If CRP is just about making lesson relatable to diverse students why do you think people get so defensive when schools announce they are doing CRP?

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

Learn more at Review Commons

Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

The last several years have seen major advances in our understanding of the basic cell biology of the set of single cell animal relatives, led by the authors and their colleagues. These groups have developed several as models and pioneered remarkable microscopy approaches to examine their cell biology. Here the authors extend this work to the ichthyosporean Sphaeroforma arctica, exploring the fascinating process by which a syncytial life stage cellularizes, and seeking to define the role of microtubules and Golgi trafficking. Their new expansion microscopy delivers impressive images of membrane and the cytoskeleton during this process and has the promise of answering important questions about the roles of microtubules and membrane trafficking. I thus went into my review quite excited. However, as I detail below, while some aspects of the process are carefully quantified, the current manuscript draws multiple broad conclusions that do not seem fully supported by the limited data provided. This substantially reduced my enthusiasm. I'd also note, though I did not take this into account in my evaluation, that many of the images are presented at a size that was difficult to interpret, without my electronically enlarging them, and two of the Figures were mis-labeled.

The general points raised here are dealt with below. All panels in the main figures are enlarged, zoom-ins are added where they help, and figures that are no longer fitted have been moved to the supplementary figures. Panel labelling has been checked throughout, the two mislabelled figures are corrected, and the labelling is now consistent across the whole figure set. The additional quantification and the associated framework is set out under comment 2.

1. Interpreting most of their Figures requires understanding the basics of cellularization in this organism. Comparing the diagram in Fig. 1B and the images in 1C left me confused. First, are all the images in 1C and similar images later cross sections? Are nuclei dispersed throughout the cytoplasm at the start or restricted to a region near the cortex. If the former, how do more central nuclei get cellularized? The transition from the unperturbed 20 and 40 minute timepoints left me unclear on the normal process. Panel G may have been helpful in this regard but only shows the treated embryo and no untreated one.

This comment identified a real shortcoming in how we presented the system, and it prompted the largest single change to the text of the revised manuscript. In writing the original version we took the basic description of cellularization in S. arctica largely for granted, since it has been built up across several previous studies (Dudin et al. 2019, Ondracka et al. 2018, Olivetta et al. 2023 and Shah et al. 2024), and we did not restate it for a reader arriving at the organism for the first time. We have addressed this on three fronts: the imaging planes, the referee's question about nuclei, and the introduction.

On the images themselves (Figure 1), these panels and the equivalent images throughout the manuscript are equatorial mid-sections. The imaging plane is now explicitly stated in every figure legend, so that single slices, equatorial mid-sections, and maximum-intensity projections can no longer be confused with one another. More usefully, we have added Figure EV1A, which shows an untreated cellularizing coenocyte as both a top view and an equatorial mid-section, at the onset of invagination and 10 minutes later, each at low and high contrast. Figure EV1A makes the two geometries directly comparable, rather than leaving the reader to reconcile the schematic in Figure 1C with a single plane, and it also provides the untreated counterpart to Figure 1G that the referee requested at the end of this comment. All parameters of cellularization measure in the study are now indicated on the sketch in Figure 1C.

Figure Legend EV1A: (A) Cellularizing control S. arctica coenocytes labelled with FM4-64, shown as a top view and an equatorial mid-section at the onset of invagination (0 min) and 10 min later, each at low and high contrast display. Nuclei are visible as dye-excluded regions (asterisks). Scale bar, 10 µm.

We would add that an untreated comparison was in fact already available, since Movie EV1 runs a control and an MBC-treated coenocyte side by side through the whole of cellularization at 10-minute intervals. We accept that this was not where the referee would naturally have looked for it, and Figure EV1A now places the comparison in the figures themselves.

On the referee's central question, we can be unambiguous. Nuclei are not dispersed throughout the cytoplasm From the coenocytic phase through to cellularization, they remain associated with the cortex, and this has been established consistently across the previous work cited above. There are therefore no central nuclei in controls, and the question of how they would be enclosed does not arise. We recognize, however, that the original manuscript never stated this outright, and that a reader had no way of knowing it, and the referee was right to ask. The revised text now says it explicitly and follows it with the geometric consequence.

Line 70-72: Nuclei divide synchronously and rather than occupying the interior of the coenocyte, associate with the cortex, evenly spacing out along the surface.

Line 78-82: Recent work has shown that S. arctica cellularization is regulated by the nucleocytoplasmic (N/C) ratio, with cellularization timing tightly coupled to nuclear content relative to cytoplasmic volume. Invaginations initiate at the cell periphery, between adjacent cortical nuclei, and advance inward, carving compartments from the cortex around each nucleus rather than assembling them from the cell interior.

Finally, the introduction has been substantially expanded so that the process is defined prior to the figures. It now sets out the coenocytic phase, the arrangement of nuclei at the cortex, the direction in which invaginations progress, and the stages through to the end of cellularization, drawing explicitly on the previous characterisations that the original manuscript had assumed the reader would already know. This also addresses the referee's difficulty with the transition between the unperturbed timepoints, which we had described without first establishing what the normal sequence is.

The authors make a number of conclusions in Figure 1. Some are carefully quantified but others are not. For example, they state "producing uncoordinated ingression with variable rates, diagonal trajectories, and occasional bifurcations, in contrast to the uniform, perpendicular furrows observed in controls". I was not convinced by the single images provided that these were different-for example, spacing in the unperturbed 10 minute time point seems variable and furrows are not "uniformly perpendicular" in the unperturbed 20 minute time point. I also was puzzled by the lack of change in nuclear spacing while furrow spacing was altered. Later on in this section they state "MBC-treated coenocytes displayed significantly decreased and irregular furrow spacing, resulting in some compartments lacking nuclei entirely (Figure 1G & H)", but none of these images visualize nuclei directly-Perhaps the lower level background in H is supposed to indicate this but no parallel wildtype image is shown. Finally, while their TEM images (in the panels that are either I or J due to mislabeling) are lovely, I was not sure what to conclude from them- only the unperturbed images show the embryo surface for orientation and the lefthand unperturbed image is not as straight as they suggest-I certainly don't think these few images support their strong, detailed conclusions here: "MBC treatment resulted in aberrant membrane architecture, with furrows exhibiting bifurcated and convoluted morphology and abnormal fusion at the base of invagination, compared to the smooth, organized structure of control furrows".

We have considerably expanded both the range and the amount of quantification in the revised manuscript, and every quantity we measure is now sketched out in Figure 1C. These measurements are organised around the four properties of cellularization that the revised manuscript is built on:

1. Nuclear organisation, measured as inter-nuclear distance and its variability within a coenocyte (Figure EV1G and Figure 1F).
2. Furrow positioning, measured as furrow spacing, its variability within a coenocyte, and the deviation of the invagination axis from perpendicular to the cortex (Figure 1H, Figure EV1H and Figure EV1I).
3. Furrow ingression dynamics, measured as ingression rate, its variability, the maximum length furrows reach, its variability, and the duration of cellularization from the onset of invagination to Flip (Figure 1E and Figure EV1B-F).
4. Developmental outcome, measured as the variability of released cell size (Figure EV1J). The same set of measurements is now applied to every perturbation in the manuscript, so that microtubule depolymerization, centrifugal displacement of nuclei and disruption of membrane trafficking are each characterised against the same quantities rather than described in their own terms. Applied across the whole dataset, these measurements answer the referee's objections directly.

The descriptors they quote were asserted from single images rather than measured. We have deleted "diagonal trajectories", "occasional bifurcations" and "uniform, perpendicular" from the manuscript, and what remains is carried by measurement.

Line 113-115: MT loss disrupted furrow ingression dynamics, producing uncoordinated ingression - in contrast to the consistent furrows observed in controls (Fig. 1D, Movie EV1).

Coordination is now measured within single coenocytes, so that furrows are compared against their own neighbours rather than across the population. This is the comparison the referee implies when looking at a single image and asking whether the furrows within it differ. It is now Figure EV1D.

Figure Legend EV1D: (C) Variability of furrow ingression rate within a coenocyte, from the rates in (B). DMSO 0.053, MBC 0.111, p = 0.014.

Perpendicularity is measured in Figure EV1L, on ten furrows per coenocyte at matched ingression depth between conditions. This concedes the referee's specific point: control furrows are not uniformly perpendicular, and deviate by 5.51 degrees on average. We claim only that treated coenocytes deviate roughly twice as far.

Figure Legend EV1I: (I) Deviation of the invagination axis from perpendicular to the cortex, |angle - 90|, averaged per coenocyte. DMSO 5.51 degrees (n=5), MBC 10.83 degrees (n=4), Ten furrows per coenocyte; p = 0.016. Ingression depth did not differ between conditions.

On the referee's puzzlement about nuclear spacing, they have identified something we had underplayed. Mean inter-nuclear spacing genuinely does not change, and we do not claim that it does. What changes is its regularity, which roughly doubles. The same pattern recurs for furrow spacing, for the length furrows reach, for ingression rate and for the size of the cells finally released, and it is why the manuscript always argued that microtubules sustain the fidelity of cellularization rather than its execution. However, now it's strengthened by numerical data.

Line 156-159: While mean inter-nuclear spacing was not significantly different between conditions (6.15 vs 6.22 μm, Fig. EV1G), MBC-treated coenocytes exhibited dramatically increased variability in nuclear positioning (0.143 vs 0.268, Fig. 1F), with nuclei ranging from properly positioned to severely mislocalized.

On the visualisation of nuclei, we would push back in part. Nuclei are directly visible in FM4-64 as regions from which the dye is excluded, and this is how they were scored throughout; the approach is not introduced here and was used in this same organism in Olivetta and Dudin (2023). We accept that this was never explained and that the display contrast made it difficult to see. The Methods now state the scoring explicitly; Figure EV1A and Figure EV3D show coenocytes at both low and high display contrast, and nuclei are marked with asterisks.

Figure legend EV1: (A) Cellularizing control S. arctica coenocytes labelled with FM4-64, shown as a top view and an equatorial mid-section at the onset of invagination (0 min) and 10 min later, each at low and high contrast display. Nuclei are visible as dye-excluded regions (asterisks). Scale bar, 10 µm.

Line 272-274: Throughout these experiments nuclei are resolved in single optical sections as regions from which FM4-64 is excluded and are visible as such at both low and high display contrast (Fig. EV3D).

The claim about compartment contents has also been moved to data where nuclei are directly labelled rather than inferred. The statement that some compartments lacked nuclei is removed from the furrow spacing sentence, and the observation is now made on U-ExM with a DNA stain, in Figure EV2C and Movie EV5, where it is made on a single section and on the full volume rather than on a projection.

Figure EV2C: (C) Two MBC-treated coenocytes: a maximum intensity projection of 50 consecutive z-sections (left) and a single z-section of a second coenocyte (right). Tubulin signals persist around a subset of nuclei after MT depolymerization, and individual compartments enclose more than one nucleus. This observation is made on the single section and on the full volume in Movie EV5, not on the projection, since nuclei at different depths overlap in projection. Scale bar, 10 µm. Scale bars are adjusted for expansion factors.

The mislabelled panels have been corrected throughout, and we thank the referee for catching them.

TEM images of furrows with visible cell surface marked as yellow asterisks are now included in the main figure. Additional images of furrows (furrow 3 and 4) and zoom-ins of the convoluted membrane at the tip are now included in the supplementary Figure EV1K,L. These are representative images selected from DMSO (n = 25 furrows from 34 tomograms, with cell surface seen in 19), MBC (n = 67 furrows from 72 tomograms, with cell surface visible in 37), total 106 tomograms imaged across different cellularization stages and conditions. This information is now included in the legend of Figure 1J. TEM images of DMSO and MBC-treated full cells are provided in EV1K to provide an overview of furrow consistency in the two conditions. Nuclei are labelled with N to indicate nuclei per compartment.

The images in Fig. 2B are remarkable and very informative, though as I note above they are presented at such a small size that they require considerable enlargement to appreciate. The surprising accumulation of actin at the invagination front, presumably long before membrane closure begins, was striking, as were the microtubule baskets. However, conclusions drawn again seemed too strong. The authors state "High magnification views further supported that these bundles closely tracked the advancing furrow fronts, with longer MT extensions associated with deeper furrows during later stages (Figure 2D, arrowheads)" (BTW once again this Figure was not labeled in parallel with the text-should be 2C). I did not think the NHS staining provided sufficient resolution of advancing furrow fronts to draw this conclusion. They end this section with some more detailed conclusions, which did not seem to me to be well supported by the single image shown: "Furrows were often misaligned, and compartments frequently enclosed multiple nuclei or, conversely, lacked nuclei entirely. In several cases, nuclei were observed trailing between furrows or located beneath partially formed compartments, suggesting that improper nuclear positioning may interfere with furrow progression and sealing (Figure 2F)." The latter conclusion also seemed to leave me wondering about cause and effect. The final sweeping conclusions in the paragraph on p. 7 top (next time please include page numbers) thus seemed much too broad.

The descriptive claim has been replaced by a measurement made across the whole dataset, and the causal claim has been removed altogether.

On presentation, all panels in Figure 2 are enlarged in the revised version. We have also added zoom-ins on a forming compartment in Figure EV2A, and a second late-stage example shown as single channels and merge in Figure EV2B, so that the relationship between the microtubule network and the invaginating membrane can be inspected at a useful magnification rather than inferred from a small panel.

The sentence the referee quotes has been deleted. Their objection is well founded, since we were reading furrow fronts off the pan-labelling and then drawing a quantitative conclusion about depth from it. In its place, the relationship between microtubule length and furrow depth is now measured directly and reported as a correlation across 68 coenocytes, and we state explicitly what that correlation does not establish.

Line 209-214: Quantitative analysis of MT networks showed that -MT length scaled with furrow depth (Spearman rho = 0.709, p = 1.3 × 10⁻¹¹, n = 68 coenocytes), consistent with MTs elongating in coordination with plasma membrane invagination (Figs. 2E,F). While this correlation suggests a role for MTs in furrow progression, it remains unclear whether this involves active polymerization at the furrow front or utilization of pre-formed MT tracks.

On the second part quoted, the speculation that improper nuclear positioning may interfere with furrow progression and sealing has been removed. This addresses the point about cause and effect directly, since we cannot separate the two from these data and we no longer imply that we can. As set out in our response to comment 2, the claim that compartments lacked nuclei is also removed, and what remains of that observation now rests on Figure EV2C and Movie EV5 rather than on a single image, so we do not repeat it here.

Line 218-221: Furrows were often misaligned, and individual compartments were observed to enclose more than one nucleus (Fig. EV2C, Movie EV5). Nuclei were also seen trailing between furrows or lying beneath partially formed compartments (Movie EV5).

The panel that should have been cited as Figure 2C is corrected, as part of the labelling pass described under comment 2, and the callouts have been checked so that each panel is cited in the order of its lettering. Line numbers are included in this revised version, as the referee requests.

Finally, in the closing paragraph of the section, we accept that it drew broader conclusions than the data in that section carried. It has been rewritten so that each claim is tied either to a specific measurement or to a named comparison with another system, and the section now ends on the comparison between our two titratable perturbations across ten measurements in Figure 4F rather than on a general statement about cytoskeletal coordination.

I thought the use of centrifugation to move nuclei was clever. However, it also is moving many other things-for example it moves whatever organelles are labeled by BODIPY and apparently nuclear associated MTOCs, leading to some caveats and calling into question their claim that it "doesn't disrupt MTs". Once again, broad conclusions were drawn based on an n=1 image: "furrow ingression proceeded with kinetics comparable to controls, confirming that the core machinery for membrane trafficking and actin-driven invagination remained functional (Figure 3B). However, furrow spatial patterning was dramatically altered: in nuclear-depleted cortical regions, furrow initiations were more frequent and closely clustered, but failed to progress deeply. In nuclear-enriched regions, furrows progressed with kinetics comparable to controls but were misaligned, frequently enclosing multiple nuclei per compartment rather than the single nucleus observed in controls" Only one thing was quantified-furrow ingression rate-and this must have been done on the selected set of furrows that progressed, and not, for example, of ones like those at the bottom of the image series presented. None of the other conclusions about spatial patterning were quantified-for example, nuclei are not even visualized in Fig 3C. Finally, they do not even mention the results of the MT perturbation presented in this Figure, and the fact that few differences are apparent calls into question their conclusion that that "nuclei (and their associated MTOCs) serve as spatial landmarks that pattern membrane invagination".

This comment is well taken on every count, and the centrifugation experiment has been reanalysed accordingly. Every claim in that section is now quantified. The comparisons are paired within single coenocytes (nuclei depleted vs enriched regions) so that each coenocyte serves as its own control. Moreover, the microtubule part of the experiment is analysed and reported rather than left aside. The new quantifications are the following:

1. Nuclear displacement itself, as the percentage of nuclei in the enriched region per coenocyte before and after centrifugation (Figure EV3B).
2. The state of the microtubule network after centrifugation, as the length of the longest microtubule of each nuclear aster (Figure EV3C).
3. Furrow spacing in the nuclei-enriched and nuclei-depleted regions of the same coenocyte and its variability (Figure 3E and Figure EV3F).
4. Furrow length by region and its ratio (Figure EV3G).
5. Ingression rate by region and across spin conditions, and the invagination angle by region (Figure 3C, Figure 3D and Figure EV3E). On MTs , we agree that the original claim was not supportable and it has been removed. We now measure the network rather than assert that it is intact. Centrifugation does not leave MTs undisturbed. It relocates them together with the nuclei, and the same sentence reports what is lost from the depleted cortex.

Line 269-276: Microtubules were relocated with the nuclei as every nucleus retained the associated MTOC and MT network, and the length of the longest microtubule of each network was unchanged by centrifugation (5.97 against 5.08 µm, Fig. EV3C). Throughout these experiments nuclei are resolved in single optical sections as regions from which FM4-64 is excluded and are visible as such at both low and high display contrast (Fig. EV3D). In the nuclei-depleted cortex of the same coenocytes, tubulin was present only as some short fragments, a median of three per coenocyte with a median length of 0.95 µm (Data EV1).

On the broader point that centrifugation moves more than nuclei, the referee is right and we do not present it as a clean perturbation. The manuscript states that displacement is only partially penetrant (Olivetta et al. 2023), gives the previously reported figures for irregular invagination and lysis under identical conditions, and restricts the analysis to coenocytes with clear nuclear displacement.

Line 257-263: This approach builds on previous work where we used centrifugation to perturb the spatial relationship between nuclei and the cortex and demonstrate that cellularization in S. arctica is sensitive to local nucleocytoplasmic ratios.26 Centrifugal displacement is partially penetrant, with approximately 40% of centrifuged coenocytes showing irregular plasma membrane invaginations and about 10% undergoing lysis.26 Analyses were therefore restricted to coenocytes showing clear nuclear displacement.

The observation about selection is also correct, and we have made it explicit rather than leaving it implicit. Measurements were indeed made on furrows that progressed far enough to be traced, and the nuclei-depleted cortex carries many additional small indentations that never sustain ingression. We now state this in the Methods and in the legend of Figure 3C. The failure of those small indentations to progress is part of the phenotype itself.

