phrasing:

“For this design, sequence-based surveys of amplified 16S rRNA genes were used to assess the composition of skin-associated microbial communities on tadpoles and their adult caregivers (i.e., the frogs carrying the tadpoles, typically referred to as ‘transporting’ frogs).”

(5) "Horizontal transfer" typically refers to bacteria acquired from other hosts, not environmental source pools (line 394).

We addressed this concern by rephrasing the sentence in the Discussion to avoid potential confusion. The revised text now reads:

“Across species, newborns might acquire bacteria not only through transfer from environmental source pools and other hosts (…)”  

(6) The authors suggest that tadpole transport may have evolved in Rv and Af to promote microbial diversity because "increased microbial diversity is linked to better health outcomes" (lines 477-479). It is often tempting to assume that more diversity is always better/more adaptive, but this is not universally true. The fact that the Ll frogs seem to be doing fine in the same environment despite their lower microbiome diversity suggests that this interpretation might be too far of a reach based on the data here.

We appreciate the reviewer’s concern, agree that increased microbial diversity is not inherently advantageous and have revised the paragraph to make this clearer.  

“While increased microbial diversity is not inherently advantageous, it has been associated with beneficial outcomes such as improved immune function, lower disease risk, and enhanced fitness in multiple other vertebrate systems.”

However, rather than claiming that greater diversity is always advantageous, we suggest that this possibility should not be excluded and consider it a relevant aspect of a comprehensive discussion. We also note that whether poison frog tadpoles perform equally well with lower microbial diversity remains an open question. Drawing such conclusions would require experimental validation and cannot be inferred from comparisons with an evolutionarily distant species that differs in life history.

Reviewer #2:

(1) Figure 2: Are the data points in C a subset (just the tadpoles for each species) of B? The numbers look a little different between them. The number of observed ASVs in panel B for Rv look a bit higher than the observed ASVs in panel C.

The data shown in panel C are indeed a subset of the samples presented in panel B, focusing specifically on tadpoles of each species. The slight differences in the number of observed ASVs between panels result from differences in rarefaction depth between comparisons: due to variation in sequencing depth across species and life stages, we performed rarefaction separately for each comparison in order to retain the highest number of taxa while ensuring comparability within each group. Although we acknowledge that this is not a standard approach, we found that results were consistent when rarefying across the full dataset, but chose the presented approach to better accommodate variation in our sample structure. This methodological detail is described in the Methods section:

“All alpha diversity analyses were conducted with datasets rarefied to 90% of the read number of the sample with the fewest reads in each comparison and visualized with boxplots.”

It is also noted in the figure legend: “The dataset was separately rarefied to the lowest read depth f each comparison.” We hope this clarification adequately addresses the reviewer’s concern and therefore have not made additional changes.

(2) Lines 304-305: in the Figure 4B plot, there appear to be 12 transported tadpoles and 8 non-transported tadpoles.

Thank you for catching this. We have corrected the plot and the associated statistics (alpha and beta diversity) in the results section as well as in the figure. Importantly, the correction did not affect any other results, and the overall findings and interpretations remain unchanged.  

(3) Line 311: I think this should be Figure 4B.

(4) Line 430: tadpole transport.

(5) Line 431: I believe commas need to surround this phrase "which range from a few hours to several days depending on the species (Lötters et al., 2007; McDiarmid & Altig, 1999; Pašukonis et al., 2019)".

We thank the reviewer for the thorough review and have corrected all typographical and formatting errors noted in comments (3) – (5).

Author Response:

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

Reviewer #1 (Recommendations for the authors): 

One minor question would be whether the authors could expand more on the application of END-Seq to examine the processive steps of the ALT mechanism? Can they speculate if the ssDNA detected in ALT cells might be an intermediate generated during BIR (i.e., is the ssDNA displaced strand during BIR) or a lesion? Furthermore, have the authors assessed whether ssDNA lesions are due to the loss of ATRX or DAXX, either of which can be mutated in the ALT setting?

We appreciate the reviewer’s insightful questions regarding the application of our assays to investigate the nature of the ssDNA detected in ALT telomeres. Our primary aim in this study was to establish the utility of END-seq and S1-END-seq in telomere biology and to demonstrate their applicability across both ALT-positive and -negative contexts. We agree that exploring the mechanistic origins of ssDNA would be highly informative, and we anticipate that END-seq–based approaches will be well suited for such future studies. However, it remains unclear whether the resolution of S1-END-seq is sufficient to capture transient intermediates such as those generated during BIR. We have now included a brief speculative statement in the revised discussion addressing the potential nature of ssDNA at telomeres in ALT cells.

Reviewer #2 (Recommendations for the authors):

How can we be sure that all telomeres are equally represented? The authors seem to assume that END-seq captures all chromosome ends equally, but can we be certain of this? While I do not see an obvious way to resolve this experimentally, I recommend discussing this potential bias more extensively in the manuscript.

We thank the reviewer for raising this important point. END-seq and S1-END-seq are unbiased methods designed to capture either double-stranded or single-stranded DNA that can be converted into blunt-ended double-stranded DNA and ligated to a capture oligo. As such, if a subset of telomeres cannot be processed using this approach, it is possible that these telomeres may be underrepresented or lost. However, to our knowledge, there are no proposed telomeric structures that would prevent capture using this method. For example, even if a subset of telomeres possesses a 5′ overhang, it would still be captured by END-seq. Indeed, we observed the consistent presence of the 5′-ATC motif across multiple cell lines and species (human, mouse, and dog). More importantly, we detected predictable and significant changes in sequence composition when telomere ends were experimentally altered, either in vivo (via POT1 depletion) or in vitro (via T7 exonuclease treatment). Together, these findings support the robustness of the method in capturing a representative and dynamic view of telomeres across different systems.

That said, we have now included a brief statement in the revised discussion acknowledging that we cannot fully exclude the possibility that a subset of telomeres may be missed due to unusual or uncharacterized structures

I believe Figures 1 and 2 should be merged.

We appreciate the reviewer’s suggestion to merge Figures 1 and 2. However, we feel that keeping them as separate figures better preserves the logical flow of the manuscript and allows the validation of END-seq and its application to be presented with appropriate clarity and focus. We hope the reviewer agrees that this layout enhances the clarity and interpretability of the data.