Line 308-317: Furrow spatial patterning was dramatically altered: in nuclear-depleted cortical regions, furrow initiations were more frequent and closely clustered but failed to progress deeply (Figs. 3B and EV3D). Among the furrows that did progress, spacing was more variable in the nuclear-free region than in the nuclear-enriched half of the same coenocyte. (Fig. 3E). Since furrow spacing is reliably quantifiable only for furrows that progress, the effective furrow spacing in this nuclear depleted region appeared wider and was abolished upon MBC treatment (Fig. EV3F). Taking into account the high number of furrow initials in the nuclear-depleted region (Figs. 3B and EV3D), and furrow separation in the region enriched with nuclei suggests a minimum furrow exclusion zone around individual nuclei and their MT networks.

On the visibility of nuclei, and as set out in our response to comment 2, nuclei are resolved in single optical sections as regions from which FM4-64 is excluded. In this figure they are now marked with asterisks * in the time-lapse panel, Figure 3B, and Figure EV3D shows a centrifuged coenocyte at both low and high display contrast, so we do not repeat the general point here.

The final point is the most important one, and the revised analysis answers it directly. The microtubule part is now reported, and far from showing few differences it reverses the relationship between nuclear position and furrow spacing. In control coenocytes the nuclei-depleted region carries wider gaps than the enriched one, and after MT depolymerization it carries narrower gaps.

Line 317-322: Furrows in nuclear-depleted regions reached shorter lengths (2.14 against 7.50 µm, Fig. EV3G), forming asymmetrically longer compartments on the nuclear-enriched side. This advantage in nuclear-enriched regions was lost upon MBC treatment confirming the role of nucleus-associated MT networks in maintaining the synchronous invagination and uniform cellular partitioning.

We have also weakened the conclusion the referee quotes, so that it claims a relationship rather than a mechanism.

Line 322-326: With centrifugation, though the nucleus-associated MT networks also migrate, the regular spacing of the cytoskeletal network at the cortex was disrupted, and furrows no longer exhibited the uniform spacing characteristic of control coenocytes, suggesting indeed that MT-defined nuclear territories serve as spatial landmarks that define the coordinates of membrane invagination.

Figure 4 is surprisingly described in a single short paragraph. While some things were quantified, I was not convinced that they could conclude that they observed furrows “mispositioned like those seen upon MT depolymerization”. More broadly, what do we really learn from this?

This section has been substantially expanded, and the comparison the referee doubted is now made statistically. The section now opens with what is known about membrane supply during cellularization in other systems, including the link between the Golgi and microtubules that makes this perturbation informative in the first place, and it reports a dose series rather than a single condition.

Line 363-375: While these experiments define how cellularization is spatially patterned, the cellular machinery driving membrane invagination itself remained to be identified. The previous experiments show that furrow invagination proceeds even when furrows are mispositioned. This indicates that the processes of new membrane addition and furrow positioning are controlled independently. To identify the cellular processes driving furrow invagination, we examined the role of membrane trafficking. In early Drosophila embryos, the membrane expands from a reservoir of microvilli localized at the apical cortex.33,34 The first phase of this membrane invagination is supplemented partly by Golgi-derived vesicles. These vesicles are transported in a MT-dependent manner and are stalled with colcemid or colchicine treatment which eventually prevented furrow invagination.18,23,35 It is unclear if such a membrane reservoir is present at the S. arctica cortex where the furrows are first initiated. Brefeldin A treatment in Drosophila embryos inhibits furrow progression in the final stage of cellularization.15,18

On the dose series, a high dose of Brefeldin A at 3 µg/ml interferes with and in some coenocytes blocks cellularization, which establishes that Golgi-mediated trafficking is required for the process and is shown in Figure EV4A to Figure EV4C. All quantitative measurements are made at 1.5 µg/ml, a dose that leaves ingression intact, and the Methods now state this separation explicitly so that no measurement is read as belonging to the blocking dose.

On the resemblance to MTs depolymerization, the referee is right that this could not be concluded from the images, and we have therefore tested it. Furrow spacing variability was measured identically in the experiments. They are statistically indistinguishable, and so are their two controls, which is what makes the comparison meaningful.

Figure 4C: (C) Variability of furrow spacing within a coenocyte, from the same measurements. Methanol 0.212, BfA 0.433, p = 0.0047. Measured the same way in both experiments, the two perturbations are indistinguishable from one another (MBC 0.446 versus BfA 0.433, p = 0.66) and so are the two controls (DMSO 0.213 versus methanol 0.212, p = 0.67).

On what is learned from the experiment, the answer is that the two perturbations dissociate, and this is now the organising result of the manuscript. Ten measurements are compared between them in Figure 4F, each as a log2 fold change against its own control and grouped by the property it belongs to, and Figure 4G summarises which machinery contributes to which property.

Line 389-395: Nuclear positioning, by contrast, was not detectably affected as neither inter-nuclear distance nor its variability differed from controls (Figs. EV4E, F). Ingression rate (Fig. 4E), its variability (Fig. EV4G) and the maximum length reached by furrows (Figs. EV4H, EV4I) were likewise comparable to controls. Cellularization nonetheless took longer to complete (from 40 to 50 min, Fig. EV4J), and the cells released at the end were of more variable size (0.140 to 0.266, Fig. EV4K).

Trafficking is therefore required for cellularization to proceed, since the high dose blocks it, yet at a dose that leaves ingression rate untouched what it contributes is where furrows form and whether cellularization finishes on time. Nuclear organisation is unaffected at that dose, in Figure EV4E and Figure EV4F, which is precisely where the two perturbations part company and is the reason the resemblance in furrow positioning is informative rather than trivial.

The closing paragraph of this section has been rewritten as described in our response to comment 3, and it now ends on this comparison rather than on a general statement.

Significance

As I note in detail in the previous section, Here the authors extend this work to the ichthyosporean Sphaeroforma arctica, exploring the fascinating process by which a syncytial life stage cellularizes, and seeking to define the role of microtubules and Golgi trafficking. Their new expansion microscopy delivers impressive images of membrane and the cytoskeleton during this process and has the promise of answering important questions about the roles of microtubules and membrane trafficking. I thus went into my review quite excited. However, as I detail below, while some aspects of the process are carefully quantified, the current manuscript draws multiple broad conclusions that do not seem fully supported by the limited data provided. This substantially reduced my enthusiasm.

We are grateful that the referee finds the ExM compelling. The concern that broad conclusions outran the data has driven most of this revision, and every conclusion in the manuscript is now either carried by a measurement made across the dataset or has been removed.

Reviewer #2

Evidence, reproducibility and clarity

Summary

This interesting paper is a follow-up from Dudin et al.'s seminal 2019 eLife paper describing cellularization in the ichthyosporean Sphaeroforma arctica. In that earlier story, a role for microtubules (MTs) in cellularization was supported by treatment with the MT-depolymerizing drug MBC, which deeply affected nuclear spacing and the regularity of cellularization. However, the difficulty of imaging microtubules at the time had prevented more in-depth functional studies. This technical barrier has now been lifted by ultrastructural expansion microscopy (U-ExM), and this paper thus picks up where the earlier study left off.

The study combines live imaging, drug treatments, electron microscopy and ultrastructural electron microscopy to support a role for microtubules, nuclei, and membrane trafficking in sustaining the fidelity of S. arctica cellularization. An extensive live imaging dataset and careful image quantifications reinforce and expand the previously published observation that microtubules, while dispensable for cellularization to occur at all, are necessary for it to occur with proper timing and spacing. UEx-M images support the idea that actin and microtubules guide plasma membrane invaginations, and centrifugation experiments support a role for nuclear positioning in ensuring fidelity of cellularization. Finally, Brefeldin A treatment followed by live imaging and U-ExM supports a role for membrane trafficking in furrow positioning and elongation.

Major comments

The conclusions are adequately supported by the data, and their limitations are transparently acknowledged: notably, it is not fully clear by what mechanisms nuclei guide cellularization, and whether those mechanisms depend on microtubules or not. Below are a few points where I feel additional data (or better visualization, or additional verbal caveats) could improve the manuscript.

We are grateful that the referee reads the work as picking up where the 2019 study left off, and that they find the conclusions supported and the limitations transparently stated. Their four points are addressed below.

1) After 12,000rpm centrifugation, the authors point out that furrows "were misaligned, frequently enclosing multiple nuclei per compartment". This is not obvious in Figure 3C, where nuclei are only visible as empty spaces and only labelled (by asterisks) at a relatively early stage of furrow ingression. This point could be better supported by more explicit images (with nuclei more evident at late stages, even if only as blank spaces), or maybe by co-staining DNA and either membrane or F-actin in centrifuged samples.

The co-staining the referee suggests is now provided. Figure 3A and Figure EV3A show centrifuged coenocytes by U-ExM with DNA, membrane, actin and tubulin labelled together, so nuclei are seen directly rather than as gaps. Asterisks now mark nuclei throughout the time-lapse in Figure 3B, and Figure EV3D shows a centrifuged coenocyte at both low and high display contrast. As set out in our response to Ref 1-2, nuclei are scored in live imaging as regions from which FM4-64 is excluded.

2) In centrifuged samples (Figure 3A), some staining is visible in tubulin channel of the nuclei-free part, but does not correspond to discrete, observable microtubules. Could the authors comment on this? Do they think these represent diffuse, perhaps damaged microtubules (nucleated independently of nuclei?), or perhaps free tubulin, or mere background?

We have measured it rather than interpreted it. These objects are short tubulin-positive fragments, clearly distinct from nuclear asters in both number and length, and we report them separately for that reason. We do not claim to know whether they are remnants of displaced MTs or independently nucleated, and the manuscript says so by describing them rather than assigning them an origin.

Figure EV3C: In the nuclei-depleted cortex of the same coenocytes, tubulin was present only as short fragments, a median of three per coenocyte and 0.95 µm long (see Data EV1), which are different objects from an aster and are not tested against it.

3) Similarly: in centrifuged samples Fig. 3C, the nuclei-free part of the cell does seem to cellularize, albeit slower and forming smaller compartments than the nucleated part. This suggests that nuclei (and microtubules?) guide cellularization, but are perhaps not necessary for it. Could the authors comment?

We agree, and this is now quantified. In the nuclei-depleted region furrows are more widely and more variably spaced, reach shorter lengths and ingress more slowly than in the nuclei-enriched region of the same coenocyte, yet they form and progress. Nuclei therefore guide cellularization without being required for it, which is also what Referee 3 takes from the same experiment.

Line 308-317: Furrow spatial patterning was dramatically altered: in nuclear-depleted cortical regions, furrow initiations were more frequent and closely clustered but failed to progress deeply (Figs. 3B and EV3D). Among the furrows that did progress, spacing was more variable in the nuclear-free region than in the nuclear-enriched half of the same coenocyte. (Fig. 3E). Since furrow spacing is reliably quantifiable only for furrows that progress, the effective furrow spacing in this nuclear depleted region appeared wider and was abolished upon MBC treatment (Fig. EV3F). Taking into account the high number of furrow initials in the nuclear-depleted region (Figs. 3B and EV3D), and furrow separation in the region enriched with nuclei suggests a minimum furrow exclusion zone around individual nuclei and their MT networks.

4) The bottom row of Figure 3C presents a series of experiments combining MBC treatment with 12,000rpm centrifugation, but if I am not mistaken these are not discussed at all in the text. This is unfortunate, as it would be interesting to know what the authors want to conclude from these experiments (whose results are however not quantified, perhaps limiting their scope). In my view, one reason to be interested in this dataset is that it could in principle inform epistatic relationships between nuclei positioning and microtubules, that are otherwise left open: do these guide furrow ingression independently of each others (in which case their effects should be additive) or does one act purely through the other (in which case the combined treatment should not be worse than individual treatments)? In any case, I would suggest either commenting on these data explicitly (perhaps with additional quantification guiding interpretations) or removing them.

The referee is right that these data were not discussed, and they are now quantified and interpreted. As set out in Ref 1-4, combining centrifugation with MT depolymerization does not add to the effect of nuclear displacement but reverses it, so that the region depleted of nuclei carries narrower gaps rather than wider ones. This is the epistatic test the referee proposes, and it argues against two contributions acting independently and in parallel. The nuclear contribution appears to run through the MT network.

Minor comments

• Figure 1 contains two distinct panel H's.
• Typo p. 6: "actomyosing"
• Page 7: "longer MT extensions associated with deeper furrows during later stages (Figure 2D, arrowheads)" rather seems to refer to Figure 2B or C.
• Line and page numbers are missing

• All corrected.

  Significance

This paper will be of broad interest to readers interested in the evolution of multinucleated cells and cellularization, and the recurrent involvement of actin and microtubules in these processes (see notably recent papers by the Brugués lab). While it could appear incremental in an ichthyosporean-centric perspective (notably compared to the 2019 eLife paper that had anticipated some of the conclusions), its comparative implications gives it an additional scope in my view. Perhaps this is something the authors themselves could emphasize a bit more in their own conclusion. Finally, although most techniques had been established in earlier papers by the same authors, this study further confirms their robustness and the power of S. arctica as an emerging cell biology model - another nice touch.

We have followed this suggestion. The closing section now sets our results against cellularization in Drosophila and in chytrids. Also, it compares it against recent work showing that partitioning by MT asters is intrinsically unstable, so that losing its control broadens the distribution of compartment sizes rather than shifting it. That is the pattern we observe in our study. We have hinted at this in the discussion, so that the comparative implications the referee points to are stated rather than left to the reader.

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

In their manuscript, Araújo et al. described their investigation into the cellularisation process in Sphaeroforma artica during the multicellular stage of its life cycle. The coenocytes are relatively small at 50 µm in diameter, but the authors developed expansion microscopy and used a new actin probe to provide a detailed description of the ingression of the membrane furrow between adjacent nuclei. They compared the formation of the furrow in the presence or absence of microtubules, as well as in conditions involving regularly spaced or clustered nuclei. They concluded that, while microtubules were not essential to the formation and ingression of the furrow, they were required for the fidelity of the process, as stated in the title of the manuscript.

A better quantification of the ingression pattern would have improved the data. The centrifugation experiment is particularly interesting, as it forces the accumulation of nuclei on one side of the coenocytes. Surprisingly, this only partially perturbs the position of the furrow. This showed, on the one hand, that nuclei contribute to the positioning of the furrow close to them, and, on the other hand, that an additional mechanism exists independently of them. The analysis does not clarify whether the absence of microtubules in these centrifuged states affects the position of the furrow. Figure 3C seems to suggest partial rescue (suggesting that the contribution of nuclei is microtubule-dependent, but that the peripheral membrane has its own partitioning mechanism), but this has not been quantified.

The quantification of ingression is considerably expanded, and the framework it now detailed in Ref 1 - 2.

On the centrifuged coenocytes lacking microtubules, this is now quantified. As set out in Ref 1 - 4, the relationship between nuclear position and furrow spacing does not merely weaken when microtubules are removed, it reverses, which supports their inference that the contribution of nuclei is microtubule-dependent. In the same experiment, the local slowing of ingression where nuclei are absent persists whether or not MTs are present, which is consistent with the second half of their reading, that the cortex retains a partitioning mechanism of its own.

One minor concern is that it remains unclear whether microtubule disruption affects the positioning of the nuclei, as stated in the text but not confirmed by the quantification (Figure 1F).

Figure 1F now reports the variability of inter-nuclear distance within each coenocyte, which roughly doubles upon microtubule depolymerization, while the mean is unchanged and is shown separately in Figure EV1G. The claim in the text is therefore about regularity rather than about mean spacing, and it is now matched by the panel that supports it. This is set out in full in Ref 1 - 2.

Reviewer #3 (Significance (Required)):

The work is primarily descriptive, and the processes determining the position of the furrow and driving its ingression remain unknown. Nevertheless, the work provides beautiful images of a poorly described yet potentially informative system. These are distant relatives of animals with interesting common characteristics, such as the cellularisation process. The conservation of this process may reveal some key fundamental properties of multicellularity. Despite its limited conceptual advances, the manuscript is thus innovative and interesting.

We thank the referee for their assessment. The revision strengthens what the paper claims. Comparing our two titratable perturbations across ten measurements shows that furrow positioning and furrow ingression dynamics can be disturbed independently of one another, and that neither prevents cellularization from completing (Figure 4F and Figure 4G). What is degraded is fidelity rather than execution of cellularization.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

The last several years have seen major advances in our understanding of the basic cell biology of the set of single cell animal relatives, led by the authors and their colleagues. These groups have developed several as models and pioneered remarkable microscopy approaches to examine their cell biology. Here the authors extend this work to the ichthyosporean Sphaeroforma arctica, exploring the fascinating process by which a syncytial life stage cellularizes, and seeking to define the role of microtubules and Golgi trafficking. Their new expansion microscopy delivers impressive images of membrane and the cytoskeleton during this process and has the promise of answering important questions about the roles of microtubules and membrane trafficking. I thus went into my review quite excited. However, as I detail below, while some aspects of the process are carefully quantified, the current manuscript draws multiple broad conclusions that do not seem fully supported by the limited data provided. This substantially reduced my enthusiasm. I'd also note, though I did not take this into account in my evaluation, that many of the images are presented at a size that was difficult to interpret, without my electronically enlarging them, and two of the Figures were mis-labeled.

1. Interpreting most of their Figures requires understanding the basics of cellularization in this organism. Comparing the diagram in Fig. 1B and the images in 1C left me confused. First, are all the images in 1C and similar images later cross sections? Are nuclei dispersed throughout the cytoplasm at the start or restricted to a region near the cortex. If the former, how do more central nuclei get cellularized? The transition from the unperturbed 20 and 40 minute timepoints left me unclear on the normal process. Panel G may have been helpful in this regard but only shows the treated embryo and no untreated one.
2. The authors make a number of conclusions in Figure 1. Some are carefully quantified but others are not. For example, they state "producing uncoordinated ingression with variable rates, diagonal trajectories, and occasional bifurcations, in contrast to the uniform, perpendicular furrows observed in controls". I was not convinced by the single images provided that these were different-for example, spacing in the unperturbed 10 minute time point seems variable and furrows are not "uniformly perpendicular" in the unperturbed 20 minute time point. I also was puzzled by the lack of change in nuclear spacing while furrow spacing was altered. Later on in this section they state "MBC-treated coenocytes displayed significantly decreased and irregular furrow spacing, resulting in some compartments lacking nuclei entirely (Figure 1G & H)", but none of these images visualize nuclei directly-Perhaps the lower level background in H is supposed to indicate this but no parallel wildtype image is shown. Finally, while their TEM images (in the panels that are either I or J due to mislabeling) are lovely, I was not sure what to conclude from them- only the unperturbed images show the embryo surface for orientation and the lefthand unperturbed image is not as straight as they suggest-I certainly don't think these few images support their strong, detailed conclusions here: "MBC treatment resulted in aberrant membrane architecture, with furrows exhibiting bifurcated and convoluted morphology and abnormal fusion at the base of invagination, compared to the smooth, organized structure of control furrows".
3. The images in Fig. 2B are remarkable and very informative, though as I note above they are presented at such a small size that they require considerable enlargement to appreciate. The surprising accumulation of actin at the invagination front, presumably long before membrane closure begins, was striking, as were the microtubule baskets. However, conclusions drawn again seemed too strong. The authors state "High magnification views further supported that these bundles closely tracked the advancing furrow fronts, with longer MT extensions associated with deeper furrows during later stages (Figure 2D, arrowheads)" (BTW once again this Figure was not labeled in parallel with the text-should be 2C). I did not think the NHS staining provided sufficient resolution of advancing furrow fronts to draw this conclusion. They end this section with some more detailed conclusions, which did not seem to me to be well supported by the single image shown: "Furrows were often misaligned, and compartments frequently enclosed multiple nuclei or, conversely, lacked nuclei entirely. In several cases, nuclei were observed trailing between furrows or located beneath partially formed compartments, suggesting that improper nuclear positioning may interfere with furrow progression and sealing (Figure 2F)." The latter conclusion also seemed to leave me wondering about cause and effect. The final sweeping conclusions in the paragraph on p. 7 top (next time please include page numbers) thus seemed much too broad.
4. I thought the use of centrifugation to move nuclei was clever. However, it also is moving many other things-for example it moves whatever organelles are labeled by BODIPY and apparently nuclear associated MTOCs, leading to some caveats and calling into question their claim that it "doesn't disrupt MTs". Once again, broad conclusions were drawn based on an n=1 image: "furrow ingression proceeded with kinetics comparable to controls, confirming that the core machinery for membrane trafficking and actin-driven invagination remained functional (Figure 3B). However, furrow spatial patterning was dramatically altered: in nuclear-depleted cortical regions, furrow initiations were more frequent and closely clustered, but failed to progress deeply. In nuclear-enriched regions, furrows progressed with kinetics comparable to controls but were misaligned, frequently enclosing multiple nuclei per compartment rather than the single nucleus observed in controls" Only one thing was quantified-furrow ingression rate-and this must have been done on the selected set of furrows that progressed, and not, for example, of ones like those at the bottom of the image series presented. None of the other conclusions about spatial patterning were quantified-for example, nuclei are not even visualized in Fig 3C. Finally, they do not even mention the results of the MT perturbation presented in this Figure, and the fact that few differences are apparent calls into question their conclusion that that "nuclei (and their associated MTOCs) serve as spatial landmarks that pattern membrane invagination".
5. 1. Figure 4 is surprisingly described in a single short paragraph. While some things were quantified, I was not convinced that they could conclude that they observed furrows "mispositioned like those seen upon MT depolymerization". More broadly, what do we really learn from this?

Referees cross-commenting

Unfortunately I remain convinced that this manuscript has significant issues with the match between the data presented and the claims made--I laid these issues out clearly and stand by them

Significance

As I note in detail in the previous section, Here the authors extend this work to the ichthyosporean Sphaeroforma arctica, exploring the fascinating process by which a syncytial life stage cellularizes, and seeking to define the role of microtubules and Golgi trafficking. Their new expansion microscopy delivers impressive images of membrane and the cytoskeleton during this process and has the promise of answering important questions about the roles of microtubules and membrane trafficking. I thus went into my review quite excited. However, as I detail below, while some aspects of the process are carefully quantified, the current manuscript draws multiple broad conclusions that do not seem fully supported by the limited data provided. This substantially reduced my enthusiasm.

GUIDE ON ALL THIS CHAPTRS VOCAB WORDS!!

I think this discussion is important to keep in mind as we discuss a patient's condition and consider the expeirence of their illness - not only the physical aspects and treatment plans, but the connotations surrounding their disease and how those may impact their incentive to seek care, trust medical providers, and precieve themselves.

This idea of "health for all" is fascinatingly contradictory to the rhetoric of the time and even more interesting, still such a point of contention today. The battle between the human right to health care and a fear of communism/socialism is ongoing as the two are contradictory. In order to have health care for all and to truly care for the poor, health care must not depend on one's income, and insurance ought not depend on one's employment status. I think if we deem something to be a human right, the govement is well positioned to fund that. However, this requires the cooporation of all voting members of a democratic society to work well in spite of the structure of healthcare funding. For example, in the US where healthcare is privatized, the quality of care is unmatched, but prices are astronomical. But in countries with socialized healthcare, the price is affordable yet the quality often suffers.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper, Chen et al. identified a role for the circadian photoreceptor CRYPTOCHROME (CRY) in promoting wakefulness under short photoperiods. This research is potentially important as hypersomnolence is often seen in patients suffering from SAD during winter times. The mechanisms underlying these sleep effects are poorly known.

Strengths:

The authors clearly demonstrated that mutations in cry lead to elevated sleep under 4:20 Light-Dark (LD) cycles. Furthermore, using RNAi, they identified GABAergic neurons as a primary site of CRY action to promote wakefulness under short photoperiods. They then provide genetic and pharmacological evidence demonstrating that CRY acts on GABAergic transmission to modulate sleep under such conditions.

Weaknesses:

The authors then went on to identify the neuronal location of this CRY action on sleep. This is where this reviewer is much more circumspect about the data provided. The authors hypothesize that the l-LNvs which are known to be arousal promoting may be involved in the phenotypes they are observing. To investigate this, they undertook several imaging and genetic experiments.

While the authors have made improvements in this resubmitted manuscript, there are still multiple concerns about the paper. I think the authors provide enough evidence suggesting that CRY plays a role in sleep under short photoperiod. The data also supports that CRY acts in GABAergic neurons. However, there are still major issues with the quality of the confocal images presented throughout the paper. In many cases it appears that the images are oversaturated with poor resolution, making it hard to understand what is going on. In addition, none of the drivers used in this study are specific to the neurons the authors aim to manipulate. Therefore, the identity of the GABAergic neurons involved in this CRY dependent sleep mechanism remains unclear. Similarly, whether l-LNvs are the target of this GABA mediated sleep regulation under short photoperiod is not fully demonstrated. The data presented suggests that but does not prove it.

Major concerns:

(1) While the authors provided sleep parameters like consolidation or waking activity for some experiments. These measurements are still not shown for several experiments (for example Figures 2E, 3, 4, 5, and 6). These data are essential, these metrics must be reported for all sleep experiments.

These metrics have now been added to Fig.2 S4 and 5, Fig.3 S1-3, Fig.4 S2 and 3, Fig.5 S2 and 4, as well as Fig.6 S1.

(2) Line 144 "We fed flies with agonists of GABA-A (THIP) and GABA-B receptor (SKF-97541) (Ki and Lim, 2019; Matsuda et al., 1996; Mezler et al., 2001). Both drugs enhance sleep in WT," The proper citation is needed here, Dissel et al., 2015 PMID:25913403. Both THIP and SKF-97541 were used in that paper.

Thank you for pointing this out. We have modified our manuscript accordingly.

(3) Figure 2C and 2F: it appears that the control data is the same in both panels. That is not acceptable.

Thank you for pointing this out. We are now using data from control flies that were monitored in the same experiments as the experimental groups.

(4) Figure 4A: With the quality of the images, it is impossible to assess whether GABA levels are increased at the l-LNvs soma.

We apologize for the poor quality. Unfortunately, the GABA immunostaining does not work very well in our hands and thus the background is high. We have now commented on this issue in the fourth paragraph of discussion and have toned down our conclusions regarding the GABAergic s-LNv—l-LNv circuitry in this revised version of the manuscript.

(5) Fig 4 S1A shows colabeling of l-LNvs and Gad1-Gal4 expressing neurons. They are almost 100% overlapping signals. This would indicate that the l-LNvs are GABAergic themselves, or that there is a problem with this experiment.

Fig 4 S1A demonstrates the expression pattern of SYT-GFP driven by Gad1GAL4, which should label the synaptic terminals of GABAergic neurons. Therefore, the labeling observed at l-LNvs suggest that GABAergic neurons project to l-LNvs. This is further validated by the GRASP and trans-Tango experiments.

(6) Fig 4 S1B: Again, I can see colabelling of the GFP and PDF staining, suggesting that Gad1-Gal4 expresses in l-LNvs.

Fig 4 S1B demonstrates anatomical sites where GABAergic neurons project to and form synaptic connections with PDF neurons. Therefore, GFP signals at the l-LNvs suggest that these cells receive synaptic inputs from GABAergic neurons, echoing the results shown in Fig 4 S1A.

(7) Line 184: "Consistently, knocking down Rdl in the l-LNvs rescues the long sleep phenotype of cry mutants (Figure 4-figure supplement 1D)." This statement is incorrect as the driver used for this experiment, 78G01-GAL4 is not specific to the l-LNvs, so it is possible that the phenotypes observed are not coming from these neurons.

Thank you for pointing this out. We have modified our manuscript to note this.

(8) Figure 4G-K: None of these manipulations are specific to the l-LNvs. The authors describe 10H10-GAL4 and 78G01-GAL4 as l-LNvs specific tools, but this is not the case. Why not use the SS00681 Split-GAL4 line described in Liang et al., 2017 PMID: 28552314? It is possible that some of the effects reported in this manuscript are not caused by manipulating the l-LNvs.

Thank you for pointing this out. We have now modified our manuscript to avoid misleading remarks. We have used SS00681 Split-GAL4 to express TrpA1 but did not observe any substantial effect on sleep duration under short photoperiod. Therefore, we did not use this line for further experiments.

(9) Similarly for the manipulation of s-LNvs, the authors cannot rule out effect that are coming from other cells as R6-GAL4 is not specific to s-LNvs.

We have now modified our manuscript to avoid misleading remarks.

(10) The staining presented in Fig 5 S1 is not very convincing. Difficult to see whether Gad1-GAL4 only expresses in the s-LNvs.

We have now quantified the GFP signal in the l-LNvs and s-LNVs in Fig.5 S1B and D. As can be seen, the s-LNvs show prominent signal above the background while the l-LNvs do not.

Reviewer #3 (Public review):

Summary:

In humans, short photoperiods are associated with hypersomnolence. The mechanisms underlying these effects is however, unknown. Chen et al. use the fly Drosophila to determine the mechanisms regulating sleep under short photoperiods. They find that mutations in the circadian photoreceptor cryptochrome (cry) increase sleep specifically under short photoperiods (e.g. 4h light: 20 h dark). They go on to show that cry is required in GABAergic neurons and that the effects of the cry mutation on sleep are mediated by alterations in GABA signalling. Further, they suggest that the relevant subset of GABAergic neurons are the well-studied small ventral lateral neurons that they suggest inhibit the arousal promoting large ventral neurons via GABA signaling

Strengths:

Genetic analysis to show that cryptochrome (but not other core clock genes) mediates the increase in sleep in short photoperiods, and circuit analysis to localise cry function to GABAergic neurons.

Weaknesses:

The authors' have substantially revised their manuscript, and the manuscript is better for the revisions. However, the conclusion that the sLNvs are GABAergic is unfortunately still not well supported by the data. A key sticking point remains the anti GABA immunostaining, and specific driver lines for sLNvs and lLNvs.

The authors should tone down their conclusions to reflect the fact that their data, as presented, does not support the model that cry acts in sLNvs to modulate GABA signalling onto lLNvs and thus modulate sleep.

Thank you for the comments. We have now toned down our conclusions regarding the GABAergic s-LNv—l-LNv circuitry in this revised version of the manuscript in the Introduction, Results and Discussion.

Reviewer #4 (Public review):

Summary:

Short photoperiod is an important experimental manipulation in neurobiology, endocrinology, and metabolism studies. However, the molecular mechanisms by which short photoperiod gives rise to behavioral phenotypes that are seen in seasonal affective disorders remain unknown. Using the classic circadian model organism Drosophila, this study examines short photoperiod-induced hypersomnolence and identifies the circadian photoreceptor cryptochrome as a regulator of GABAergic tone within the clock neural circuit to promote wakefulness under short photoperiod conditions. The discovery has broad implications for understanding how short photoperiod modulates neural inhibition in circadian circuits in regulating sleep.

Strengths:

The Drosophila model provided a powerful platform to dissect the molecular mechanisms underlying short photoperiod-induced hypersomnolence. A battery of behavioral, imaging, circuit-manipulation approaches was employed to test the novel hypothesis that the circadian photoreceptor cryptochrome modulates GABAergic tone within the clock neural circuit to promote wakefulness under short photoperiod conditions.

Weaknesses:

The current model proposed by the authors suggests that the small ventral lateral neurons of the Drosophila clock circuit are GABAergic; however, this remains unclear. At present, the field lacks sufficient data and validated reagents to definitively establish the GABAergic identity of these neuropeptidergic neurons.

Thank you for the comments. We have now toned down our conclusions regarding the GABAergic s-LNv—l-LNv circuitry in this revised version of the manuscript.

Recommendations for the authors:

The manuscript has improved after revisions. However, the evidence in support of the claim that the sLNVs secrete GABA onto the lLNvs remains unconvincing. The evidence that loss of cry in GABAergic neurons modulates sleep is solid. However, the authors' claim that the sLNVs are the relevant GABAergic neurons is not sufficiently backed up by the evidence presented. We suggest that the authors tone down their conclusions to reflect this.

Thank you for the comments. We have now toned down our conclusions regarding the GABAergic s-LNv—l-LNv circuitry in this revised version of the manuscript in the Introduction, Results and Discussion.

Reviewer #3 (Recommendations for the authors):

Minor points:

(1) The authors suggest that the effects of cry on sleep and mediated by the Rdl receptor, and use the GABA agonist THIP as support of this argument. However THIP acts on the Lcch3 and Grd receptors, not Rdl

Thank you for pointing this out. We have modified relevant discussion accordingly.

(2) In several instances (e.g. line 66, line 148), the authors use 'consistently' in the sense of 'consistent with previous data'. It would be better if they rephrase this.

This has been fixed.

Reviewer #4 (Recommendations for the authors):

It is my pleasure to serve as a reviewer for this revised manuscript. The authors have carefully revised the manuscript in response to the critiques raised by all previous reviewers and have used all the available reagents to conduct additional experiments to assess the GABAergic properties of the small ventral lateral neurons (sLNv). Although it remains unclear in the field whether sLNvs co-transmit GABA, this study raises this possibility within an interesting biological relevant context. I recommend this manuscript for final publication.

Thank you for your comments.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors characterize the phospholipid scramblase Xkr in Drosophila. They generate null mutants in both S2 cells and flies and find that phosphatidylserine (PS) exposure is reduced during apoptosis; they show reduced engulfment of apoptotic cells, and that the protein is localized partially within the cytoplasm, overlapping with the ER. They go on to identify Xkr binding partners and show that they overlap with plasma membrane-ER contact sites, suggesting that Xkr facilitates PS transfer from the ER to PM. Overall, this reveals a new role for Xkr and identifies new binding partners, which are valuable contributions to the field.

Strengths:

(1) The generation of new Xkr reagents in both S2 cells and flies to analyze its function. Tools are used to quantify both PS exposure and efferocytosis, and the effects of Xkr knockout are significant.

(2) The discovery of new binding partners of Xkr which also affect PS exposure and efferocytosis.

(3) The authors demonstrate that the binding partners are conserved in mammalian cells.

Weaknesses:

(1) Throughout the manuscript (e.g, lines 105, 165, 274 and discussion), the authors describe Xkr as being activated in a caspase-independent manner, and use this as the rationale for identifying binding partners. However, this is never shown in the manuscript or clearly referenced. Interestingly, there is a TEVDA sequence in the fly ortholog at the same location as the caspase cleavage site in C. elegans Ced-8 (Figure S1), suggesting the caspase cleavage site is conserved. This should be further investigated, or the statements regarding caspase independence should be modified. I don't think the N- and C-terminal GFP fusions indicate caspase independence, especially since apoptosis was not induced in Figure 1A, B. If cleavage occurred at the TEVDA site in Figure S1A, it would not lead to a noticeable change on the Western blot, although the size does look a bit smaller in Figure S2B at the 8 h time point.

We thank the reviewer for pointing out that, as E/DXXD has been considered a conserved caspase-3 cleavage site, TEVDA has also been validated as a caspase-6 cleavage site, which we have missed. We will further confirm this using site-mutated expression vectors in S2 cells.

(2) The authors examine overlap between tagged Xkr and cellular compartment markers and find substantial overlap with Lamp (and other vesicle markers to a lesser extent) (Figure S2). This is not addressed in the paper and could indicate engulfment of other cells since S2 cells are macrophages. To test this, the staining could be tested on the mixed cells (vesicle-GFP tagged S2 + apoptotic xkr-mcherry). Similarly, calreticulin is an eatme signal that gets translocated to the PM of apoptotic cells. This could affect interpretation of colocalization (Figure 2J), and ideally another ER marker should be used.

We thank the reviewer for the suggestion. We will attempt to label Xkr-mCherry under apoptosis with other vesicles and change the ER marker to Cnx99A (Calnexin ortholog in Drosophila).

(3) There are some places where there is over- or incorrect interpretation, and these instances should be corrected.

We thank the reviewer for their careful reading, and we will correct the mistakes in the revised manuscript.

Specific examples:

a) Line 342 "Relative expression analysis by RT-qPCR showed that all three mutants were likely null alleles." This does not make sense since there is still mRNA present. In Figure S7A, the tm9sf4 allele is expressed at 75% of the control. The others show a greater reduction, but this is not proof of a null allele.

We agree with the reviewer’s opinion. These mutants from the BDSC are not completely deleted but partially deleted; therefore, the RT-qPCR assay may not be very accurate. We will detect the mRNA levels of tm9sf4, dorp9, and sac1 using RT primers from different cDNA regions to make the results more convincing.

b) Figure S3I - It looks like mCherry-Lact:C2 does get localized to the PM with AcD treatment in the xkr[ko], although the authors conclude "this disrupted PS localization to the PM could not be restored by apoptosis induction". However, the PM localization does look disrupted in the tm9sf4 and sac1 knockdowns.

We thank you for raising this intriguing hypothesis. Indeed, PM localization of Lact:C2 was reduced in xkr^ko cells, and the distribution could not be rescued after apoptosis. Unlike xkr^ko, tm9sf4, and sac1 RNAi-treated cells displayed weak PS disorder, which may be due to the efficiency of knockdown. However, the statistical results indicated that the ratio of PM/Cyto was reduced in tm9sf4 and sac1 RNAi-treated cells.

c) Figure 3I. The control Lact:C2 staining looks very different from the staining in Figure 2J, with abundant Lact:C2 outside the cell. Given the variability in the staining, were the contact sites quantified? On lines 287-288, it is stated that "fewer ER-PM MCSs were detected in xkrko cells than in WT", but no quantification is provided.

We thank for the reviewer’s suggestion. We will add the statistical results of Fig. 3I in the revised version.

d) Line 299-300 - "the interaction between Xkr and dORP9 was enhanced after apoptosis induction". The interaction does not look enhanced in Figure S5F, so this statement should be removed or data supporting the statement should be provided. The interaction between Xkr and dORP2 looks enhanced upon apoptosis induction, but also paradoxically looks even more enhanced when apoptosis is blocked.

We thank you for raising this intriguing hypothesis. We will delete the relevant statement to eliminate unnecessary misunderstandings.

e) The data in Figure S6 are highlighted in the abstract. If this is a major conclusion, it would be best to move it to the main text and provide quantification.

We thank for the reviewer’s suggestion. We will move this to the main text and provide quantification in the revised version.

f) Lines 392-4. The concluding statement seems overstated given that there was only a modest inhibition of PS exposure in the osbpl5 knockdown (Figure 6A) and no defects in efferocytosis (Figure 6C). The osbpl8 showed a stronger effect on PS exposure but still a very modest effect on efferocytosis.