Scale bars should be added to all microscopy figures.

We thank the reviewer for pointing this out. We have now added scale bars to all the microscopy panels in the figures and included the scale details in the figure legends.

Reviewer #3 (Recommendations for the authors):

Overall, the discussion section is lacking depth and should be expanded and a few additional experiments should be performed to clarify the results.

We thank the reviewer for the suggestions. Based on this reviewer’s comments and comments for the other reviewers, we incorporated several points into the discussion. As a result, we hope that we provide additional depth to our conclusions.

(1) The finding that the abundance of variant telomeric repeats (VTRs) within the final 30 nucleotides of the telomeric 5' ends is similar in both telomerase-expressing and ALT cells is intriguing, but the authors do not address this result. Could the authors provide more insight into this observation and suggest potential explanations? As the frequency of VTRs does not seem to be upregulated in POT1-depleted cells, what then drives the appearance of VTRs on the C-strand at the very end of telomeres? Is CST-Pola complex responsible?

The reviewer raises a very interesting and relevant point. We are hesitant at this point to speculate on why we do not see a difference in variant repeats in ALT versus non-ALT cells, since additional data would be needed. One possibility is that variant repeats in ALT cells accumulate stochastically within telomeres but are selected against when they are present at the terminal portion of chromosome ends. However, to prove this hypothesis, we would need error-free long-read technology combined with END-seq. We feel that developing this approach would be beyond the scope of this manuscript.

(2) The authors also note that, in ALT cells, the frequency of VTRs in the first 30 nucleotides of the S1-END-SEQ reads is higher compared to END-SEQ, but this finding is not discussed either. Do the authors think that the presence of ssDNA regions is associated with the VTRs? Along this line, what is the frequency of VTRs in the END-SEQ analysis of TRF1-FokI-expressing ALT cells? Is it also increased? Has TRF1-FokI been applied to telomerase-expressing cells to compare VTR frequencies at internal sites between ALT and telomerase-expressing cells?

Similarly to what is discussed above, short reads have the advantage of being very accurate but do not provide sufficient length to establish the relative frequency of VTRs across the whole telomere sequence. The TRF1-FokI experiment is a good suggestion, but it would still be biased toward non-variant repeats due to the TRF1-binding properties. We plan to address these questions in a future study involving long-read sequencing and END-seq capture of telomeres.

Finally, in these experiments (S1-END-SEQ or END-SEQ in TRF1-Fok1), is the frequency of VTRs the same on both the C- and the G-rich strands? It is possible that the sequences are not fully complementary in regions where G4 structures form.

We thank the reviewer for this observation. While we do observe a higher frequency of variant telomeric repeats (VTRs) in the first 30 nucleotides of S1-END-seq reads compared to END-seq in ALT cells, we are currently unable to determine whether this difference is significant, as an appropriate control or matched normalization strategy for this comparison is lacking. Therefore, we refrain from overinterpreting the biological relevance of this observation.

The reviewer is absolutely correct. Our calculation did not exclude the possibility of extrachromosomal DNA as a source of telomeric ssDNA. We have now addressed this point in our discussion.

The reviewer is correct in pointing out that we still do not know what causes ssDNA at telomeres in ALT cells. Replication stress seems the most logical explanation based on the work of many labs in the field. However, our data did not reveal any significant difference in the levels of ssDNA at telomeres in non-ALT cells based on telomere length. We used the HeLa1.2.11 cell line (now clarified in the Materials section), which is the parental line of HeLa1.3 and has similarly long telomeres (~20 kb vs. ~23 kb). Despite their long telomeres and potential for replication-associated challenges such as G-quadruplex formation, HeLa1.2.11 cells did not exhibit the elevated levels of telomeric ssDNA that we observed in ALT cells (Figure 4B). Additional experiments are needed to map the occurrence of ssDNA at telomeres in relation to progression toward ALT.

(3) Based on the ratio of C-rich to G-rich reads in the S1-END-SEQ experiment, the authors estimate that ALT cells contain at least 3-5 ssDNA regions per chromosome end. While the calculation is understandable, this number could be discussed further to consider the possibility that the observed ratios (of roughly 0.5) might result from the presence of extrachromosomal DNA species, such as C-circles. The observed increase in the ratio of C-rich to G-rich reads in BLM-depleted cells supports this hypothesis, as BLM depletion suppresses C-circle formation in U2OS cells. To test this, the authors should examine the impact of POLD3 depletion on the C-rich/G-rich read ratio. Alternatively, they could separate high-molecular-weight (HMW) DNA from low-molecular-weight DNA in ALT cells and repeat the S1-END-SEQ in the HMW fraction.

The reviewer is absolutely correct. Our calculation did not exclude the possibility of extrachromosomal DNA as a source of telomeric ssDNA. We have now addressed this point in our discussion.

(4) What is the authors' perspective on the presence of ssDNA at ALT telomeres? Do they attribute this to replication stress? It would be helpful for the authors to repeat the S1-END-SEQ in telomerase-expressing cells with very long telomeres, such as HeLa1.3 cells, to determine if ssDNA is a specific feature of ALT cells or a result of replication stress. The increased abundance of G4 structures at telomeres in HeLa1.3 cells (as shown in J. Wong's lab) may indicate that replication stress is a factor. Similar to Wong's work, it would be valuable to compare the C-rich/G-rich read ratios in HeLa1.3 cells to those in ALT cells with similar telomeric DNA content.

The reviewer is correct in pointing out that we still do not know what causes ssDNA at telomeres in ALT cells. Replication stress seems the most logical explanation based on the work of many labs in the field. However, our data did not reveal any significant difference in the levels of ssDNA at telomeres in non-ALT cells based on telomere length. We used the HeLa1.2.11 cell line (now clarified in the Materials section), which is the parental line of HeLa1.3 and has similarly long telomeres (~20 kb vs. ~23 kb). Despite their long telomeres and potential for replication-associated challenges such as G-quadruplex formation, HeLa1.2.11 cells did not exhibit the elevated levels of telomeric ssDNA that we observed in ALT cells (Figure 4B). Additional experiments are needed to map the occurrence of ssDNA at telomeres in relation to progression toward ALT.