We thank for the reviewer’s suggestion. We will weaken the statement in the Results section of Figure 6 and perform osbpl9 knockdown to observe efferocytosis in Raw264.7 cells, as OSBPL9 interacts with Xkr8 strongly.

Reviewer #2 (Public review):

In this study, the authors investigate the mechanisms underlying phosphatidylserine (PS) exposure during efferocytosis in Drosophila. They first show that Xkr promotes PS exposure and apoptotic cell clearance in both S2 cells and Drosophila embryos. As Drosophila Xkr lacks the canonical caspase cleavage site found in mammalian XKR proteins, the authors further explore the underlying mechanism by which Xkr regulates PS externalization. Through protein interaction studies, they identify TM9SF4 as an interacting partner of Xkr that regulates PS distribution and show that non-vesicular PS transport contributes to apoptotic PS exposure and efferocytosis. Using protein interaction studies, they further demonstrate that Xkr interacts with the lipid transfer protein dORP9 at ER-PM contact sites to facilitate non-vesicular PS transport to the plasma membrane. Loss of these proteins affects PS externalization and efferocytosis in Drosophila. Finally, using human cells, they demonstrate that human OSBPL8 interacts with XKR8 to regulate apoptotic PS exposure. Overall, the study supports a model in which Xkr promotes efferocytosis by facilitating lipid transport in addition to its role as a phospholipid scramblase.

Thank you for your comprehensive and generous assessment of our work and for the time and expertise you have devoted to reviewing our manuscript. We will revise the manuscript accordingly and provide a point-by-point response in the revised version.

Reviewer #3 (Public review):

Summary:

The manuscript investigates the function of the Drosophila Xkr protein, a homolog of mammalian Xkr8 that lacks the canonical caspase-cleavage motif. The authors show that apoptotic stimuli increase Xkr protein abundance through a post-transcriptional mechanism and that Xkr promotes phosphatidylserine (PS) exposure during apoptosis. Using immunoprecipitation coupled with mass spectrometry, they identify TM9SF4 as an Xkr-interacting protein and further implicate TM9SF4, Sac1, dORP2, dORP9, and Vap33 in regulating apoptotic PS exposure and efferocytosis. Based on these findings, the authors propose that Xkr regulates PS transport at ER-PM contact sites. Similar observations are also presented in human cells.

Strengths:

Overall, this is an interesting study. The authors provide convincing evidence that Drosophila Xkr participates in apoptotic PS exposure and employ multiple complementary approaches to support the involvement of several proteins in this pathway. The identification of TM9SF4 as a potential regulator of Xkr-mediated PS exposure is likely to be of broad interest.

Weaknesses:

I am less convinced by the evidence supporting the proposed role of ER-PM contact sites, and several mechanistic conclusions appear to extend beyond the data presented. Addressing the following points would substantially strengthen the manuscript.

We sincerely thank you for your careful reading and accurate summary of our manuscript. We appreciate the time, effort, and expertise you have dedicated to evaluating our work, and we will try our best to improve our manuscript according to your suggestions.

Major concerns:

(1) In Figure 2A and related text, it is unclear whether the mass spectrometry analysis was performed using untreated cells or AcD-treated cells. If the objective was to identify apoptosis-associated Xkr interactors, it would be helpful to clarify the experimental condition and explain whether apoptosis-specific interactors were analyzed separately.

We thank for the reviewer’s suggestion. We used AcD-treated S2 cells and untreated S2 cells to perform mass spectrometry. To clarify this, we will add a detailed method description in the method section.

(2) In Figure 2B, 2E, and several other co-IP results, a negative control of Flag tag only is required to exclude experimental errors like insufficient washing, etc.

We thank for the reviewer’s suggestion. We used anti-HA magnetic beads to perform immunoprecipitation, and single HA-TM9SF4 was used as a negative control.

(3) In Figure S3B, S3F, and several other BiFC results, an mVC-only negative control would be important to exclude nonspecific fluorescence complementation.

We thank for the reviewer’s suggestion, we will add the negative control for BiFC results in the revised version.

(4) In Figure 2G, the quantitative values appear inconsistent with the flow cytometry histograms. The peak shift following Sac1 knockdown appears smaller than that of TM9SF4 knockdown, whereas the quantified values suggest the opposite. Please clarify this apparent discrepancy.

We sincerely thank you for the careful consideration of our statistical results, which were obtained from 3 repeats. We will choose another flow cytometry histogram of tm9sf4 and sac1 to make the data and images more consistent.

(5) I find the interpretation in Lines 223-227 difficult to reconcile with the data. Knockdown of both tm9sf4 and sac1 impaired apoptotic PS exposure to a similar extent as xkr knockout. However, while xkr deficiency significantly reduced efferocytosis, sac1 knockdown produced only a modest, statistically insignificant effect. These observations suggest that impaired PS exposure alone may not fully account for the efferocytosis phenotype observed in xkr-deficient cells. These results appear difficult to reconcile with the proposed model, which needs careful discussion.

We sincerely thank the reviewer for their careful and thoughtful observations. Given the results we have observed, we will add this to the discussion section in the revised version.

(6) In Lines 274-275, the authors state that 'increased Xkr may accelerate non-vesicular PS transport for efficient apoptotic PS exposure'. However, Xkr protein levels increase only ~8 h after AcD treatment, whereas PS exposure occurs much earlier. Thus, alternative explanations like Xkr relocalization (Figure S5C), rather than increased abundance, may also explain how Xkr mediates PS transport. An Xkr overexpression experiment could be helpful to support this statement.

We thank for the reviewer’s suggestion. We will overexpress Xkr with or without AcD treatment to observe whether the localization or amount of Lact:C2 changes and to re-evaluate the role of Xkr in PS exposure.

(7) The interpretation of the MAPPER experiments requires further clarification. In Line 283, the authors refer to "the intracellular proportion of the signal for each protein overlapping with MAPPER." Since MAPPER is designed to label ER-PM contact sites, which are located on the plasma membrane, intracellular MAPPER fluorescence likely represents the ER network rather than bona fide ER-PM contacts. Throughout the manuscript (including Figure S6, etc.), intracellular MAPPER puncta appear to be interpreted as ER-PM contacts, which may not be appropriate. In contrast, the peripheral MAPPER puncta observed along the cell cortex (e.g., Figure S5C after AcD treatment) are more consistent with authentic ER-PM contact sites. It is also not obvious that these cortical MAPPER signals colocalize with Xkr(Figure S5C). Thus, while the data support a role for the ER, they do not yet convincingly demonstrate Xkr clustering at ER-PM contact sites.

We thank the reviewer for the suggestion, and we believe that the TIRF technique can help us demonstrate the ER-PM signal. Since our college has no TIRF microscope, we will try our best to seek cooperation from other colleges to achieve this experiment.

(8) In the Xkr knockout cells, all fluorescence signals appear substantially low in intensity. Differences in protein distribution are difficult to interpret when overall probe expression also appears altered. It would be helpful to demonstrate that probe expression levels are comparable between conditions. Furthermore, as noted above, intracellular MAPPER signal may primarily represent ER rather than ER-PM contacts. Finally, despite the reduced signal intensity, the remaining MAPPER and PS signals still appear well colocalized in the knockout cells, similar to the observations in Figure 2J. The interpretation in Lines 285-288 should therefore be reconsidered.

We sincerely thank the reviewer for this careful and thoughtful observation, and we agree that the interpretation in Line 285-288 is overstated. To explain this, we plan to detect the Lact:C2 and MAPPER signals in S2 and xkr^ko cells with or without AcD to confirm how Xkr regulates PS via ER-PM under apoptotic conditions.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Some of the authors proposed in a PNAS paper in 2016 the occurrence of the EntnerDoudoroff (ED) pathway in cyanobacteria and plants, on the basis of several lines of biochemical and genetic evidence. However, more recent results indicated that one of the two specific enzymes of the ED pathway (EDD) is missing in Synechocystis PCC 6803. The authors carried out additional experiments, which demonstrated that EDD is missing, and one of the enzymes (ED aldolase) is a promiscuous enzyme which seems to be involved in proline metabolism and is not actually participating in the ED pathway as initially believed. The results described in this paper are strong evidence that this new interpretation is appropriate, and therefore, it corrects the previous proposal, providing an honest description of the reasons why the authors had reached the wrong conclusion about the existence of the ED pathway in cyanobacteria and plants.

We thank Reviewer 1 for the summary and comments. Based on our finding that EDA is a promiscuous aldolase that, in addition to the cleavage of KDPG to GAP and pyruvate (a reaction of the ED pathway) catalyzes other reactions in vitro, we proposed potential in vivo functions of EDA, including its involvement in proline metabolism. However, these assumptions require further experimental testing. We do not yet have definitive findings regarding the function of the promiscuous aldolase EDA in Synechocystis in vivo, but respective studies are currently underway.

Strengths:

Thorough reanalysis of the experimental results obtained in previous studies, which led to the publication of the PNAS paper in 2016.

New experimental evidence to confirm that enzymes previously considered as participating in the ED actually are not catalyzing the ED biochemical reactions, but are involved in other metabolic pathways. Also, the authors completely discarded the occurrence of the GDH/GK shunt in Synechocystis PCC 6803. Generally speaking, the manuscript is very clearly written, with a precise description of the previous findings, the mistakes which took place in the 2016 paper, and the strategies they have used to address those issues, in order to reach a thoroughly revised vision of the glucose metabolic pathways in Synechocystis PCC 6803. In this regard, the drawings shown in Figures 1 and 7 are very helpful for the reader to follow the story and understand the possible metabolic transformations depending on the working hypothesis.

Also, I commend the authors for openly describing previous mistakes. In this paper, they reassess past observations in light of more recent findings and to integrate the information in this manuscript. The scientific conclusions are solid and very interesting, and besides, they use the opportunity to offer valuable advice to researchers. This is especially focused on the importance of careful biochemical characterization of enzymes, which should always be carried out when studying proteins which have been identified as a specific enzyme on the basis of sequence homology. In a similar way, they found that an insertional mutant was the cause of the absence of specific metabolites, which had been attributed to particularities of a metabolic pathway in that mutant, when it was actually due to a nucleotide insertion; this could have been easily prevented by confirming the correct generation of the mutant by DNA sequencing.

We thank the reviewer for this kind comment. We agree that biochemical characterization of enzymes as well as DNA sequencing to check deletion mutants, are important and valuable tools. As outlined in the manuscript and additionally in more detail in a recently submitted article, which is available at bioRxiv (Theune et al. 2026, doi: https://doi.org/10.64898/2026.04.08.717167) and is currently under review at PLOS One, we suggest that genome sequencing of deletion mutants in combination with complemented strains as controls are required to minimize the risk of misinterpretation based on secondary mutations (1). During the early stages of our research on the ED pathway, and later as well when we were already trying to resolve the conflicting results that had accumulated concerning the ED pathway, genome sequencing for Synechocystis mutants was not affordable as a routine procedure (2-4). Therefore, we could not have easily prevented this misconception based on this technique at that time. However, we strongly encourage genome sequencing of deletion mutants (in combination with complemented strains) as routine procedures these days (1).

Weaknesses:

The authors propose that EDA might be involved in the PEP-pyruvate-OAA node, or in the proline metabolism, but this requires further experimental work for clarification; what their results indicate clearly is that this enzyme is not actually catalyzing the transformation of KDPG to GAP, which is the second specific enzyme of the ED pathway. But the real physiological function in this cyanobacterium is still unconfirmed.

As stated above and in the manuscript, we agree that the in vivo role of EDA requires further experimental work which is in progress. However, our results demonstrate that EDA splits KDPG into GAP and pyruvate in vitro, but we assume that this reaction does not play a role in vivo due to the absence of its substrate.

Another aspect which could be improved is that the recombinant expression of some genes was carried out in E. coli; even if this is a useful and valid research strategy, in studies like this (where there is a strong focus on the physiological function of enzymes in the original organism, Synechocystis PCC 6803), I think it would have been more appropriate to express the 6803 genes in another cyanobacterium easily amenable for genetic transformation and gene expression, which would produce the protein in a physiological environment more similar to another cyanobacterium (compared to E. coli, which is an heterotrophic bacterium). I am not sure this would change any of the obtained results, but it certainly would confer additional robustness to the enzymatic results.

Synechocystis is easily amenable to genetic manipulation, and we agree that expression and purification of all enzymes from this host would have been ideal. However, the first characterization of Synechocystis EDA was performed with proteins that were purified from Synechocystis and showed activity on KDPG at comparable rates as proteins that were purified from E. coli in this study (2). Moreover, most biochemical characterizations of EDAs from archaea, bacteria and plants were performed after recombinant expression in E. coli and yielded highly active enzyme as in the case of Synechocystis is this study (5-7). Therefore, we currently have no reason to worry that the expression in E. coli might affect the enzymatic activity of EDA. The main reason for utilizing E. coli as an expression strain in this study was to gain higher yields of protein for in-depth analyses.

Bibliography:

I think the list of papers used in this manuscript is complete and up to date. However, I do miss recent papers which addressed one aspect that was proposed in the original 2016 PNAS paper: the authors wrote, "We therefore suggest that Prochlorococcus might oxidize glucose via the ED pathway under mixotrophic conditions, as shown for Synechocystis." Recent studies checked this hypothesis and have shown that the ED pathway seems to be also missing in Prochlorococcus and marine Synechococcus, and I think this manuscript is a good place to cite them, since these results are consistent with the findings of this paper.

We will include a references from Moreno-Cabezuelo et a. 2023 (DOI: 10.1128/spectrum.03275-22) in which the proteomes of three marine Prochlorococcus and three marine Synechococcus strains were investigated upon exposure to glucose (8). Protein levels of EDA were either downregulated or not affected while proteins involved in OPP pathway and CBB cycle were upregulated. The authors of this study conclude that this indicates that the latter processes rather than the ED pathway are involved in photomixotrophy in these strains. However, flux analyses are still missing.

Reviewer #2 (Public review):

Summary:

The study presents novel results on the presence of the Entner-Doudoroff pathway in Synechocystis sp. PCC 6803. In contrast to an earlier study, compelling evidence is given that this strain lacks both an ED pathway and a glucose dehydrogenase/glucokinase bypass but contains a promiscuous aldolase, which also decarboxylates oxaloacetate and cleaves 2-keto-4-hydroxyglutarate (as it occurs in proline degradation). The study concludes with successfully reconciling data from different studies and with lessons learned from the previous misconception.

Strengths:

Solid biochemical data are presented to reconcile contradicting data of earlier studies and to serve as a basis for disclosing possible functions of a promiscuous aldolase. Earlier misconceptions and lessons to be learned are well discussed.

Weaknesses:

The materials and methods section is rather lengthy, suffering from a lack of conciseness and repetition, and nevertheless misses some specifications.

We thank Reviewer 2 for the kind summary and comments and will improve the materials and methods part accordingly in a revised version.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Some additional aspects that could be improved:

(1) L182-184: Are there any known in vitro attempts to determine whether some DHADs can accept 6PG as substrate? If not, did the authors check this possibility in the lab?

To the best of our knowledge, as mentioned in the manuscript, some DHADs are tested for their activity towards gluconate and some other substrates but not 6PG. It was suggested that since gluconate is smaller it might fit in the catalytic site of DHADs normally occupied by DHIV (7). We discussed this point in the manuscript (Line 177-185).

In this study we tested the DHAD Slr0452 from Synechocystis and DHAD from Synechococcus with 6PG as substrate but the enzyme did not catalyze 6PG dehydration. The result for Slr0452 is shown in Figure S3.

(2) L234-241: This paragraph shows how important it is to avoid relying only on sequence alignments to assign functions to proteins (and enzymes in particular). The authors stress this idea elsewhere in the paper, but I think it should receive even more attention in a manuscript like this. Physiological characterization of the protein function is paramount, especially in the case of enzymes. Also, the GDH1 overexpression mutant was done in E. coli; this adds an additional layer of uncertainty, since the protein processing in E. coli might not be entirely identical to that carried out in cyanobacteria, as I mentioned above. This, in turn, could be one of the reasons for not finding the expected enzymatic activity. This comment is also relevant for the results shown in Table 1 (page 12).

As outlined following lines L234-241 we tested crude cell extracts from Synechocystis WT, a Synechocystis strain overexpressing putative GDH1 (Sll1709) and a Dzwf deletion mutant which can be assumed to upregulate a GDH/GK bypass if present in Synechocystis for GDH activity but did not find any. This strongly indicates that sll1709 does not code for an active GDH in Synechocystis. We thereafter also overexpressed GDH1 in E. coli and again could not detect any GDH activity. In case of GDH1, enzyme activity was therefore tested both in Synechocystis and E. coli and yielded similar results.

(3) L309-310: "we currently have no explanation for the gluconate that was detected in previous IC-ESI-MSMS measurements in Synechocystis". This is a serious issue, given how important this evidence was for the conclusions of the 2016 PNAS paper and the hypothesis of the ED pathway in cyanobacteria. I would suggest that the authors provide some possible explanations, even if it is based on studies from other teams.

It would be very speculative and therefore in our eyes not helpful to search for explanations in this case as indeed the measurements were done in another lab. One explanation might be that 6P gluconate got dephosphorylated and yielded gluconate as an artifact. However, as we have no experimental validation for this idea and furthermore cannot test it. We therefore prefer to not further comment on this aspect.

(4) L347: The presence of an insertion in the sequence of zwf in the ∆gnd mutant is a welcome explanation for the observed results: abolition of 6PG production in this mutant. This is another important message to stress in this manuscript: construction of mutants should always be double checked by DNA sequencing of the relevant genomic regions, to ensure that these kinds of side problems do not appear, leading to confusing results.

We agree with the reviewer and would get even one step further and rather suggest combining whole-genome sequencing with complemented mutants as it is difficult to know all relevant genomic regions that should be sequenced. We discuss this issue in even more detail in another manuscript that is currently available as online preprint in bioRxiv and is under review (9). This work was now added as a citation in line 566 and the end of the following statement (line 564-566): Routine complementation of deletion mutants and sequencing of selected genes or the entire genome are effective means of identifying secondary mutations that can lead to misleading phenotypes (9).

(5) L418-419 and Table 2: The results observed for the authors (i.e., that EDA could also catalyze reactions with OAA and KHG, albeit with substantially lower catalytic efficiency than with KDPG), is a matter for concern: if their hypothesis is correct (meaning that this EDA is fundamentally involved in the PEP-pyruvate-OAA node and/or proline metabolism, and not with the ED pathway), then why should it keep in the evolution of these organisms such a strong preference for KPDG, when it is not being used physiologically for the ED pathway)? Furthermore, the Km for KDPG is lower than for OAA or KHG, leading to a very big difference in the Kcat/Km values.

To solve these questions further respective studies are underway. As EDD is absent from Synechocystis no KDPG should be available in the cells so that catalytic activity on KDPG should be irrelevant in vivo. The in vivo role of Eda requires further clarification.

Hereafter, I will mention some aspects, following the instructions of eLife, which are related to suggestions for improved experiments/data/analyses, improvements of writing and presentation, and minor corrections to text/figures.

(1) L81: I would modify the text to "Accordingly, this raises further questions...".

Thanks for this hint. We modified the text accordingly.

(2) L189: Add "pages" after "following".

Thanks for pointing this out. We replaced “following” by “below”.

(3) Page 7: The whole beginning of the Results section is actually more discussion than description of results, and the first mention of figures appears in L207 of page 8. Given the content of the paper, I think the authors might reconsider using "Results and Discussion" rather than different, specific sections for Results and Discussion. This is one of the papers where I think the combined use of both makes sense and will allow an easier understanding of the message.

We thank the reviewer for this valuable suggestion and changed the heading to Results and Discussion.

(4) L181: Add reference regarding the llvD/EDD superfamily.

We added the following references in lines 172-176 and 185-189:

(1) Melse, O., Sutiono, S., Haslbeck, M., Schenk, G., Antes, I., & Sieber, V. (2022). Structure Guided Modulation of the Catalytic Properties of [2Fe− 2S]-Dependent Dehydratases. ChemBioChem, 23(10), e202200088.

(2) Ren, Y., Vettenranta, E., Penttinen, L., Jänis, J., Rouvinen, J., & Hakulinen, N. (2025). The engineered dimer of L-arabinonate dehydratase from Rhizobium leguminosarum bv. trifolii: The role of intersubunit interactions in IlvD/EDD family. Biochemical and Biophysical Research Communications, 757, 151610.

(3) Ahmed, H., Ettema, T. J., Tjaden, B., Geerling, A. C., Van Der Oost, J., & Siebers, B. (2005). The semi-phosphorylative Entner–Doudoroff pathway in hyperthermophilic archaea: a reevaluation. Biochemical Journal, 390(2), 529-540. ff

(4) Bräsen, C., Esser, D., Rauch, B., & Siebers, B. (2014). Carbohydrate metabolism in Archaea: current insights into unusual enzymes and pathways and their regulation. Microbiology and Molecular Biology Reviews, 78(1), 89-175.

(5) Figure 2: The data shown in column plots in Fig 2A, B and C, and 4B, could be presented in tables, which would save space while providing the same information: basically, very little/no activity in some cases vs high levels of activity in others.

We would like to keep the column plots as we still think that they visualize our data well.

(6) L255 "Unfortunately, we were not able to overexpress putative GDH2". It would be interesting to give more details about the possible reasons for this fact.

We tested different growth conditions for recombinant GDH2 expression. The expression culture was incubated at 37 °C for 3 hours as well as overnight at 18 °C for overnight after induction. Both experiments did not resolve the expression problem.

(7) L409-410: I think this sentence should include a brief part explaining the kind of essay used to test this activity.

We added now that the LDH-coupled continuous assay was used (see line 403).

(8) Figure 6E: Please give the specific activity in U/mg, as in Fig 6F, instead of percents.

100% is given in U/mg units in the figure legend as “control without effector (100 %; specific activity of 4.3 U/mg)”. For easy comparison of effectors, the relative activity (%) is often used. We would therefore prefer to keep the current data presentation.

(9) L576: Provide the origin of the utilized PCC 6803 strain, given there is a certain level of variability in this strain (glucose tolerance, etc). Also, even if there are some methods which are very widely used, I think the Materials and Methods section should either properly describe them or else cite the source. For instance, BG11 medium is mentioned, but no further information is given.

We included the information that the glucose-tolerant Synechocystis strain was utilized and added the receipt of and a citation for BG11 medium (10).

(10) L582 Generation of mutants: This section mentions the Gibson Assembly cloning method, but I miss further information to allow the reader to reproduce the methodology with as many details as possible, or at least cite papers which do so.

We added a reference in which Gibson Assembly is described (11). Together with the primers listed in Table S3 the generation of mutants is now reproducible.

(11) L609 Please give information in g, not rpm, for centrifugation. Also, mention the model and brand of the centrifuge and rotors used. Also, immunoblotting is very loosely described. This is also valid for other sections, for instance, L618, L636.

We now added the following information: Cells were harvested by centrifugation at an RCF (relative centrifugal force) of 3,992 x g in a Beckman Coulter with a JLA-8.1000 Rotor for 20 minutes at 4°C. We now added a reference (12) in which immunoblotting is described in more detail.

(12) L613: Describe the "small scale purification".

We now added the information that the small-scale purification was performed using a 50-ml aliquot of the large culture which was treated as described below for the remaining sample.

(13) L619-620: Describe the composition of the lysis buffer.

The composition of the lysis buffer is already described as follows: lysis buffer (50 mM NaPO₄ pH=7.0; 250 mM NaCl; 1 tablet complete protease inhibitor EDTA-free

(Roche) per 50 mL)

(14) L691: Specify which amounts of auxiliary enzymes in coupled enzymatic assays were used.

Thanks for pointing this out. We have now integrated the information that 1U of each of the auxiliary enzymes was utilized in the coupled enzymatic assays.

(15) L716: The authors mention several times using a "double beam spectrophotometer". Please provide the model and brand.

Model and brand were now added for the double-beam spectrophotometer (Uvikon 810, Kontron, Augsburg, Germany).

(16) L717 and 718: define "∆absorption".

In line 715, the information is given that absorption was measured at 340 nm, "∆absorption" is accordingly the ∆absorption at 340 nm. This information was added.

(17) L723: "Synechocystis" should be in italics.

Synechocystis is now written italics.

(18) L749-759: This section should be described in more detail: preparation of protein extracts, SDS, immunoblotting, etc, or cite references of the same team where these methods were properly described.

In this section the listed methods are already described in detail.

(19) 798-799: "frozen cell pellets". Please provide numbers to specify the amount of material used.

Thanks for pointing this out. We now added the information that frozen cell pellets with a wet weight of 2.4 g wet weight were resuspended.

(20) L871-872: "It was ensured that auxiliary enzymes were not rate-limiting. One unit (1 U) of enzyme activity is defined as 1 µmol substrate consumed or product formed per minute" is repeated several times in the manuscript (L 907-909, L936-938). I would advise using it the first time, and on other occasions, refer to the same conditions as described above.

We have accordingly circumvented the repetition of 1 U definition from the manuscript.

Reviewer #2 (Recommendations for the authors):

(1) Interpunctuation, especially comma placement, should be improved.

We improved interpunctuation, especially comma placement to the best of our knowledge.

(2) Line 63: delete the first "which".

“Which” was deleted.

(3) Lines 81/82: revise sentence.

We revised the sentence to: Accordingly, this raises further questions about the presence of the ED pathway in cyanobacteria and plants.

(4) Line 164: "presumed" instead of "presumes".

The word was changed accordingly.

(5) Line 228: by others? especially in reference 1?

We deleted by others as the reference is given.

(6) Line 240: "or" instead of "no".

“no” was replaced by “or”

(7) Figure 2: The axes are not well visible, and the explanation for the positive control in panel B is missing in the legend.

Axes from figures 2, 3 and 4 were enlarged. For Figure 2B the following information was added in the legend: As a positive control, 0.05 U glucose dehydrogenase from Pseudomonas sp. was added to Δzwf cultures and to purified putative GDH1 (Sll1709). Axes from figures 2, 3 and 4 were enlarged.

(8) The investigation on the general absence/presence of the GDH/GK bypass in cyanobacteria may not be necessary for this study.

We included this data in this manuscript as the mistaken assumption that the GDH/GK bypass exist in Synechocystis lead among other observations to the misinterpretation of an existing ED pathway in Synechocystis. We would therefore prefer to keep these data in the manuscript.

(9) Line 316: delete "on".

“on” was deleted.

(10) Line 352: delete "or".

“or” was deleted.

(11) Lines 352/353: ZWF expression level appears to be reduced accordingly. This should be stated.

We agree that Zwf expression might be lower, however, we are not entirely sure if this is truly valid and would rather test this assumption further as described in the following lines.

(12) Figure 4: The axes are not well visible.

Axes from figures 2, 3 and 4 were enlarged.

(13) Line 363: values are not only normalized to protein content, but also to activity found for the WT.

We now added: The values are normalized to Zwf enzyme activity found in the WT based on protein content.

(14) Line 408: no separate subsection required.

The title for a new subsection was deleted.

(15) Lines 437-439: These are results descriptions, which should not be placed in the legend, but in the main text, as is partially done.

We deleted these result descriptions in the legend.

(16) Lines 441/442: formatting: one or no bracket pair.

The brackets were corrected.

(17) Lines 443/444: refer to Table 2 instead of giving the values in the legend to avoid duplication.

We deleted the values and now refer to Table 2.

(18) Line 503: delete "identified".

We deleted the second “identified” in the sentence and changed the wording to: Apart from four identified cyanobacteria that possess potential EDDs. In addition, we also added the names of the four cyanobacteria that were found including the sequence IDs of the putative EDDs.

(19) Lines 529/530: revise sentence and format.

We added one sentence and revised the following sentence: In contrast to Synechocystis EDA, EDA from Synechococcus prefers OAA over KDPG. The catalytic efficiency of Synechococcus EDA on oxaloacetate is rather low (OAA 0.437 s^-1 mM^-1), however, its activity can be enhanced by NADP⁺(13).

(20) Line 542: revise sentence.

We revised the sentence to: It remains to be investigated whether this reaction could play a role in vivo, with KDPG potentially acting as a regulatory metabolite at low concentrations.

(21) Line 577: The glass tubes used for cultivation should be specified.

We now added the following information: Custom-made glass tubes were placed in a photobioreactor (manufactured by Willi Hilke, Uslar, Germany).

(22) Lines 584-585: unclear, was the resistance cassette not placed in the gene to be deleted?

Yes, the resistance cassette was placed in the gene to be deleted and was fused for homologous recombination to two DNA fragments approximately 200 bp directly upstream and downstream of the gene. This information was now added.

(23) Line 607: cultivation equipment to be specified.

The following information was now added: For the purification of GDH1 from Synechocystis, a 6 L photoautotrophic culture of the P3-His-GDH1 overexpression strain was grown in a 10 L glass flask at 28°C, illuminated with constant light (50 µmol m^-2 s^-1) and gassed with filter sterilized ambient air to an OD₇₅₀ of about 1.

(24) Line 670: GTS should be specified.

Thank you for this hint. This was a typo. GST was meant not GTS. This was now corrected and GST was specified as Glutathione S-Transferase.

(25) Line 679: delete "gluconate kinase (GK) and".

The second gluconate kinase (GK) was deleted and sentence was revised to:

For gluconate kinase (GK) activity measurements in Synechocystis crude cell extracts the GK reaction was enzymatically coupled to 6-phosphogluconate dehydrogenase (GND) reaction, the latter providing NADP⁺ reduction, which was monitored photometrically at 340 nm.

(26) Line 686: again GK activity? Difference unclear. Was the previously described procedure for GND activity determination?

GK activity measurements in Synechocystis crude cell extracts and GK activity measurements with recombinant enzyme that was expressed in E. coli were done in two different labs with different protocols. Therefore, the first description refers to measurements with Synechocystis while the second measurement refers to measurements with E.coli. This is now specified more clearly.

(27) Type/supplier of spectrophotometers and centrifuges used should be given.

Model and brand were now added for the double-beam spectrophotometer (Uvikon 810, Kontron, Augsburg, Germany). As this study was performed in two different labs over a period of 8 years including one lab moving to a new location, it is now impossible to specify all centrifuges that were utilized. Even though we agree that it would be good to provide this information, we now would have difficulties to be specific.

(28) Consider the referencing of published methods to streamline the materials and methods section.

We now streamlined the materials and methods section by deleting repetitions as outlined below. However, as protein expression, protein purification and enzymatic tests were performed in different labs, in some cases several protocols are given.

(29) Line 757: give specifics of anti-rabbit antibody and define PBS-T and PBS-T Cytiva.

Specifics were added to the text.

(30) Lines 761ff: It is not given for all genes used how they were derived. All synthesized?

We now added detailed information for all genes.

(31) Line 762: codon-optimized for? E. coli?

The information was added that genes that were expressed in E. coli were codon-optimized for E. coli.

(32) Lines 782-786: Rationals for experimental strategies do not belong to materials and methods sections, but to results sections.

The part was deleted in the materials and methods section and transferred to the results section.

(33) Lines 818/819: repetitive.

We removed the repetition and refer to the purification method as stated above in the materials and methods section.

(34) Lines 847-851: True for all EDA-type assays? Kinetic parameters are shown in Table 2 rather than Table 1.

Yes, true for all EDA-type assays. We changed the Table number to 2.

(35) Line 863: delete "in".

“in” was deleted

(36) Lines 888-893: sounds repetitive.

The lines were modified accordingly.

(37) Lines 908/909: repetitive.

The repetitive comment on the definition of 1U was deleted.

(38) Lines 928-938: repetition

The repetition was deleted.

References

(1) M. Theune et al., Easy-to-use whole-genome sequencing workflows and standardized practices to uncover hidden genetic variation in <em> Synechocystis </em> PCC 6803 wild-type and knock-out strains. bioRxiv 10.64898/2026.04.08.717167, 2026.2004.2008.717167 (2026).

(2) X. Chen et al., The Entner–Doudoroff pathway is an overlooked glycolytic route in cyanobacteria and plants. Proceedings of the National Academy of Sciences 113, 5441-5446 (2016).

(3) D. Schulze et al., GC/MS-based 13C metabolic flux analysis resolves the parallel and cyclic photomixotrophic metabolism of Synechocystis sp. PCC 6803 and selected deletion mutants including the Entner-Doudoroff and phosphoketolase pathways. Microbial Cell Factories 21, 69 (2022).

(4) A. Makowka et al., Glycolytic Shunts Replenish the Calvin–Benson–Bassham Cycle as Anaplerotic Reactions in Cyanobacteria. Molecular Plant 13, 471-482 (2020).

(5) V. Zaitsev et al., Insights into the Substrate Specificity of Archaeal Entner–Doudoroff Aldolases: The Structures of Picrophilus torridus 2-Keto-3-deoxygluconate Aldolase and Sulfolobus solfataricus 2-Keto-3-deoxy-6-phosphogluconate Aldolase in Complex with 2-Keto-3-deoxy-6-phosphogluconate. Biochemistry 57, 3797-3806 (2018).

(6) J. S. Griffiths et al., Cloning, isolation and characterization of the Thermotoga maritima KDPG aldolase. Bioorg Med Chem 10, 545-550 (2002).

(7) S. E. Evans et al., Plastid ancestors lacked a complete Entner-Doudoroff pathway, limiting plants to glycolysis and the pentose phosphate pathway. Nature Communications 15, 1102 (2024).

(8) J. Moreno-Cabezuelo, G. Gómez-Baena, J. Díez, J. M. García-Fernández, Integrated Proteomic and Metabolomic Analyses Show Differential Effects of Glucose Availability in Marine Synechococcus and Prochlorococcus. Microbiol Spectr 11, e0327522 (2023).

(9) M. Theune et al., Easy-to-use whole-genome sequencing workflows and standardized practices to uncover hidden genetic variation in Synechocystis sp. PCC 6803 wild-type and knock-out strains. bioRxiv 10.64898/2026.04.08.717167, 2026.2004.2008.717167 (2026).

(10) R. Y. Stanier, R. Kunisawa, M. Mandel, G. Cohen-Bazire, Purification and properties of unicellular blue-green algae (order Chroococcales). Bacteriol Rev 35, 171-205 (1971).

(11) D. G. Gibson et al., Enzymatic assembly of DNA molecules up to several hundred kilobases. Nature Methods 6, 343-345 (2009).

(12) M. Boehm et al., Comprehensive study on ferredoxin isoforms in the cyanobacterium Synechocystis sp. PCC 6803. bioRxiv 10.64898/2026.04.08.717189, 2026.2004.2008.717189 (2026).

(13) N. Xie, C. Sharma, K. Rusche, X. Wang, Phosphoketolase and KDPG aldolase metabolisms modulate photosynthetic carbon yield in cyanobacteria. The Plant cell 10.1093/plcell/koae291 (2024).

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

Learn more at Review Commons

Reply to the reviewers

We provide below a point-by-point response to reviewers’ comments, describing changes that were made to the manuscript. We also uploaded a "Full Revision" file that contains a general statement in addition to these responses to reviewers. We sincerely thank both reviewers for their thorough reading and suggestions that we believe contributed to a better concision and clarity of the revised manuscript.

Reviewer #1

Major Comments

1. TDH3 has been a major model in the study of the evolution of gene expression as developed by the authors. While most conclusions derived from this system relate to genetic mechanisms, this study attempted to identify the molecular/cellular mechanisms. Although I greatly appreciate the author's comprehensive efforts, I would suggest that conclusions regarding molecular/cellular mechanisms should be made with greater caution, especially avoiding over-generalized conclusions that may be specific to P_TDH3. Thus, I suggest going over the manuscript again and adjusting some statements if they are over-generalizing, as well as adding an explicit discussion of this limitation.

As suggested by the reviewer, we went over the manuscript and made sure that we specifically mentioned the TDH3 promoter in conclusions that may be specific to this promoter. In addition, we further addressed this limitation by including new results of an experiment where we measured the effects of yme2, chs1 and msh1 mutations on expression noise of three additional yeast promoters (PFBA1, PACT1, PTEF1). We found that the three mutations had similar effects on expression noise driven by PTDH3, PACT1 and PTEF1, but different or no effect on PFBA1 expression noise. Therefore, some of our conclusions may not be specific to the TDH3 promoter, such as the importance of mitochondrial state in regulating expression noise of nuclear genes. We described these findings in Results, in the new Figure 7 and in associated supplements. We also added a paragraph in the Discussion and we included new co-authors who performed these additional experiments. We believe these new results will increase the impact of the study.

1. On the surface, it may seem reasonable to ask for changed noise by unchanged mean in order to distinguish independent regulators. However, from a mechanistic perspective, this is quite demanding. In the current prevailing model (transcriptional burst) of noise origination, mutations are not assumed to be noise-specific without affecting the mean. See e.g. PMID: 31320634. If noise and mean are intrinsically coupled, looking for noise-only regulatory mechanisms would imply something very different. This may mean, for example, that we are seeking one single mutation that changes noise and mean through one mechanism, while at the same time reverting mean to its wildtype value through another mechanism. It is likely that this is one of the reasons why causal mutations are difficult to identify.

This is a very sensible comment. We agree that in the model of noise originating from transcriptional bursts, cis-acting mutations are not expected to alter noise without affecting the mean. However, trans-acting mutations may affect transcriptional bursts of a given gene via different mechanisms that compensate each others at the level of mean expression but not at the level of expression noise. Even though mutations impacting noise without altering mean expression may be less common than mutations affecting both mean and noise, they do exist as we showed here. It is possible that we did not identify mutations in transcription factors known to regulate TDH3 promoter activity because such mutations would affect both mean expression and noise. We added two sentences in the discussion to mention this hypothesis. In addition, while the transcriptional burst model can explain the coupling between intrinsic noise and mean expression, it does not apply to mutations impacting extrinsic noise.