Finally, Reviewer #3 raises a list of minor points:

(1) The Y-axes of Figure 4 have been relabeled to account for the G-strand reads.

(2) Statistical analyses have been added to the figures where applicable.

(3) The manuscript has been carefully proofread to improve clarity and consistency throughout the text and figure legends

(4) We have revised the text to address issues related to the lack of cross-referencing between the supplementary figures and their corresponding legends.

Author Response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

Summary: 

Genome-wide association studies have been an important approach to identifying the genetic basis of human traits and diseases. Despite their successes, for many traits, a substantial amount of variation cannot be explained by genetic factors, indicating that environmental variation and individual 'noise' (stochastic differences as well as unaccounted for environmental variation) also play important roles. The authors' goal was to address whether gene expression variation in genetically identical individuals, driven by historical environmental differences and 'noise', could be used to predict reproductive trait differences. 

Strengths: 

To address this question, the authors took advantage of genetically identical C. elegans individuals to transcriptionally profile 180 adult hermaphrodite individuals that were also measured for two reproductive traits. A major strength of the paper is its experimental design. While experimenters aim to control the environment that each worm experiences, it is known that there are small differences that each worm experiences even when they are grown together on the same agar plate - e.g. the age of their mother, their temperature, the amount of food they eat, and the oxygen and carbon dioxide levels depending on where they roam on the plate. Instead of neglecting this unknown variation, the authors design the experiment up front to create two differences in the historical environment experienced by each worm: 1) the age of its mother and 2) 8 8-hour temperature difference, either 20 or 25 {degree sign}C. This helped the authors interpret the gene expression differences and trait expression differences that they observed. 

Using two statistical models, the authors measured the association of gene expression for 8824 genes with the two reproductive traits, considering both the level of expression and the historical environment experienced by each worm. Their data supports several conclusions. They convincingly show that gene expression differences are useful for predicting reproductive trait differences, predicting ~25-50% of the trait differences depending on the trait. Using RNAi, they also show that the genes they identify play a causal role in trait differences. Finally, they demonstrate an association with trait variation and the H3K27 trimethylation mark, suggesting that chromatin structure can be an important causal determinant of gene expression and trait variation. 

Overall, this work supports the use of gene expression data as an important intermediate for understanding complex traits. This approach is also useful as a starting point for other labs in studying their trait of interest. 

We thank the reviewer for their thorough articulation of the strengths of our study.  

Weaknesses: 

There are no major weaknesses that I have noted. Some important limitations of the work (that I believe the authors would agree with) are worth highlighting, however: 

(1) A large remaining question in the field of complex traits remains in splitting the role of non-genetic factors between environmental variation and stochastic noise. It is still an open question which role each of these factors plays in controlling the gene expression differences they measured between the individual worms. 

Yes, we agree that this is a major question in the field. In our study, we parse out differences driven between known historical environmental factors and unknown factors, but the ‘unknown factors’ could encompass both unknown environmental factors and stochastic noise.

(2) The ability of the authors to use gene expression to predict trait variation was strikingly different between the two traits they measured. For the early brood trait, 448 genes were statistically linked to the trait difference, while for egg-laying onset, only 11 genes were found. Similarly, the total R2 in the test set was ~50% vs. 25%. It is unclear why the differences occur, but this somewhat limits the generalizability of this approach to other traits. 

We agree that the difference in predictability between the two traits is interesting. A previous study from the Phillips lab measured developmental rate and fertility across Caenorhabditis species and parsed sources of variation (1). Results indicated that 83.3% of variation in developmental rate was explained by genetic variation, while only 4.8% was explained by individual variation. In contrast, for fertility, 63.3% of variation was driven by genetic variation and 23.3% was explained by individual variation. Our results, of course, focus only on predicting the individual differences, but not genetic differences, for these two traits using gene expression data. Considering both sets of results, one hypothesis is that we have more power to explain nongenetic phenotypic differences with molecular data if the trait is less heritable, which is something that could be formally interrogated with more traits across more strains.

(3) For technical reasons, this approach was limited to whole worm transcription. The role of tissue and celltype expression differences is important to the field, so this limitation is important. 

We agree with this assessment, and it is something we hope to address with future work.

Reviewer #2 (Public review): 

Summary: 

This paper measures associations between RNA transcript levels and important reproductive traits in the model organism C. elegans. The authors go beyond determining which gene expression differences underlie reproductive traits, but also (1) build a model that predicts these traits based on gene expression and (2) perform experiments to confirm that some transcript levels indeed affect reproductive traits. The clever study design allows the authors to determine which transcript levels impact reproductive traits, and also which transcriptional differences are driven by stochastic vs environmental differences. In sum, this is a rather comprehensive study that highlights the power of gene expression as a driver of phenotype, and also teases apart the various factors that affect the expression levels of important genes. 

Strengths: 

Overall, this study has many strengths, is very clearly communicated, and has no substantial weaknesses that I can point to. One question that emerges for me is about the extent to which these findings apply broadly. In other words, I wonder whether gene expression levels are predictive of other phenotypes in other organisms. I

think this question has largely been explored in microbes, where some studies (PMID: 17959824) but not others (PMID: 38895328) find that differences in gene expression are predictive of phenotypes like growth rate. Microbes are not the primary focus here, and instead, the discussion is mainly focused on using gene expression to predict health and disease phenotypes in humans. This feels a little complicated since humans have so many different tissues. Perhaps an area where this approach might be useful is in examining infectious single-cell populations (bacteria, tumors, fungi). But I suppose this idea might still work in humans, assuming the authors are thinking about targeting specific tissues for RNAseq. 

In sum, this is a great paper that really got me thinking about the predictive power of gene expression and where/when it could inform about (health-related) phenotypes. 

We thank the reviewer for recognizing the strengths of our study. We are also interested in determining the extent to which predictive gene expression differences operate in specific tissues.

Reviewer #3 (Public review): 

Summary: 

Webster et al. sought to understand if phenotypic variation in the absence of genetic variation can be predicted by variation in gene expression. To this end they quantified two reproductive traits, the onset of egg laying and early brood size in cohorts of genetically identical nematodes exposed to alternative ancestral (two maternal ages) and same generation life histories (either constant 20C temperature or 8-hour temperature shift to 25C upon hatching) in a two-factor design; then they profiled genome-wide gene expression in each individual. 

Using multiple statistical and machine learning approaches, they showed that, at least for early brood size, phenotypic variation can be quite well predicted by molecular variation, beyond what can be predicted by life history alone. 

Moreover, they provide some evidence that expression variation in some genes might be causally linked to phenotypic variation. 

Strengths: 

(1) Cleverly designed and carefully performed experiments that provide high-quality datasets useful for the community. 

(2) Good evidence that phenotypic variation can be predicted by molecular variation. 

We thank the reviewer for recognizing the strengths of our study.

Weaknesses:  

What drives the molecular variation that impacts phenotypic variation remains unknown. While the authors show that variation in expression of some genes might indeed be causal, it is still not clear how much of the molecular variation is a cause rather than a consequence of phenotypic variation. 

We agree that the drivers of molecular variation remain unknown. While we addressed one potential candidate (histone modifications), there is much to be done in this area of research. We agree that, while some gene expression differences cause phenotypic changes, other gene expression differences could in principle be downstream of phenotypic differences.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

I have a number of suggestions that I believe will improve the Methods section. 

(1) Strain N2-PD1073 will probably be confusing to some readers. I recommend spelling out that this is the Phillips lab version of N2.

Thank you for this suggestion; we have added additional explanation of this strain in the Methods.

(2) I found the details of the experimental design confusing, and I believe a supplemental figure will help. I have listed the following points that could be clarified: 

a. What were the biological replicates? How many worms per replicate?

Biological replicates were defined as experiments set up on different days (in this case, all biological replicates were at least a week apart), and the biological replicate of each worm can be found in Supplementary File 1 on the Phenotypic Data tab.

b. I believe that embryos and L4s were picked to create different aged P0s, and eggs and L4s were picked to separate plates? Is this correct?

Yes, this is correct.

c. What was the spread in the embryo age?

We assume this is asking about the age of the F1 embryos, and these were laid over the course of a 2-hour window.  

d. While the age of the parents is different, there are also features about their growth plates that will be impacted by the experimental design. For example, their pheromone exposure is different due to the role that age plays in the combination of ascarosides that are released. It is worth noting as my reading of the paper makes it seem that parental age is the only thing that matters.

The parents (P0) of different ages likely have differential ascaroside exposure because they are in the vicinity of other similarly aged worms, but the F1 progeny were exposed to their parents for only the 2-hour egg-laying window, in an attempt to minimize this type of effect as much as possible.  

e. Were incubators used for each temperature?

Yes.

f. In line 443, why approximately for the 18 hours? How much spread?

The approximation was based on the time interval between the 2-hour egg-laying window on Day 4 and the temperature shift on Day 5 the following morning. The timing was within 30 minutes of 18 hours either direction.

g.  In line 444, "continually left" is confusing. Does this mean left in the original incubator?

Yes, this means left in the incubator while the worms shifted to 25°C were moved. To avoid confusion, we re-worded this to state they “remained at 20°C while the other half were shifted to 25°C”.

h. In line 445, "all worms remained at 20 {degree sign}C" was confusing to me as to what it indicated. I assume, unless otherwise noted, the animals would not be moved to a new temperature.

This was an attempt to avoid confusion and emphasize that all worms were experiencing the same conditions for this part of the experiment.  

i. What size plates were the worms singled onto?

They were singled onto 6-cm plates.

j. If a figure were to be made, having two timelines (with respect to the P0 and F1) might be useful.

We believe the methods should be sufficient for someone who hopes to repeat the experiment, and we believe the schematic in Figure 1A labeling P0 and F1 generations is sufficient to illustrate the key features of the experimental design.

k. Not all eggs that are laid end up hatching. Are these censored from the number of progeny calculations?

Yes, only progeny that hatched and developed were counted for early brood.

(3) For the lysis, was the second transfer to dH20 also a wash step?

Yes.

(4) What was used for the Elution buffer?

We used elution buffer consisting of 10 mM Tris, 0.1 mM EDTA. We have added this to the “Cell lysate generation” section of the methods

(5) The company that produced the KAPA mRNA-seq prep kit should be listed.

We added that the kit was from Roche Sequencing Solutions.

(6) For the GO analysis - one potential issue is that the set of 8824 genes might also be restricted to specific GO categories. Was this controlled for?

We originally did not explicitly control for this and used the default enrichGO settings with OrgDB = org.Ce.eg.db as the background set for C. elegans. We have now repeated the analysis with the “universe” set to the 8824-gene background set. This did not qualitatively change the significant GO terms, though some have slightly higher or lower p-values. For comparison purposes, we have added the background-corrected sets to the GO_Terms tab of Supplementary File 1 with each of the three main gene groups appended with “BackgroundOf8824”.

Reviewer #2 (Recommendations for the authors): 

(1) The abstract, introduction, and experimental design are well thought through and very clear.

Thank you.

(2) Figure 1B could use a clearer or more intuitive label on the horizontal axis. The two examples help. Maybe the genes (points) on the left side should be blue to match Figure 1C, where the genes with a negative correlation are in the blue cluster.

Thank you for these suggestions. We re-labeled the x-axis as “Slope of early brood vs. gene expression (normalized by CPM)”, which we hope gives readers a better intuition of what the coefficient from the model is measuring. We also re-colored the points previously colored red in Figure 1B to be color-coded depending on the direction of association to match Figure 1C, so these points are now color-coded as pink and purple.  

(3) If red/blue are pos/neg correlated genes in 1C, perhaps different colors should be used to label ELO and brood in Figures 2 and 3. Green/purple?

We appreciate this point, but since we ended up using the cluster colors of pink and purple in Figure 1, we opted to leave Figures 2 and 3 alone with the early brood and ELO colorcoding of red and blue.

(4) I am unfamiliar with this type of beta values, but I thought the explanation and figure were very clear. It could be helpful to bold beta1 and beta2 in the top panels of Figure 2, so the readers are not searching around for those among all the other betas. It could also be helpful to add an English phrase to the vertical axes inFigures 2C and 2D, in addition to the beta1 and beta2. Something like "overall effect (beta1)" and"environment-controlled effect (beta2)". Or maybe "effect of environment + stochastic expression differences

(beta1)" and "effect of stochastic expression differences alone (beta2)". I guess those are probably too big to fit on the figure, but it might be nice to have a label somewhere on this figure connecting them to the key thing you are trying to measure - the effect of gene expression and environment.