Regarding the difficulty to identify mutations altering only expression noise, we found a causal mutations in three out of five mutants analyzed. Interestingly, the three successes corresponded to mutations that increase noise, and the two failures to mutations that decrease noise, suggesting that mutations decreasing noise may be particularly difficult to identify. Finally we note that expression noise is a complex genetic trait in natural populations. An interesting case is shown in Fehrmann et al. 2013, where three trans-acting alleles (loci on chr7, 8 & 13) had a strong individual contribution on noise, partially coupled to mean changes. When combined together, their cumulative effect was very strong on both mean and noise, although the wild strain from which these alleles originate showed an elevated noise but no remarkable change in mean as compared to a reference strain. This implies that other (unmapped) loci “buffer” expression mean in this wild strain against the action of the three noise-acting loci, a scenario comparable to the one suggested by the reviewer.

1. L209-214. The authors state that they selected 254 mutants with the largest noise changes from a library of 1,241 strains (L209-214). However, I cannot match this statement when contrasting figure1-figure supplement 1 (254 mutants) and Figure 1a (1,241 strains). Is this caused by experiments conducted in different labs ? Are there any intuitive ways for the authors to show the strains (and their parameter distribution) that produced consistent results across the two batches of data? E.g. using gray/black dots for un-/repeatable strains. Also, are mean expression levels similarly (un-)repeatable compared to noise ?

Both fluorescence screens were performed in the same laboratory, using the same instrument and following the same protocol. We clarified in the text and figures how the 254 mutants were selected for the secondary screen. In particular, we colored dots on Figure 1 and on Figure 1 – figure supplement 1 to highlight strains with reproducible or non-reproducible change in expression noise in both assays. The apparent lack of reproducibility between the first screen of 1241 strains and the second screen of 254 mutants is not surprising because the 254 strains were not picked randomly among the 1241 initial strains: they were picked because they showed the largest expression changes (either for mean or noise) in the first screen. Statistically, the most extreme effects on mean expression and expression noise observed among the 1241 strains are expected to be over-estimated on average. This phenomena is similar to the “Winner’s curse” in economy. When measuring a quantitative trait for a large number of samples with a certain degree of uncertainty, values that fall in the tails of the distribution (the most extreme values) are statistically expected to be less accurately estimated than values falling near the mean of all samples. To address the last question of the reviewer, mean expression levels were found to show better repeatability than expression noise, probably because error bars (variation among replicate samples) tended to be much smaller (one order of magnitude) for mean expression than for expression noise.

1. How were the five strains analyzed chosen? Are they the only strains fulfilling the criteria on L211-214?

The five strains were picked arbitrarily among nine strains that matched the criteria mentioned in the text. We added a sentence to mention this point. We moved to Supplementary File 5 the section describing how the five strains were chosen to make the main text shorter and easier to read.

1. L243-247. I didn't understand the logic why m2 is included, please elaborate.

We modified the text to clarify why we picked mutation m2 as a candidate. The logic is that there was no strong statistical evidence to exclude the mutation (because of lower statistical power relative to other mutations).

1. The equation for extrinsic noise (L899) seem to be slightly differently from that in Fu and Pachter 2016. The product of mean(RFP) and mean(YFP) is multiplied by 2 here, but not in Fu and Pachter 2016.

We made a typo in the text and corrected it in the revised version. We verified in our R scripts that we used the correct version from Fu and Pachter (with product of mean(RFP) and mean(YFP) not multiplied by 2), which was the case. We are particularly thankful to the reviewer for the thorough proofreading of the manuscript.

1. The experimental design to exclude noise from partitioning for yme2 is really nice. It would have been great if we had gotten to the bottom of this. (This is not a question so no response is needed)

No response requested.

1. The authors demonstrate that a nonsense mutation in CHS1 increases extrinsic noise via impaired chitin septum reparation in daughter cells. However, glucosamine treatment itself alters cell size (Figure 5-figure supplement 3a), which correlates with noise levels. This raises the question: do the observed changes in extrinsic noise stem from glucosamine-induced changes in cell size or from the impaired chitin repair caused by the CHS1 mutation itself? To disentangle these effects, an alternative approach to modulating chitin synthesis that does not alter cell size should be employed.

We do not think that glucosamine-induced changes in cell size can explain the effect of glucosamine treatment on extrinsic noise in chs1 mutant. We observed that glucosamine treatment had a stronger impact on cell size in WT cells than in chs1(G1752a) mutant cells (Figure 5 – figure supplement 3a). However, glucosamine treatment had a much stronger impact on extrinsic noise of chs1(G1752a) mutant cells than WT cells (Figure 5g). Therefore, there is no direct correspondence between the effect of glucosamine on cell size and the effect of glucosamine on extrinsic noise. Even though glucosamine drastically reduced cell size in WT cells, it had almost no impact on expression noise in these cells. We added a sentence in the revised Results to clarify this point.

Our hypothesis is that glucosamine increases chitin synthesis not only during repair of the chitin septum, but more globally at all stages of the cell cycle (as shown by Bulik et al., 2003), which may reduce cell size. The global impact of glucosamine on cell wall chitin levels could rescue defects caused by chs1 mutation on chitin septum repair. Previous studies showed that CHS1 was not involved in global chitin synthesis, but only in the repair of chitin septum in daughter cells.

1. Why did glucosamine doses not significantly impact cell growth rates during the first phase after addition (Figure5 -figure supplement 4) ? Additionally, I can seem to find the experimental details for glucosamine dosing in the Methods.

We specified the dose of glucosamine in the revised Methods. We did not observe a significant impact of glucosamine on growth rates during exponential growth either in the first growth phase or in the second growth phase after addition. However, glucosamine increased the duration of the lag phase in the second phase of growth. We do not know exactly why, but we speculate it is because the chitin cell wall becomes thicker after diauxic shift in presence of glucosamine, leading to a delay to resume cell division after cells are exposed to fresh medium with glucose.

1. Figure 2-figure supplement 2g-l are missing.

We included the missing panels in the revised figure.

1. The current manuscript is a bit lengthy (although nicely comprehensive). After deciding the journal, I suggest it would need to be more concised and logically streamlined.

We agree that the main text is lengthy, with methodological explanations sometime disrupting the main message. For this reason, we included in the revised version a new Supplementary File 5 where we moved these explanations that were important yet not essential for the reader to understand the main conclusions.

Minor points

1. P12,L345, "may not only by caused by" should be "may not only be caused by", ,and "YFP an RFP" should be "YFP and RFP" in the same sentence

We corrected these mistakes.

1. P19,L565, "sensitivite" is misspelled and should be "sensitive".P21,L630, "mitochondria dysfunction" should be "mitochondrial dysfunction."

We corrected these mistakes.

1. Typo in Figure 3's legend "** 0.001 > P {greater than or equal to} 0.001", which should read "0.01 > P {greater than or equal to} 0.001." This error appears again in Figure 4's legend.

We corrected these mistakes.

1. P9, L219 "Table 1" should be "Supplementary File 1"?

We added the number of mutations per strain in Table 1.

1. Inconsistent tetrad numbers: methods state 22 tetrads (L844) , results mention 21 tetrads ( L262 ) , and figure( figure1 -figure supplement 3) legends indicate 20 tetrads. Please clarify the correct number.

Thank to the reviewer for mentioning this inconsistency. In fact, we dissected 22 tetrads but only included 21 tetrads that showed the expected segregation of all genetic markers in the fluorescence assay. Finally, we reported fluorescence measurements for 20 tetrads due to a possible contamination for the remaining tetrad. We clarified this in the Methods.

1. The speculated retrograde response pathway is interesting. Can the authors propose some specific experiments to test that ?

To test the involvement of the retrograde pathway in PTDH3 intrinsic noise, one could mutate negative or positive regulators of the retrograde signaling in wild-type cells or in chs1 and msh1 mutant cells and quantify the effect on intrinsic noise. We proposed this experiment in the revised discussion. In previous studies, null alleles of rtg1, rtg2 or rtg3 were shown to impair the retrograde response, while specific mutations in rtg2 and deletion of mks1 were shown to activate the retrograde pathway (Garrigos et al., 2024; Jazwinski and Krete, 2012). We expect to observe an elevated intrinsic noise in wild-type cells, but not necessarily in yme2 and msh1 mutant cells, when we activate the retrograde signaling. Conversely, we expect yme2 and msh1 mutations to not alter intrinsic noise anymore when the retrograde pathway activity is impaired by mutation.

Reviewer #2

The manuscript by Martin et al. titled 'Trans-acting mutations reveal non-nuclear modulators of both intrinsic and extrinsic gene expression noise in a eukaryote.' identifies genetic mutations in yeast that can has regulate gene expression noise in trans. The manuscript is well written, and the experiments have been performed in replicates. The authors also clearly highlight the experiments where the replicates do not agree in their outcomes.

However, there are some issues that the authors need to address:

1. Introduction is too long and needs to be concise

We have shorten the introduction in the revised version. We have also moved parts of the main text in Supplementary File 5 to be more concise.

1. Lines 150-153: Do we have enough studies yet for generalizations?

We do not know other studies/examples that compared the effects of cis-acting and trans-acting mutations on mean expression and expression noise of a target gene. Therefore, we cannot generalize the results obtained for the TDH3 promoter. However, these results show that cis- and trans-acting mutations can significantly differ in their effects on expression noise (but we do not know for how many genes it is the case).

1. Line 209 - Why 254 strains? Please justify

We clarified why and how we chose these 254 strains for the secondary screen. We also added colors on Figure 1 to highlight these 254 strains.

1. Why are the authors choosing median expression and not mean expression (which is usually the norm)?

We used the median to quantify the average expression among cells as we did in previous studies with the same fluorescent reporter system because median is more robust than mean to rare outliers. However, we found the difference between median and mean fluorescence to be really small. We included a new figure (Figure 2 – figure supplement 4) showing that the effect of yme2, chs1 and msh1 mutations on expression noise were almost identical when using mean and median to calculate the noise. This is because we measured fluorescence from large number of cells for each sample (~5000) and because the distributions of fluorescence levels among cells are always unimodal with very rare outliers (as showed in Figure 3 – figure supplement 1; Figure 5 – figure supplement 1 and Figure 6 – figure supplement 1).

1. Do EMS mutants have intra-population genetic heterogeneity? This should be discussed in the text.

We sequenced the genome of the 5 EMS mutants at a coverage of ~100x, but did not find evidence of genetic heterogeneity in these strains: all mutations detected were found at a frequency near 1. In another project, we sequenced the genomes of 288 EMS mutants and detected genetic heterogeneity in 3 strains: mutations were not fixed in these strains, but found at a frequency near 0.75. We therefore expect the number of mutants with genetic heterogeneity from the collection analyzed in figure 1 to be very small. In addition, genetic heterogeneity cannot impact our conclusions because no genetic heterogeneity was detected in the 5 EMS mutants analyzed and because we constructed two independent clones to investigate the effects of each mapped mutation. We added a sentence in the main text mentioning that no genetic heterogeneity was detected in the 5 EMS mutants.

1. Line 238-240: Shouldn't the change in frequency in low, mid and high- subpopulations be tested relative to the expected distribution from the wild-type strain? This could also alter how mutations are chosen for validation. This should be mentioned in the results section and the text should be rephrased to reflect this point, although it is mentioned in the methods section

We are not completely sure to understand what statistical test the reviewer has in mind. We could not easily compare the observed frequency of mutant and wild-type alleles in low, mid and high subpopulations to expected frequencies, because these frequencies depend not only on the effect of the mutation on fluorescence among cells but also on the effect of the mutation on growth rate (which is unknown). Our strategy to compare mutation frequency in medium bulk vs low and high bulk was designed to detect mutations changing expression noise independently from their potential effect on mean expression or growth rate.

1. Line 243: The mutant name YPW2162 suddenly appears in the text - where did this strain come from?

This is the name of one of five mutants analyzed, as mentioned in Table 2 referenced in the same sentence. We modified the sentence to make it clearer: “For a fourth mutant (YPW2162), ...”

1. Line 286: 'increase' instead of 'increased' .

We corrected this error.

1. Could genomic rearrangements/copy number variation alter expression noise? For example, for m4, m5 and m6 mutants. The authors have genome data of these strains, so this can be checked.

According to the reviewer’s comment, we performed additional analyses showing that CNVs and rearrangements did not contribute to variation of expression noise in the five EMS mutants included in the mapping experiments. To detect large CNVs and aneuploidies, we computed sequencing depth in 1-kb sliding windows along the genome for each mutant. The profiles were uniform and similar to coverage profiles obtained for the reference strain. To detect rearrangements, we analyzed sequencing data using the GRIDSS module that can detect junctions between non-contiguous parts of the genome from the mapping location of paired-end reads. Using this tool, we only detected 5 rearrangements that were previously known to be present in the genome of all mutant strains relative to the reference genome (deletions at ho and ura3 loci and duplications of TDH3 promoter, CYC1 terminator as well as 41 bases from chromosome I in the PTDH3-YFP transgene inserted at the ho locus). None of these rearrangements can explain variation of expression noise among mutants. Results from GRIDSS analysis are included in Supplementary File 4 and reported in the main text.

1. Figure 2 - y-axis: What is the measure of expression noise used here? This should be mentioned in the figure captions throughout to avoid confusion.

We used the same measure of expression noise for all figures, as mentioned in the Methods. We added it in the figure captions as suggested by the reviewer to avoid confusion.

1. Line 359 - please mention the effect size here and wherever possible throughout the manuscript

In the sentence mentioned by the reviewer, we used the forward scatter signal (FSC.A) as a relative measure of cell size. A difference of FSC.A between two samples is known to reflect a difference of cell size. However, we cannot estimate the effect size on cell size because the relationship between FSC.A and cell size depends on the instrument and settings, and we have not characterized this relationship empirically. Therefore, we removed “a small effect” from the sentence and we instead only mentioned that the effect on cell size was statistically significant. Indeed, we cannot be sure that the small (and significant) reduction of FSC.A we observed corresponded to a small reduction of cell size. 12. Figure 6 - figure supplement 2 - Please mention the strains represented by grey and orange boxes

To make it more visible, we moved this information from an inset in panel b to the top of the figure.

1. One could envisage that there are many more genetic regulators of expression noise which may have not been discovered yet. This point perhaps could be discussed.

Absolutely. We added a sentence in the discussion to acknowledge that many genetic modulators of noise may still remain unknown.

1. The figure captions are too long - they should be made concise

We reduced the length of the longest figure legends. In particular, some of the text from Figure 4 legend was moved to Supplementary File 5.

Author response:

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

We thank you for the time you took to review our work and for your feedback! We have performed the following additional analyses:

(1) We analyzed the optomotor mismatch response as a function of time spent in the optogenetic closed-loop session.

(2) We show the correlation between optomotor mismatch response and visuomotor mismatch response for functionally identified PE neurons.

The main changes to the manuscript are:

(3) Clarification of our terminology (moved and refined definition of the teaching signals).

(4) A new figure panel summarizing the functional influence patterns we identified.

(5) Clarification of our argumentation for the JEPA-inspired proposal.

All comments are addressed individually in the following.

Public Reviews:

Reviewer #1 (Public review):

Vasilevskaya and Keller test different models of cortical function through the lens of predictive processing, a powerful framework for the brain to learn and predict the statistics of the world via generative internal models. The authors use a clever combination of behavioral perturbations in closedloop and open-loop visuomotor virtual reality assays, a paradigm the Keller lab pioneered and used effectively in the past decade, in conjunction with two-photon imaging of neuronal calcium responses and targeted optogenetic perturbations of activity. They specifically put to test proposed hierarchical vs. non-hierarchical circuit implementations of predictive processing by analyzing the logic of inter-lamina interactions (superficial vs. deep; L2/3 vs. L5/6).

The authors conclude that both versions of predictive processing architectures they analyze are likely invalid, and instead formulate an alternative novel model of cortical function based on a recently developed machine learning algorithm for self-supervised learning (joint embeddings of predictive architectures, JEPA) and its further refinements. JEPA borrows elements from predictive processing, engaging two encoder networks and training the output of one network to predict the output of the other. In their new model of cortical computations, prediction error neurons in L2/3 compare the deep layers (L5/6) activity, which is taken as a teaching signal, to a local, L2/3 prediction of this latent representation.

Specifically, the authors build on their previous work and reports from other groups that different sets of L2/3 neurons compute positive prediction errors (fire when sensory stimuli appear unexpectedly with respect to the movements of the animal; e.g., grating onsets in the absence of locomotion) and respectively negative prediction errors (fire when sensory stimuli are absent, while the brain expected them to be present; e.g. mice locomote but visual flow is suddenly halted - visuomotor mismatches). These L2/3 positive and negative prediction error neurons exchange messages with neurons in the deeper cortical layers that, the authors propose, build an internal representation (R) of the sensory stimuli given the animals' movements.

In the hierarchical model, internal representation neurons (R) are supposed to act as a teaching signal for both types of prediction error neurons; the output of the positive prediction error neurons is assumed to suppress activity of R such that the error between the teaching signal and the prediction is minimized; similarly, in the non-hierarchical version, R serves as a prediction for the prediction error neurons, and in turn it receives excitatory drive from the positive prediction error neurons and negative input from the negative prediction error neurons.

The authors find that the functional impact of L5 neurons on L2/3 neurons is not compatible with the non-hierarchical architecture they and other groups proposed, but rather in accordance with the hierarchical model. At the same time, the functional impact of L2/3 neurons (positive vs. negative prediction error neurons) on L5 neurons (internal representation) appears not compatible with the hierarchical model, but rather in accordance with the non-hierarchical implementation.

They further hypothesize that L2/3 prediction error neurons don't use sensory input, but rather the L5 activity as a teaching signal, and test it using perturbations (halts) of optogenetic stimulation of L5 neurons coupled with locomotion (Figure 7).

All in all, the question is topical, and the new model addresses a decades-long quest to develop a unifying model of cortical function. The findings reported here transform our understanding of cortical computations, opening new, exciting avenues for future investigation. The experimental design and execution are rigorous; the arguments are clearly laid out (in spite of ample potential for confusion given the numerous loops and sign flips). These include a discussion of why the non-hierarchical model proposed by the same group does not hold, as well as potential caveats in interpreting the results and novel testable proposed experiments emerging from the JEPA-like model.

I have several questions about the interpretations of some of the claims and suggestions for potential additional experiments and analyses.

We thank the reviewer for their comments. We address them below.

(1) Some of the pieces of the puzzle remain to be identified and demonstrated: the existence of internal representation neurons in L2/3 and ascertaining that the L5/6 neurons analyzed function indeed as internal representation neurons. The authors find that stimulation of L2/3 positive prediction error neurons enhances activity of L5 neurons...If L5 neurons hold a latent representation that serves as a teaching signal for L2/3 neurons (as the authors posit), wouldn't one expect that the input they receive from the positive prediction neurons be suppressive, such that the error is further minimized?

Not necessarily - this depends on the model one has for how cortex works. In the hierarchical predictive processing model, PE+ neurons are expected to suppress the local internal representation neurons in L5. Our data, however, are not consistent with this model. This is one of the key arguments we build the idea on that JEPA is a better model for cortex than hierarchical predictive processing. In JEPA we would not expect the L2/3 prediction error to update L5 directly, but instead update the prediction of L5 activity (the source of this signal remains to be identified; see our speculations on the origin of prediction signals in the comments to question 3), and drive plasticity in the local L5 encoder network. That something acts like a teaching signal for the L2/3 comparator does not, by itself, determine how the outcome of the comparison influences the source of the teaching signal.