Thank you for these suggestions. We increased the font sizes and bolded β1 and β2 in Figure 2A-B. In Figure 2C-D, we added a parenthetical under β1 to say “(env + noise)” and β2 to say “(noise)”. We agree that this should give the reader more intuition about what the β values are measuring.  

Reviewer #3 (Recommendations for the authors): 

The authors collected individuals 24 hours after the onset of egg laying for transcriptomic profiling. This is a well-designed experiment to control for the physiological age of the germline. However, this does not properly control for somatic physiological age. Somatic age can be partially uncoupled from germline age across individuals, and indeed, this can be due to differences in maternal age (Perez et al, 2017). This is because maternal age is associated with increased pheromone exposure (unless you properly controlled for it by moving worms to fresh plates), which causes a germline-specific developmental delay in the progeny, resulting in a delayed onset of egg production compared to somatic development (Perez et al. 2021). You control for germline age, therefore, it is likely that the progeny of day 1 mothers are actually somatically older than the progeny of day 3 mothers. This would predict that many genes identified in these analyses might just be somatic genes that increase or decrease their expression during the young adult stage. 

For example, the abundance of collagen genes among the genes negatively associated (including col-20, which is the gene most significantly associated with early brood) is a big red flag, as collagen genes are known to be changing dynamically with age. If variation in somatic vs germline age is indeed what is driving the expression variation of these genes, then the expectation is that their expression should decrease with age. Vice versa, genes positively associated with early brood that are simply explained by age should be increasing.  So I would suggest that the authors first check this using time series transcriptomic data covering the young adult stage they profiled. If this is indeed the case, I would then suggest using RAPToR ( https://github.com/LBMC/RAPToR ), a method that, using reference time series data, can estimate physiological age (including tissue-specific one) from gene expression. Using this method they can estimate the somatic physiological age of their samples, quantify the extent of variation in somatic age across individuals, quantify how much of the observed differences in expressions are explained just by differences in somatic age and correct for them during their transcriptomic analysis using the estimated soma age as a covariate (https://github.com/LBMC/RAPToR/blob/master/vignettes/RAPToR-DEcorrection-pdf.pdf). 

This should help enrich a molecular variation that is not simply driven by hidden differences between somatic and germline age. 

To first address some of the experimental details mentioned for our paper, parents were indeed moved to fresh plates where they were allowed to lay embryos for two hours and then removed. Thus, we believe this minimizes the effects of ascarosides as much as possible within our design. As shown in the paper, we also identified genes that were not driven by parental age and for all genes quantified to what extent each gene’s association was driven by parental age. Thus, it is unlikely that differences in somatic and germline age is the sole explanatory factor, even if it plays some role. We also note that we accounted for egg-laying onset timing in our experimental design, and early brood was calculated as the number of progeny laid in the first 24 hours of egg-laying, where egg-laying onset was scored for each individual worm to the hour. The plot of each worm’s ELO and early brood traits is in Figure S1. Nonetheless, we read the RAPToR paper with interest, as we highlighted in the paper that germline genes tend to be positively associated with early brood while somatic genes tend to be negatively associated. While the RAPToR paper discusses using tissue-specific gene sets to stage genetically diverse C. elegans RILs, the RAPToR reference itself was not built using gene expression data acquired from different C. elegans tissues and is based on whole worms, typically collected in bulk. I.e., age estimates in RILs differ depending on whether germline or somatic gene sets are used to estimate age when the the aging clock is based on N2 samples. Thus, it is unclear whether such an approach would work similarly to estimate age in single worm N2 samples. In addition, from what we can tell, the RAPToR R package appears to implement the overall age estimate, rather than using the tissue-specific gene sets used for RILs in the paper. Because RAPToR would be estimating the overall age of our samples using a reference that is based on fewer samples than we collected here, and because we already know the overall age of our samples measured using standard approaches, we believe that estimating the age with the package would not give very much additional insight.  

Bonferroni correction: 

First, I think there is some confusion in how the author report their p-values: I don't think the authors are using a cut-off of Bonferroni corrected p-value of 5.7 x 10-6 (it wouldn't make sense). It's more likely that they are using a Bonferroni corrected p of 0.05 or 0.1, which corresponds to a nominal p value of 5.7 x 10-6, am I right?

Yes, we used a nominal p-value of 5.7 x 10-6 to correspond to a Bonferroni-corrected p-value of 0.05, calculated as 0.05/8824. We have re-worded this wherever Bonferroni correction was mentioned.

Second, Bonferroni is an overly stringent correction method that has now been substituted by the more powerful Benjamini Hochberg method to control the false discovery rate. Using this might help find more genes and better characterize the molecular variation, especially the one associated with ELO?

We agree that Bonferroni is quite stringent and because we were focused on identifying true positives, we may have some false negatives. Because all nominal p-values are included in the supplement, it is straightforward for an interested reader to search the data to determine if a gene is significant at any other threshold.   

Minor comments: 

(1) "In our experiment, isogenic adult worms in a common environment (with distinct historical environments) exhibited a range of both ELO and early brood trait values (Fig S1A)" I think this and the figure is not really needed, Figure S1B is already enough to show the range of the phenotypes and how much variation is driven by the life history traits.

We agree that the information in S1A is also included in S1B, but we think it is a little more straightforward if one is primarily interested in viewing the distribution for a single trait.

(2) Line 105 It should be Figure S2, not S3.

Thank you for catching this mistake.

(3) Gene Ontology on positive and negatively associated genes together: what about splitting the positive and negative?

We have added a split of positive and negative GO terms to the GO_Terms tab of Supplement File 1. Broadly speaking, the most enriched positively associated genes have many of the same GO terms found on the combined list that are germline related (e.g., involved in oogenesis and gamete generation), whereas the most enriched negatively associated genes have GO terms found on the combined list that are related to somatic tissues (e.g., actin cytoskeleton organization, muscle cell development). This is consistent with the pattern we see for somatic and germline genes shown in Figure 4.

(4) A lot of muscle-related GOs, can you elaborate on that?

Yes, there are several muscle-related GOs in addition to germline and epidermis. While we do not know exactly why from a mechanistic perspective these muscle-related terms are enriched, it may be important to note that many of these terms have highly overlapping sets of genes which are listed in Supplementary File 1. For example, “muscle system process” and “muscle contraction” have the exact same set of 15 genes causing the term to be significantly enriched. Thus, we tend to not interpret having many GO terms on a given tissue as indicating that the tissue is more important than others for a given biological process. While it is clear there are genes related to muscle that are associated with early brood, it is not yet clear that the tissue is more important than others.  

(5) "consistent with maternal age affecting mitochondrial gene expression in progeny " - has this been previously reported?

We do not believe this particular observation has been reported. It is important to note that these genes are involved in mitochondrial processes, but are expressed from the nuclear rather than mitochondrial genome. We re-worded the quoted portion of the sentence to say “consistent with parental age affecting mitochondria-related gene expression in progeny”.

(6) PCA: "Therefore, the optimal number of PCs occurs at the inflection points of the graph, which is after only7 PCs for early brood (R2 of 0.55) but 28 PCs for ELO (R2 of 0.56)." 

Not clear how this is determined: just graphically? If yes, there are several inflection points in the plot. How did you choose which one to consider? Also, a smaller component is not necessarily less predictive of phenotypic variation (as you can see from the graph), so instead of subsequently adding components based on the variance, they explain the transcriptomic data, you might add them based on the variance they explain in the phenotypic data? To this end, have you tried partial least square regression instead of PCA? This should give gene expression components that are ranked based on how much phenotypic variance they explain.  

Thank you for this thoughtful comment. We agree that, unlike for Figure 3B, there is some interpretation involved on how many PCs is optimal because additional variance explained with each PC is not strictly decreasing beyond a certain number of PCs. Our assessment was therefore made both graphically and by looking at the additional variance explained with each additional PC. For example, for early brood, there was no PC after PC7 that added more than 0.04 to the R2. We could also have plotted early brood and ELO separately and had a different ordering of PCs on the x-axis. By plotting the data this way, we emphasized that the factors that explain the most variation in the gene expression data typically explain most variation in the phenotypic data.  

(7) The fact that there are 7 PC of molecular variation that explain early brood is interesting. I think the authors can analyze this further. For example, could you perform separate GO enrichment for each component that explains a sizable amount of phenotypic variance? Same for the ELO.  

Because each gene has a PC loading in for each PC, and each PC lacks the explanatory power of combined PCs, we believe doing GO Terms on the list of genes that contribute most to each PC is of minimal utility. The power of the PCA prediction approach is that it uses the entire transcriptome, but the other side of the coin is that it is perhaps less useful to do a gene-bygene based analysis with PCA. This is why we separately performed individual gene associations and 10-gene predictive analyses. However, we have added the PC loadings for all genes and all PCs to Supplementary File 1.

(8) Avoid acronyms when possible (i.e. ELO in figures and figure legends could be spelled out to improve readability).

We appreciate this point, but because we introduced the acronym both in Figure 1 and the text and use it frequently, we believe the reader will understand this acronym. Because it is sometimes needed (especially in dense figures), we think it is best to use it consistently throughout the paper.

(9) Multiple regression: I see the most selected gene is col-20, which is also the most significantly differentially expressed from the linear mixed model (LMM). But what is the overlap between the top 300 genes in Figure 3F and the 448 identified by the LMM? And how much is the overlap in GO enrichment?

Genes that showed up in at least 4 out of 500 iterations were selected more often than expected by chance, which includes 246 genes (as indicated by the red line in Figure 3F). Of these genes, 66 genes (27%) are found in the set of 448 early brood genes. The proportion of overlap increases as the number of iterations required to consider a gene predictive increases, e.g., 34% of genes found in 5 of 500 iterations and 59% of genes found in 10 of 500 iterations overlap with the 448 early brood genes. However, likely because of the approach to identify groups of 10 genes that are predictive, we do not find significant GO terms among the 246 genes identified with this approach after multiple test correction. We think this makes sense because the LMM identifies genes that are individually associated with early brood, whereas each subsequent gene included in multiple regression affects early brood after controlling for all previous genes. These additional genes added to the multiple regression are unlikely to have similar patterns as genes that are individually correlated with early brood.  

(10) Elastic nets: prediction power is similar or better than multiple regression, but what is the overlap between genes selected by the elastic net (not presented if I am not mistaken) and multiple regression and the linear mixed model?

For the elastic net models, we used a leave-one-out cross validation approach, meaning there were separate models fit by leaving out the trait data for each worm, training a model using the trait data and transcriptomic data for the other worms, and using the transcriptomic data of the remaining worm to predict the trait data. By repeating this for each worm, the regressions shown in the paper were obtained. Each of these models therefore has its own set of genes. Of the 180 models for early brood, the median model selects 83 genes (range from 72 to 114 genes). Across all models, 217 genes were selected at least once. Interestingly, there was a clear bimodal distribution in terms of how many models a given gene was selected for: 68 genes were selected in over 160 out of 180 models, while 114 genes were selected in fewer than 20 models (and 45 genes were selected only once). Therefore, we consider the set of 68 genes as highly robustly selected, since they were selected in the vast majority of models. This set of 68 exhibits substantial overlap with both the set of 448 early brood-associated genes (43 genes or 63% overlap) and the multiple regression set of 246 genes (54 genes or 79% overlap). For ELO, the median model selected 136 genes (range of 96 to 249 genes) and a total of 514 genes were selected at least once. The distribution for ELO was also bimodal with 78 genes selected over 160 times and 255 genes selected fewer than 20 times. This set of 78 included 6 of the 11 significant ELO genes identified in the LMM.  We have added tabs to Supplementary File 1 that include the list of genes selected for the elastic net models as well as a count of how many times they were selected out of 180 models.

(11) In other words, do these different approaches yield similar sets of genes, or are there some differences?