(2) Do the authors envision any specific differences between the representations of the two encoder networks posited to exist in L2/3 and L5 in the JEPA-like implementation? Are they synchronous/offset in their temporal representations, or any other features?

Given theoretical work (Mohammadi et al., 2025), one would expect to find differences in learning rates between the predictor and the encoder networks. Assuming the predictor network is also implemented in L2/3, we would expect to see faster learning rates in L2/3 compared to L5. Implementations inspired by related theoretical works also predict differences in learning rate between the two encoder networks (Grill et al., 2020), again with higher learning rates expected in L2/3 compared to L5. Beyond that, however, we are not aware of any experimentally observable differences one might expect to find. We are hoping the computational community will remedy this soon.

(3) Where is the prediction coming from onto L2/3 neurons? Is it emerging locally in L2/3 from the putative internal representation neurons, or is it long-range - as work from the authors previously proposed? Or a mix of both?

We expect the predictions to come from long-range inputs. In classical (hierarchical) JEPA one would expect these to be the lateral communication within L2/3. In a non-hierarchical implementation that is capable of operating on arbitrary graphs (as would be necessary for it to work in cortex), we suspect that the L2/3 network will use both long-range L2/3 and long-range L5 input. In JEPA terminology: the encoder A network uses information from non-local sources of both networks to predict local activity of encoder B network (assuming that information is statistically useful in predicting that activity).

(4) What is the role of the indiscriminate L4 input that appears to enhance activity of both positive and negative prediction error neurons in L2/3?

The short answer is, we don’t know. We would have indeed expected to find some asymmetry of influence. There are a few options: A) We might be failing to activate a specific interneuron that mediates feedforward inhibition on this pathway by the artificial stimulation of Scnn1a neurons. B) We know that Scnn1a neurons are only a subset of L4 neurons – there are other populations of L4 neurons that might exhibit the opposing influence. C) The Scnn1a population is more than 1 layer of a JEPA away from the comparator and not part of the predictor that forms the actual representation compared against L5 (e.g. L4 could provide an input to L2/3 internal representation neurons, and thus only indirectly influence L2/3 PE neurons). D) The JEPA analogy is wrong.

(5) Does Figure 7D change in a meaningful manner if the authors plot the correlation between optomotor mismatch response and visuomotor mismatch response specifically for the negative prediction error neurons in L2/3 (Adamts-2) rather than for all L2/3 cells sampled?

We might be misunderstanding. If the reviewer means genetically identified negative prediction error neurons (Adamts2), we do not have the data to address this question, as we did not perform any recordings of molecularly defined Adamts2 population in L2/3. If the reviewer means functionally identified negative prediction neurons, this would be the two rightmost data points in Figure 7D (the x-axis in this panel is the visuomotor mismatch response strength we use to functionally identify PE- neurons). These two data points on the right-hand side of the plot correspond exactly to what we classify as negative prediction error neurons throughout the rest of the manuscript (15% of the most responsive neurons to visuomotor mismatch).

Does the reviewer mean, is there also a positive correlation between optomotor mismatch response and visuomotor mismatch response when looking only at neurons that we identify as PE-? If so, the answer is yes (Author response image 1). Interestingly, while there is a positive correlation, there is also nonuniformity in response patterns. We think that this is expected, given that our visuomotor coupling paradigm captures only a very small subspace of stimuli that prediction error neurons are tuned to. Bulk stimulation of L5, in contrast, might work better to separate all PE neurons. In other words, we speculate that L5 stimulation is a better predictor of the functional role of an L2/3 neuron.

Author response image 1.

Optomotor mismatch response as a function of visuomotor mismatch response for neurons that are functionally classified as PE. Red line shows a linear fit estimated with a bootstrap approach.

(6) Do the optomotor mismatch responses in L2/3 neurons depend on how long the closed-loop coupling of optogenetic stimulation of Tlx3 L5 neurons and locomotion speed has been in place for?

No, not that we can measure. We performed an analysis in which we split the optogenetic closed-loop session into two equal parts, early and late. We then quantified the average optomotor mismatch response independently for early and late parts of the session (Author response image 2A). Based on this quantification, we find no evidence of a change as a function of time in the closed-loop session. We also performed a sliding window analysis on a shorter timescale. While it did look like the responses may be smaller in the first few minutes, we do not have sufficient data to address this. None of the differences in response size were significant (Author response image 2B).

Author response image 2.

Optomotor mismatch response as a function of experience with artificial closed-loop coupling. (A) Mean L2/3 population response to optomotor mismatch in the first half (Early MM) and in the second half (Late MM) of the optogenetic closed-loop session. (B) Mean L2/3 population response to optomotor mismatch as a function of time in the optogenetic closed-loop session. Error bars indicate SEM. Differences between the mean values were estimated by hierarchical bootstrap and are not significant.

Reviewer #2 (Public review):

This manuscript reveals the functional connectivity of two different classes of cortical neurons that respond in opposite ways to mismatches between sensory and top-down inputs. These data are very valuable because different theories of information processing in the cortex make different predictions on the patterns of connectivity of these neurons. Therefore, these data strongly constrain possible theories of cortical processing.

We thank the reviewer for their comments. We address them below.

General comments:

(1) The methods of statistical testing are insufficiently described. I did not understand the description in lines 1105-1119. The authors should provide sufficient details so the reader can reproduce their analyses. For example, it may be helpful to provide specific details of the testing procedure for one of the comparisons (e.g. the first comparison in Table S1).

We assume the reviewer is not familiar with hierarchical bootstrapping in general. If so, the explanation below would summarize the procedure. This is the procedure with particular emphasis on its application to neuroscience data is described in the paper we reference in that part of the methods (Saravanan et al., 2020). Given that the analysis has become relatively standard (and is described in the reference provided), we think it might be an overkill to add the full explanation below to the manuscript. In addition to the general procedure, there are only 2 pieces of information relevant to fully reconstructing the analysis:

(1) What are the “levels” (mice, recording sites, neurons, trials)?

(2) What is the number of bootstrap samples used.

Thus, we think all information is already provided in the methods. We now also explicitly added the levels when describing the nested structure of the data in the manuscript to increase clarity.

Hierarchical bootstrap analysis:

Our data are naturally nested: multiple neurons are recorded within a single mouse, and multiple mice are tested within an experimental group. Standard bootstrapping (sampling with replacement from the entire pool of neurons) fails because it assumes all observations are independent. In reality, neurons from the same mouse are more similar to each other than to neurons from a different mouse. The hierarchical bootstrap (or multi-level bootstrap) preserves this nested structure, ensuring your confidence intervals are not artificially narrow due to pseudoreplication.

To illustrate the problem, assume you have 100 neurons from Mouse A and 10 neurons from Mouse B, a simple bootstrap will be heavily biased toward Mouse A. Furthermore, the simple bootstrap ignores the fact that the true variance in your population comes from two sources:

(1) Between-mouse variance (differences in surgery, genetics, or behavior).

(2) Within-mouse variance (differences in tuning or activity between individual cells).

Hierarchical bootstrap addresses this problem, and is implemented as follows: To estimate the mean response while accounting for different sample sizes per mouse, a two-level resampling scheme is used

(1) Resample the higher level (Mice)

First, you account for the variability between animals.

Suppose you have N mice in total.

Randomly draw N mice with replacement from your original pool.

Note: Because this is with replacement, a single mouse’s data might be included multiple times in one bootstrap iteration, while another mouse might be left out entirely.

(2) Resample the lower level (Neurons)

For each mouse selected in Step 1, you must now account for the variability within that specific animal.

Look at the number of neurons actually recorded from that mouse (let’s call it k_i).

Randomly draw k_i neurons with replacement from that mouse’s specific pool of recorded cells.

This step is crucial: you always resample the same number of neurons that were originally recorded for that specific mouse. This maintains the "weight" or "influence" that animal had in the original dataset.

(3) Calculate the resampled statistic

Calculate the mean of all neurons collected in this “bootstrap sample”.

(4) Iterate

Repeat Steps 1–3 many times (typically B = 1,000 or 10,000 iterations).

The distribution of these B bootstrap means represents your sampling distribution and is used to calculate confidence intervals and p-values. 

(2) The authors should clarify how the problem of multiple comparisons was addressed for comparisons performed in multiple moments of time, where significance is indicated by a black bar (e.g. in Figure 2F).

There is no family-wise error correction in cases of comparing response time courses implemented in our analysis. If the reviewer has a good suggestion for how to implement family wise error correction, we would be happy to implement it. We are not aware of anything that is better than what we currently do (the time bin-wise comparison). To briefly explain the problem: In most neuroscience papers, response curves are compared by choosing a time window (e.g. 0.5 to 1 s following a trigger) and calculating mean values of the curves in these windows. This hides the problem of multiple comparisons that arises from the fact that the experimenter is free to choose a response window used for analysis. Note, this also creates a strong incentive to “optimize” choice of an analysis window – a part of the analysis that a reader is typically completely blind to. We could of course also choose an analysis window that sounds reasonable and yields significant differences for our analyses. However, to provide a more unbiased image of the data, we have come to do bin-wise comparisons with a fixed p-value (typically 0.05). This is used in all of our papers at the moment. Given that samples from neighboring timepoints are correlated via a combination of actual responses and a subset of noise sources, the samples are not independent. We now also implemented a correction for spurious positive values by requiring at least 2 neighboring bins to have a p-value below 0.05 to be shown. If the samples were independent, this would mean a false positive rate of 0.0025. Given that they are not, this is a lower bound only. Additionally, any family-wise error correction would be a function of the number of time bins we show in the plot. This would mean that our choice of the time window shown in a plot (-1s to +4s, or +5s, etc.) would change the p-value we consider significant. Thus, there is no explicit family-wise error correction, and we have come to the conclusion that the bin-wise comparison with a fixed p-value is the most unbiased representation of the data we can provide. The alternative would be to additionally plot z-scores or the p-values as a function of time, but in our experience these types of plots are even harder to read for readers not used to it.

(3) It would be helpful to add a figure in the Discussion summarising the functional connectivity suggested by all experiments.

We now added a panel that summarizes the functional connectivity observed in our experiments to Figure S10. 

(4) Throughout the manuscript, the authors use the term "teaching signals", but I am unclear what they mean by it: after reading the definition in lines 45-46, I thought that they corresponded to values (as they are compared to sensory signals). Later (428-430), the text suggests that they correspond to error neurons. But then lines 605-607 say it is not an error signal. The authors should define teaching signals very precisely or remove this term.

The formal definition of the teaching signal was in footnote 1 of the manuscript. We assume the reviewer may have missed this. We now moved this definition into the main text to increase clarity.

We use the term teaching signal to mean exactly this definition throughout the manuscript. We suspect, a second source of confusion may come from ambiguity in regards to anatomical vs. functional definitions. We have attempted to emphasize that the definition of teaching signal is a functional one, not an anatomical one (as is the case for ‘prediction’ – predictions are functionally defined, not anatomically – hence it makes sense to ask questions of the form “what are the potential sources of predictions” etc.). A teaching signal is a signal that is compared against a prediction (the ‘ground truth’ the prediction is compared and trained against). In different circuit implementations of predictive processing, different inputs function as predictions and teaching signals. In the hierarchical implementation, activity of the internal representation neuron at the lower level serves as a teaching signal for a prediction signal that is formed by the internal representation neuron from the higher level. In the non-hierarchical implementation, external inputs from the thalamus or other cortical areas serve as teaching signals for the respective prediction signals that are formed by internal representation neurons. This terminology is most intuitive when thinking from the perspective of a prediction error neuron, since a prediction error neuron computes the difference between two inputs signals – one of which functions as a teaching input, and the other one as a respective prediction. Hence, lines 428-430 specify that layer 5 input onto prediction error neurons of layer 2/3 serves as a teaching input.

Reviewer #2 (Public review):

Vasilevskaya and Keller set out to experimentally distinguish between two variants of predictive processing: a hierarchical and a non-hierarchical variant. The hierarchical variant assumes a hierarchical organization in which internal representation neurons (believed to be a subset of layer 5 excitatory neurons) serve as a source of a teaching signal for local prediction error neurons as well as for the next higher level of the hierarchy, while simultaneously providing prediction signals to the preceding lower level. In contrast, the non-hierarchical variant posits that these layer 5 internal representation neurons provide local predictions to layer 2/3 prediction error neurons.

The interaction between internal representation neurons and prediction error neurons differs fundamentally between the two variants. In the hierarchical variant, internal representation neurons excite positive prediction error neurons and inhibit negative prediction error neurons, while at the same time being inhibited by positive prediction error neurons and excited by negative prediction error neurons. In the non-hierarchical variant, this pattern of connectivity is reversed.

This work is very exciting, timely, and carefully executed. The authors functionally, and later molecularly, identify layer 2/3 prediction error neurons in V1 and probe their interactions with genetically defined neuron types in cortical layers 5 and 6 using optogenetics. They demonstrate that the functional influence of putative prediction error neurons in layer 2/3 onto layer 5 is incompatible with the hierarchical variant, whereas the influence of layer 5 onto putative prediction error neurons in layer 2/3 is incompatible with the non-hierarchical variant. They then test an alternative hypothesis, in which layer 2/3 responses resemble prediction errors with respect to perturbations of artificial layer 5 activity patterns. To investigate this, they designed an experiment in which optogenetic activation of L5 IT neurons was closed-loop coupled to the mouse's locomotion speed in the absence of visual feedback, allowing them to probe the causal influence of L5 activity on layer 2/3 responses.

Finally, the authors hypothesize that their data are more consistent with a joint embedding predictive architecture (JEPA) and outline experimentally testable predictions arising from this framework.

We thank the reviewer for their comments. We address them below.

While the work is overall convincing and significantly advances our understanding of the circuit-level implementation of predictive processing, there are a few weaknesses that should be addressed or discussed:

(1) The authors define putative positive prediction error neurons as the 15% of neurons most responsive to grating onset and putative negative prediction error neurons as the 15% most responsive to visuomotor mismatch. While this selection would be expected to overlap with negative and positive prediction error neurons, the criterion is not sufficiently stringent (independent of the exact percentage chosen). In particular, classification of a neuron as a prediction error neuron should ideally be accompanied by evidence that it does not exhibit a significant increase in activity when the prediction matches the sensory input or teaching signal.

We understand the reviewer’s intuition. We can indeed use other stimuli to identify prediction error neurons, like the relative suppression of responses in closed-loop running onset vs open-loop running onsets. This was the reason behind including Figure S1, to show that our selection results in expected pattern of running onset responses. We don’t typically use the running onset responses as they have an additional confound we have not fully understood. This is that running onset always tends to result in an increase of calcium activity in all neurons. This could have a variety of reasons: A) Contamination of hemodynamic occlusion signals (blood vessels tend to constrict at running onset, making it appear like an increase in calcium activity) – see Yogesh et al., 2025. B) The virtual coupling in our VR is not good enough to provide a true “closed loop” experience. Humans typically notice lags of larger than 30ms – in our VR it is approximately 100 ms. C). Running onset in head-fixed animals is not accompanied by a vestibular input. D) Predictive processing is wrong. We tend to think it is a combination of the three.

We can also use combinations of the two criteria to select neurons - if the reviewer has a specific selection criteria in mind (top XXX% MM responsive AND top XXX% closed-loop suppressed, etc.) we are happy to repeat the analysis for that specific set of criteria, but the fundamental problem that we are using a functional response to select these neurons does not go away. We know that our functional selection criteria mean we select a population of neurons that is enriched for prediction error neurons. If the enrichment is too weak, we would expect to find no effects in terms of functional influence. It is hard to explain, however, how a weak enrichment could result in a strong effect on functional influence. Our arguments in more lengthy form, for why the visuomotor mismatch is a good stimulus to identify negative prediction error neurons can be found here: Attinger et al., 2017; Jordan and Keller, 2020; Leinweber et al., 2017; O’Toole et al., 2023; Vasilevskaya et al., 2022; Zmarz and Keller, 2016.

(2) The authors "speculate that the prediction error responses in layer 2/3 may not be computed with respect to sensory input, but with respect to layer 5 activity as a teaching signal." However, it is unclear how this perspective differs from earlier statements in the manuscript. In the Introduction, the authors note that "these signals, typically referred to as sensory signals, we will refer to as teaching signals," and later describe the hierarchical variant as one "in which internal representation neurons act as a source of the teaching signal." Given this framing, it is difficult to identify what is conceptually novel in the updated view. Is the key distinction that layer 2/3 neurons are now proposed to generate predictions in an internal representation space rather than in sensory input space, as briefly suggested in the Discussion? Or are the authors introducing a distinction between an external (sensory) and an internal (cortical) teaching signal? If so, this distinction should be made explicit. Clarifying this point would considerably strengthen the manuscript.

There might be a misunderstanding regarding our usage of the term teaching signal. In hierarchical predictive processing the teaching signal is typically referred to as a sensory signal, as e.g. in: “prediction error neurons compare predictions to sensory input”. In non-hierarchical predictive processing, or far away from the sensory input (think prefrontal cortex), or for cross-modal interactions “sensory” input is misleading. Also, in non-predictive-processing type models (like JEPA), sensory input has a different functional role. Thus, we operationally define teaching signal as the signal that is compared against the prediction by prediction error neurons.

The two primary options we are comparing are:

(1) Is the teaching signal to the L2/3 comparator a bottom-up input to V1 (as one would expect in predictive processing). 

(2) Is the teaching signal to the L2/3 comparator L5 input (as one would expect in JEPA).

Our data argue in favor of option 2. We have rephrased parts of the manuscript to try to make this clearer. 

(3) The authors propose that "L2/3 neurons predict L5 activity, hence making predictions in the internal representation space rather than the input space," and further suggest that, since both deep and superficial cortical layers receive thalamic input, the cortex may function like a JEPA. This idea appears closely related to the model introduced by Nejad et al. (2025), which effectively implements a JEPA-like architecture: L5 activity serves as a target against which L2/3 predictions are compared in a selfsupervised manner, with both L5 and L2/3 (via L4) receiving thalamic input. It would be helpful for the authors to clarify how their framework differs from that model, and to specify the key conceptual or mechanistic distinctions between the present proposal and the approach described by Nejad et al.

The two proposals indeed share similarities in assuming that bottom-up input for both L2/3 and L5 arrives from thalamus, and that representations formed in L2/3 are used for predicting the activity of L5. However, there are a few important differences between the JEPA implementation proposal formulated here and the Nejad et al. model.

(1) There is no proposed mapping of computations in the Nejad et al. model onto different JEPA networks. We assume that the suggested mapping would be L4 and L5 as encoder networks, and L2/3 as a predictor network? In that case, it is different to our proposal, in which L2/3 is part of the encoder network.

(2) Our proposal contains explicit prediction error neuron cell types within L2/3, while prediction errors in Nejad et al. are encoded in the gradients, and the layer origin of these signals is hypothesized to be L5 (‘the learning-driving error signal originates in L5’). Hence, also the role of L5-L2/3 connection is distinct between the two proposals. In Nejad et al. this connection serves the role of error propagation and update for predictions in L2/3, while in our proposal this connection contains teaching signal (target representations) that are compared to predictions within L2/3. Similarly, the functional role of L2/3-L5 connection is also different, since in Nejad et al, it is supposed to carry predictions of L5 activity, whereas in our proposal we expect it to drive plasticity in L5 encoder.