In the end, which approach is actually giving the best predictive power? From the perspective of R2, both the multiple regression and elastic net models are similarly predictive for early brood, but elastic net is more predictive for ELO. However, in presenting multiple approaches, part of our goal was identifying predictive genes that could be considered the ‘best’ in different contexts. The multiple regression was set to identify exactly 10 genes, whereas the elastic net model determined the optimal number of genes to include, which was always over 70 genes. Thus, the elastic net model is likely better if one has gene expression data for the entire transcriptome, whereas the multiple regression genes are likely more useful if one were to use reporters or qRTPCR to measure a more limited number of genes.  

(12) Line 252: "Within this curated set, genes causally affected early brood in 5 of 7 cases compared to empty vector (Figure 4A).

" It seems to me 4 out of 7 from Figure 4A. In Figure 4A the five genes are (1) cin-4, (2) puf5; puf-7, (3) eef-1A.2, (4) C34C12.8, and (5) tir-1. We did not count nex-2 (p = 0.10) or gly-13 (p = 0.07), and empty vector is the control.

(13) Do puf-5 and -7 affect total brood size or only early brood size? Not clear. What's the effect of single puf-5 and puf-7 RNAi on brood?

We only measured early brood in this paper, but a previous report found that puf-5 and puf-7 act redundantly to affect oogenesis, and RNAi is only effective if both are knocked down together(2). We performed pilot experiments to confirm that this was the case in our hands as well.  

(14)  To truly understand if the noise in expression of Puf-5 and /or -7 really causes some of the observed difference in early brood, could the author use a reporter and dose response RNAi to reduce the level of puf-5/7 to match the lower physiological noise range and observe if the magnitude of the reduction of early brood by the right amount of RNAi indeed matches the observed physiological "noise" effect of puf-5/7 on early brood?

We agree that it would be interesting to do the dose response of RNAi, measure early brood, and get a readout of mRNA levels to determine the true extent of gene knockdown in each worm (since RNAi can be noisy) and whether this corresponds to early brood when the knockdown is at physiological levels. While we believe we have shown that a dose response of gene knockdown results in a dose response of early brood, this additional analysis would be of interest for future experiments.

(15) Regulated soma genes (enriched in H3K27me3) are negatively correlated with early brood. What would be the mechanism there? As mentioned before, it is more likely that these genes are just indicative of variation in somatic vs germline age (maybe due to latent differences in parental perception of pheromone).

We can think of a few potential mechanisms/explanations, but at this point we do not have a decisive answer. Regulated somatic genes marked with H3K27me3 (facultative heterochromatin) are expressed in particular tissues and/or at particular times in development. In this study and others, genes marked with H3K27me3 exhibit more gene expression noise than genes with other marks. This could suggest that there are negative consequences for the animal if genes are expressed at higher levels at the wrong time or place, and one interpretation of the negative association is that higher expressed somatic genes results in lower fitness (where early brood is a proxy for fitness). Another related interpretation is that there are tradeoffs between somatic and germline development and each individual animal lands somewhere on a continuum between prioritizing germline or somatic development, where prioritizing somatic integrity (e.g. higher expression of somatic genes) comes at a cost to the germline resulting in fewer progeny. Additional experiments, including measurements of histone marks in worms measured for the early brood trait, would likely be required to more decisively answer this question.  

(16) Line 151: "Among significant genes for both traits, β2 values were consistently lower than β1 (Figures 2CD), suggesting some of the total effect size was driven by environmental history rather than pure noise".

We are interpreting this quote as part of point 17 below.

(17) It looks like most of the genes associated with phenotypes from the univariate model have a decreased effect once you account for life history, but have you checked for cases where the life history actually masks the effect of a gene? In other words, do you have cases where the effect of gene expression on a phenotype is only (or more) significant after you account for the effect of life history (β2 values higher than β1)?

This is a good question and one that we did not explicitly address in the paper because we focused on beta values for genes that were significant in the univariate analysis. Indeed, for the sets of 448 early brood genes ad 11 ELO genes, there are no genes for which β2 is larger than β1. In looking at the larger dataset of 8824 genes, with a Bonferroni-corrected p-value of 0.05, there are 306 genes with a significant β2 for early brood. The majority (157 genes) overlap with the 448 genes significant in the univariate analysis and do not have a higher β2 than β1. Of the remaining genes, 72 of these have a larger β2 than β1. However, in most cases, this difference is relatively small (median difference of 0.025) and likely insignificant. There are only three genes in which β1 is not nominally significant, and these are the three genes with the largest difference between β1 and β2 with β2 being larger (differences of 0.166, 0.155, and 0.12). In contrast, the median difference between β1 and β2 the 448 genes (in which β1 is larger) is 0.17, highlighting the most extreme examples of β2 > β1 are smaller in magnitude than the typical case of β1 > β2. For ELO, there are no notable cases where β2 > β1. There are eight genes with a significant β2 value, and all of these have a β1 value that is nominally significant. Therefore, while this phenomenon does occur, we find it to be relatively rare overall. For completeness, we have added the β1 and β2 values for all 8824 genes as a tab in Supplementary File 1.

Author Response:

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

Reviewer #1 (Public Review):

Summary: Zhu et al., investigate the cellular defects in glia as a result of loss in DEGS1/ifc encoding the dihydroceramide desaturase. Using the strength of Drosophila and its vast genetic toolkit, they find that DEGS1/ifc is mainly expressed in glia and its loss leads to profound neurodegeneration. This supports a role for DEGS1 in the developing larval brain as it safeguards proper CNS development. Loss of DEGS1/ifc leads to dihydroceramide accumulation in the CNS and induces alteration in the morphology of glial subtypes and a reduction in glial number. Cortex and ensheathing glia appeared swollen and accumulated internal membranes. Astrocyte-glia on the other hand displayed small cell bodies, reduced membrane extension and disrupted organization in the dorsal ventral nerve cord. They also found that DEGS1/ifc localizes primarily to the ER. Interestingly, the authors observed that loss of DEGS1/ifc drives ER expansion and reduced TGs and lipid droplet numbers. No effect on PC and PE and a slight increase in PS.

The conclusions of this paper are well supported by the data. The study could be further strengthened by a few additional controls and/or analyses.

Strengths:

This is an interesting study that provides new insight into the role of ceramide metabolism in neurodegeneration.

The strength of the paper is the generation of LOF lines, the insertion of transgenes and the use of the UAS-GAL4/GAL80 system to assess the cell-autonomous effect of DEGS1/ifc loss in neurons and different glial subtypes during CNS development.

The imaging, immunofluorescence staining and EM of the larval brain and the use of the optical lobe and the nerve cord as a readout are very robust and nicely done.

Drosophila is a difficult model to perform core biochemistry and lipidomics but the authors used the whole larvae and CNS to uncover global changes in mRNA levels related to lipogenesis and the unfolded protein responses as well as specific lipid alterations upon DEGS1/ifc loss.

Weaknesses:

(1) The authors performed lipidomics and RTqPCR on whole larvae and larval CNS from which it is impossible to define the cell type-specific effects. Ideally, this could be further supported by performing single cell RNAseq on larval brains to tease apart the cell-type specific effect of DEGS1/ifc loss.

We agree that using scRNAseq or pairing FACS-sorting of individual glial subtypes with bulk RNAseq would help tease apart the cell-type specific effects of DEGS1/ifc loss on glial cells. At this time, however, this approach extends beyond the scope of the current paper and means of the lab. 

(2) It's clear from the data that the accumulation of dihydroceramide in the ER triggers ER expansion but it remains unclear how or why this happens. Additionally, the authors assume that, because of the reduction in LD numbers, that the source of fatty acids comes from the LDs. But there is no data testing this directly.

As CERT, the protein that transports ceramide from the ER to the Golgi, is far more efficient at transporting ceramide than dihydroceramide, we speculate that dihydroceramide accumulates in the ER due to inefficient transport from the ER to the Golgi by CERT. We state this model more explicitly in the results under the subheading “Reduction of dihydroceramide synthesis suppresses the ifc CNS phenotype”.

We agree with the point on lipid droplet. We observe a correlation, not a causation, between reduction of lipid droplets and a large expansion of ER membrane. We have tried to clarify the text in the last paragraph of the discussion to make this point more clearly. See also response to reviewer 2 point 3. 

(3) The authors performed a beautiful EMS screen identifying several LOF alleles in ifc. However, the authors decided to only use KO/ifcJS3. The paper could be strengthened if the authors could replicate some of the key findings in additional fly lines.

We agree. We replicated the observed cortex glia swelling, ER expansion in cortex glia, and observed increase in neuronal cell death markers in late-third instar larvae mutant for either the ifcjs1 or ifcjs2 allele. These data are now provided as Supplementary Figure 7.

(4) The authors use M{3xP3-RFP.attP}ZH-51D transgene as a general glial marker. However, it would be advised to show the % overlap between the glial marker and the RFP since a lot of cells are green positive but not per se RFP positive and vice versa.

We visually reexamined the expression of the 3xP3 RFP transgene relative to FABP labeling for cortex glia, Ebony for astrocyte-like glia, and the Myr-GFP transgene driven by glial-subtype specific GAL4 driver lines for perineurial, subperineurial, and ensheathing glia. We note that RFP localizes to the nucleus cytoplasm while FABP and Ebony localize to the cytoplasm and Myr-GFP to the cell membrane. Thus, an observed lack of overlap of expression between RFP and the other markers can arise to differential localization of the two markers in the same cells (see, for example, Fig. S2D where Myr-GFP expression in the nuclear envelope encircles that of RFP in the nucleus. Through visual inspection of five larval-brain complexes for each glial subtype marker, we found that essentially all cortex, SPG, and ensheathing glia expressed RFP. Similarly, nearly all astrocyte-like glia also expressed RFP, but they expressed RFP at significantly lower levels than that observed for cortex, SPG, or ensheathing glia. This analysis also confirmed that most perineurial glia do not express RFP. The 3xP3 M{3xP3-RFP.attP}ZH-51D transgene then labels most glia in the Drosophila CNS. We have added text to Supplementary Figure 2 noting the above observations as to which glial cells express RFP. 

(5) The authors indicate that other 3xP3 RFP and GFP transgenes at other genomic locations also label most glia in the CNS. Do they have a preferential overlap with the different glial subtypes?

We assessed three different types of 3xP3 RFP and GFP transgenes: M{3xP3RFP.attp} transgenes (n=4), Mi{GFP[E.3xP3]=ET1} transgenes (n=3), and

Tl{GFP[3xP3.cLa]=CRIMIC.TG4} transgenes (n>6). All labeled cortex glia, but different lines exhibited differential labeling of astrocyte and ensheathing glia. These data are now included as Supplementary Figure 3.

Reviewer #2 (Public Review):

Summary:

The manuscript by Zhu et al. describes phenotypes associated with the loss of the gene ifc using a Drosophila model. The authors suggest their findings are relevant to understanding the molecular underpinnings of a neurodegenerative disorder, HLD-18, which is caused by mutations in the human ortholog of ifc, DEGS1.

The work begins with the authors describing the role for ifc during fly larval brain development, demonstrating its function in regulating developmental timing, brain size, and ventral nerve cord elongation. Further mechanistic examination revealed that loss of ifc leads to depleted cellular ceramide levels as well as dihydroceramide accumulation, eventually causing defects in ER morphology and function. Importantly, the authors showed that ifc is predominantly expressed in glia and is critical for maintaining appropriate glial cell numbers and morphology. Many of the key phenotypes caused by the loss of fly ifc can be rescued by overexpression of human DEGS1 in glia, demonstrating the conserved nature of these proteins as well as the pathways they regulate. Interestingly, the authors discovered that the loss of lipid droplet formation in ifc mutant larvae within the cortex glia, presumably driving the deficits in glial wrapping around axons and subsequent neurodegeneration, potentially shedding light on mechanisms of HLD-18 and related disorders.

Strengths:

Overall, the manuscript is thorough in its analysis of ifc function and mechanism. The data images are high quality, the experiments are well controlled, and the writing is clear.

Weaknesses:

(1) The authors clearly demonstrated a reduction in number of glia in the larval brains of ifc mutant flies. What remains unclear is whether ifc loss leads to glial apoptosis or a failure for glia to proliferate during development. The authors should distinguish between these two hypotheses using apoptotic markers and cell proliferation markers in glia.