(3) The difference outlined above also makes it evident that the two proposals should differ in how deep and superficial layers are expected to influence the activity of one another. Indeed, the proposal in Nejad et al. is based on the cortical column idea, and according to eq. 2 and 3 in the Methods, activity in L5 is a function of activity in L2/3, while activity in L2/3 is not a function of activity in L5. Our proposal is based on idea of layers forming parallel networks, where horizontal communication is the dominant mode of cortico-cortical interactions, and activity in deep layers serve as a teaching signal for L2/3. In our case, we expect the opposite - that activity in L2/3 depends on activity of L5, while activity of L5 is not immediately dependent on activity of L2/3 (only via plasticity route). This led us to propose one of direct tests for our framework – silencing L2/3 in a familiar setting should result in no immediate changes to L5 activity and behavior of the animal.

(4) The proposal in Nejad et al. relies on input reconstruction or variance maximization within the L5 autoencoder network to avoid collapse. Instead, our proposal has no reconstruction objective.

(5) Lastly, there is a time delay between inputs to L5 and L2/3 that is proposed in Nejad et al., while this is not something inherent to our proposal.

We expect that the most useful future models should move beyond JEPA, with the emphasis on nonhierarchical models capable of operating on arbitrary graphs. We think cortex functions according to principles of a JEPA (predictions in latent space), and that the role of cell types and the exact computational organization remain to be constrained.

REFERENCES

Attinger, A., Wang, B., Keller, G.B., 2017. Visuomotor Coupling Shapes the Functional Development of Mouse Visual Cortex. Cell 169, 1291-1302.e14. https://doi.org/10.1016/j.cell.2017.05.023

Grill, J.-B., Strub, F., Altché, F., Tallec, C., Richemond, P.H., Buchatskaya, E., Doersch, C., Pires, B.A., Guo, Z.D., Azar, M.G., Piot, B., Kavukcuoglu, K., Munos, R., Valko, M., 2020. Bootstrap your own latent: A new approach to self-supervised Learning. https://doi.org/10.48550/arXiv.2006.07733

Jordan, R., Keller, G.B., 2020. Opposing Influence of Top-down and Bottom-up Input on Excitatory Layer 2/3 Neurons in Mouse Primary Visual Cortex. Neuron 108, 1194-1206.e5. https://doi.org/10.1016/j.neuron.2020.09.024

Leinweber, M., Ward, D.R., Sobczak, J.M., Attinger, A., Keller, G.B., 2017. A Sensorimotor Circuit in Mouse Cortex for Visual Flow Predictions. Neuron 95, 1420-1432.e5. https://doi.org/10.1016/j.neuron.2017.08.036

Mohammadi, A.G., Halvagal, M.S., Zenke, F., 2025. Understanding cortical computation through the lens of joint-embedding predictive architectures. https://doi.org/10.1101/2025.11.25.690220

O’Toole, S.M., Oyibo, H.K., Keller, G.B., 2023. Molecularly targetable cell types in mouse visual cortex have distinguishable prediction error responses. Neuron 111, 2918-2928.e8. https://doi.org/10.1016/j.neuron.2023.08.015

Saravanan, V., Berman, G.J., Sober, S.J., 2020. Application of the hierarchical bootstrap to multi-level data in neuroscience. Neurons Behav. Data Anal. Theory 3, https://nbdt.scholasticahq.com/article/13927-application-of-the-hierarchical-bootstrap-tomulti-level-data-in-neuroscience.

Vasilevskaya, A., Widmer, F.C., Keller, G.B., Jordan, R., 2022. Locomotion-induced gain of visual responses cannot explain visuomotor mismatch responses in layer 2/3 of primary visual cortex. https://doi.org/10.1101/2022.02.11.479795

Yogesh, B., Heindorf, M., Jordan, R., Keller, G.B., 2025. Quantification of the effect of hemodynamic occlusion in two-photon imaging of mouse cortex. eLife 14, RP104914. https://doi.org/10.7554/eLife.104914

Zmarz, P., Keller, G.B., 2016. Mismatch Receptive Fields in Mouse Visual Cortex. Neuron 92, 766–772. https://doi.org/10.1016/j.neuron.2016.09.057

Author response:

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

We sincerely thank the reviewers and the Reviewing Editor for their careful evaluation of our manuscript and for their constructive and insightful comments. Their suggestions have helped us to improve the clarity, rigor, and presentation of our work. In response to these comments, we have substantially revised the manuscript and performed several additional analyses and experiments, as summarized below.

Major additions and modifications made during revision

In response to the reviewers' comments, we have substantially revised the manuscript and performed several additional analyses and experiments:

New analyses

- Quantification of MyoF recovery following auxin washout using MyoF-mAID-HA immunofluorescence (Figure 8B, Figure S10D).

- Quantification of maternal MIC2 fluorescence intensity following 24 h MyoF depletion and subsequent redistribution after auxin washout (150 micronemes per condition; Figure S10A,B).

- Pearson correlation analysis of ANKER1-Halo and HDEL-GFP localization (Pearson's R = 0.92 ± 0.04; n = 30 parasites).

- Additional probability-based analysis supporting regulated microneme inheritance.

- Expanded analysis of microneme redistribution across larger replication stages (Figure S5D).

New figures

- Figure S6: Dual-labelling analysis of additional Group 2 organelles (ER, apicoplast, glideosome).

- Figure S10A, B: MIC2 fluorescence intensity analysis following RB retention and redistribution.

- Figure S10D: Correlation between MyoF recovery and phenotype rescue.

- Figure S11: Schematic overview of quantification and analysis workflow.

Additional experimental efforts

- Generation of a MIC2-Halo / IMC1-mKATE / Cb-Emerald parasite line to improve visualization of RB-associated trafficking.

- Multiple attempts to perform higher-temporal-resolution live-cell imaging. However, prolonged acquisition resulted in severe phototoxicity, replication arrest, and parasite death, preventing reliable long-term recordings.

Textual and methodological revisions

- Expanded Materials and Methods section with detailed descriptions of fluorescence quantification, colocalization analyses, and statistical procedures.

- Re-evaluation of statistical analyses using two-tailed tests throughout.

- Revision of manuscript text to clarify the evidence supporting RB-associated trafficking and to better acknowledge current limitations.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work asks the question of how different organelles and structures in the apicomplexan parasite Toxoplasma gondii are recycled and/or segregated to the daughter cells during cell replication. In particular, they consider an unusual cell structure called the residual body that links replicating cells during the intracellular infection stage of this parasite. The residual body has historically been considered a 'dumping ground' for unnecessary relics of the mother cell during division, but this notion is increasingly being revised. Indeed, cell replication in Toxoplasma is often misinterpreted as cell division (cytokinesis), but in fact, the cell replicates its organelles and structures to multiple 10s of copies in seemingly distinctly formed daughter cells, but cytokinesis is delayed for many such cycles and typically only occurs simultaneously with parasite egress from its host cell. The residual body is, in fact, the connection between these pre-cytokinetic replicated daughters, and effectively, this is still a single cell at this stage. The authors have previously shown that an actin network extends through the residual body between these daughter cells, and ER and mitochondria common to all cells are also linked through this structure. This study examining the fates of organelles during cell replication is timely for continuing our understanding of how this fascinating component of the cell participates in these processes. The authors use Halo-tags as their principal tool to track discrete populations of proteins, labelling their organelle locations, and this provides beautiful insight into these processes.

Strengths:

Using dyes conjugated to Halo tags, this work elegantly tracks the fates of proteins synthesised by an original 'mother' cell over several replication cycles of pre-cytokinetic 'daughters'. Using this tool, they show that some organelles are made intact just once and that some of these can be subsequently sorted to the daughters (micronemes and rhoptries) while others are dismantled (IMC) and the daughters must make their own. A third set of organelles (largely synthesis, sorting, and metabolic compartments) is divided and inherited, and new daughter-synthesised proteins are added to the preexisting maternal proteins in these structures. A role for actin and myosin is clearly demonstrated for micronemes and rhoptries, and this correlates with their relatively late inheritance into the developing daughters. Overall, this work gives clarity to the behaviours of several cell structures during replication and paves the way to a better understanding of the mechanisms that drive the differences between structures and the universality of these processes in other apicomplexan parasites.

Weaknesses:

In addressing the question of residual body participation in sorting of organelles, it would be useful to clearly define this structure and when and where it is delineated from the posterior of a mother cell during the formation of daughter structures. This might seem like a moot point, but it would give clarity to notions of recycling and 'reservoirs'. Mother cells retain their active invasion apparatus until very late in daughter formation, and the need for micronemes and rhoptries to be released from this service late in the process might explain why they are only then trafficked to the cell posterior and then into the daughters. So, is this a distinct 'residual body' body function/reservoir or just a spatial constraint of this sequence of daughter formation? In subsequent cell replications (4, 8, 16... stages), is there a separation between the residual body that links them all and the posterior of each new 'mother cell', and if so, when is this distinction lost? This is important because without a definition, we might be confusing different processes.

We thank the reviewer for this excellent and thoughtful question. The residual body (RB) emerges at the end of the first replication cycle, where it is delineated by the basal complex and persists as an IVN-associated compartment connecting all daughter parasites through both plasma membrane and cytoplasm. Previous EM and live-cell studies, including ours, have shown that the RB is not a passive remnant but a dynamic structure dependent on F-actin and unconventional myosins, supporting recycling, inter-parasite connectivity, and synchronous growth (Delbac et al., 2001; Muñiz-Hernández et al., 2011; Frénal et al., 2017; Periz et al., 2017).

In the present study, the MyoF reversibility experiment provides strong support for a model in which RB functions as an active recycling hub. Upon MyoF depletion, maternal microneme and rhoptry proteins accumulate within the RB. Following restoration of MyoF expression, this material is redistributed to daughter organelles. We interpret this reversible phenotype as evidence that the RB represents a distinct and regulated trafficking intermediate rather than simply a by-product of late daughter cell formation.

We agree with the reviewer that mother cells retain a functional invasion apparatus until very late during daughter formation, and that the delayed release of micronemes and rhoptries likely contributes to their late trafficking toward the cell posterior. However, our data indicate that once released, these organelles transit through a defined RB compartment that actively participates in their recycling rather than merely reflecting positional constraints. This has been previously well illustrated for micronemes, which are trafficked along F-actin filaments within the residual body (Periz et al., 2019).

At later rounds of replication (4, 8, 16 parasites), previous studies have demonstrated the presence of multiple residual body centres within the same vacuole. However, the precise temporal and structural distinction between the RB linking parasites within the vacuole and the posterior of newly formed mother cells remains insufficiently resolved and is beyond the scope of the present study. Importantly, available ultrastructural and live-cell imaging supports the persistence of shared RB compartments connecting parasites within a vacuole, arguing against a simple conflation of posterior membranes and residual body material.

While the primary aim of the current work was to investigate the RB's role in organelle recycling, we fully agree that a more precise definition of when and how the RB is formed, remodelled, and ultimately resolved during successive replication cycles will be essential to distinguish recycling from spatial constraints. We have revised the Discussion to better acknowledge this limitation and to avoid overinterpreting the role of the RB in organelle inheritance.

Are rhoptries/micronemes that originate in one 'mother' able to be sorted to the 'daughters' from a distinct mother in this syncytium? If so, this would make it a sorting centre, but otherwise we could be just capturing the activities at the posterior of any given cell during replication. The authors' further thoughts on this would be very interesting.

We agree with the reviewer that our current data do not definitively demonstrate whether rhoptries or micronemes originating from one “mother” parasite can be redistributed to daughters derived from another mother within the same syncytial vacuole. Nevertheless, our MyoF chase experiments are consistent with a model in which the RB/IVN functions as an active recycling and sorting hub rather than simply representing posterior trafficking events associated with individual parasites.

Upon MyoF depletion, maternal micronemes accumulated within the RB. Following restoration of MyoF expression, these accumulated micronemes were subsequently redistributed to daughter parasites. This reversible redistribution is more consistent with an active recycling process than with passive accumulation alone.

To further support this interpretation, we expanded the analysis presented in Figure S5 by including additional vacuoles and larger replication stages (new panel D). These analyses show that maternal micronemes are redistributed broadly and relatively evenly among daughter parasites. We additionally performed a probability-based analysis demonstrating that the recurrent and homogeneous redistribution patterns observed are highly unlikely to arise from stochastic capture events occurring independently at the posterior end of each parasite during replication. Together, these analyses support the interpretation that microneme redistribution is a regulated process.

Direct demonstration of recycling between all parasites within a vacuole would require a system allowing simultaneous differential labeling of (i) daughter parasites derived from a specific mother cell and (ii) the maternal organelles originating from that same mother during a subsequent replication cycle. To our knowledge, such an approach is not currently technically feasible. Nevertheless, our live-cell imaging experiments provide additional support for communal redistribution, as microneme material accumulated within the RB was subsequently observed redistributing, albeit unevenly, across multiple tachyzoites within the same vacuole.

The Group 2 structures are described as those that are divided between daughters and receive newly synthesised proteins that add to the maternal protein of these compartments. While this is a logical conclusion for several that are mentioned, where the maternal protein signal is seen to be depleted with replication (including for the apicoplast, ER, glideosome, and Golgi). Data for the addition of new proteins to these existing structures is actually only presented in direct support of this for the Golgi.

We thank the reviewer for this important clarification. We initially selected the Golgi as a representative example because its morphology and restricted localization provide the clearest visualization of the dual-labeling dynamics. However, the same experimental approach was applied to all Group 2 organelles analyzed in this study. To address the reviewer's concern more directly, we have now included a new supplementary figure (Figure S6) showing that the same pattern is also observed for the apicoplast, ER, and glideosome.

We would also like to clarify that the maternal protein signal is not lost during replication but instead becomes progressively diluted as these organelles expand, are partitioned into daughter parasites, and incorporate newly synthesized proteins. The Golgi was originally highlighted because these dynamics are most readily visualized in this compartment; however, the same principle applies to all Group 2 organelles analyzed in this study, as now illustrated in Figure S6.

Reviewer #2 (Public review):

Summary:

Toxoplasma gondii is an obligate intracellular parasite and the causative agent of Toxoplasmosis. Parasite invasion into host cells, intracellular replication, and then egress, which results in the destruction of the infected cell, is central to pathogenicity. This manuscript focuses on understanding how maternal resources (in this case, cellular organelles) are shared between daughter parasites during cell division. Many organelles are single copy, meaning that division and inheritance by the daughters is crucial for successful replication. The major strength of this study was the use of a Halobased pulse chase assay to characterize patterns of organelle inheritance. The results show that both microneme and rhoptries (secretory vesicles) previously thought to be synthesized de novo are inherited by daughter parasites. Thus, this paper adds new insight to our understanding of cell division in this important parasite.

Strengths:

This study demonstrated that pulse labeling of proteins can be used to monitor protein synthesis, turnover, and movement. This approach will be of great interest to the field. Using this method, the authors demonstrate three main modes of organelle inheritance.

(1) Organelles, where there are multiple copies (such as secretory vesicles, micronemes, and rhoptries), are divided between the daughter parasites, with additional contribution of newly formed vesicles. New and old material remain as separate entities in the cell.

(2) Single-copy organelles, which are expanded to include newly synthesized material prior to division, such as the Golgi and apicoplast.

(3) Cytoskeletal structures that are synthesized anew during each round of division. These studies provide more refined insight into patterns or organelle inheritance and demonstrate that secretory organelles are not made de novo during each round of division as previously thought. The paper has a logical flow, and overall, the data is presented in a clear and organized fashion.

Weaknesses:

(1) Descriptions of methodology and statistical analysis were incomplete.

We agree with the reviewer that the description of the methodology and statistical analyses required further clarification. To address this, we have added a new supplementary figure (Figure S11) illustrating the experimental workflow, quantification strategy, and analysis pipeline. We have also expanded the Materials and Methods section to provide detailed descriptions of the experimental design, fluorescence quantification procedures, statistical analyses, and the number of biological replicates. These revisions provide a clearer and more comprehensive description of the methodology and data analysis.

(2) There are inconsistencies between the data in Figures 1 and 5. In Figure 1, a small amount of maternal IMC is visible in stage 2 parasites. Although this is a ~90% reduction, these parasites should be quantified as parasites with material IMC. However, the graph in Figure 5C indicates that no material parasites have GAPM1a, given that graph 5C is a binary measure (present vs. absent), one would expect a non-zero percent of parasites to have maternal material.

We agree with Reviewer 2 that, based on the raw fluorescence signal, one might expect a non-zero percentage of parasites to retain maternal IMC material after the first replication. The apparent discrepancy between Figures 1 and 5 reflects our thresholding strategy rather than inconsistent data.

Figure 5C presents a binary analysis (presence versus absence) using a threshold calibrated from stage 1 parasites and applied uniformly across all markers. Under this criterion, the residual GAPM1a signal after the first replication falls below the detection threshold, resulting in 0% positive vacuoles. Although normalization to stage 2 parasites would detect this weak residual signal, such a protein-specific threshold would compromise direct comparison across the dataset.

To clarify this point, we have updated the Figure 5C legend to explain the analytical approach and the asterisk associated with GAPM1a. The residual maternal IMC signal visible in Figure 1 represents a rare example selected to illustrate the remaining ~10% signal and is consistent with the absence of detectable maternal IMC1 after replication in Figures 2C and 5E.

(3) The conclusion from Figure 6 was not justified based on the data. I agree with the author's conclusion that the accumulation of micronemes and rhoptries in the residual body was timedependent. In Figure 6A, the signal observed in the residual body at times 6:30, 13, and 14 hours is not observed in subsequent time points. However, the fate of these micronemes and rhoptries is unclear. It cannot be concluded that these vesicles are recycled back to the mother. They could also have been degraded. In fact, the graphs of microneme inheritance in Figure 2B show a decrease in maternal signal from 100% to 80% between stages 1 and 2, indicating that some microneme degradation is taking place.

We agree with the reviewer that Figure 6 alone does not definitively establish the fate of micronemes and rhoptries accumulating within the residual body (RB), and that both recycling and degradation remain possible interpretations. Our conclusion that maternal micronemes are predominantly recycled is therefore based on the integration of Figure 6 with our MyoF depletion and recovery experiments, additional quantitative analyses, and previous work demonstrating F-actin-dependent microneme trafficking through the RB (Periz et al., 2019).

Consistent with this model, MyoF depletion results in the accumulation of maternal micronemes within the RB, whereas restoration of MyoF expression following auxin washout leads to their redistribution across multiple tachyzoites within the same vacuole (Figure 8). Furthermore, maternal microneme signal remains detectable even after prolonged MyoF depletion (up to 48 h) and multiple rounds of replication (Figures 7 and 8), arguing against extensive degradation.

To further address this possibility, we quantified the fluorescence intensity of individual maternal MIC2-positive micronemes retained within the RB after 24 h of MyoF depletion and following redistribution after auxin washout (150 micronemes per condition). No significant difference in fluorescence intensity was observed compared with control maternal micronemes (Figure S10A,B), indicating that maternal microneme signal is preserved during RB retention and redistribution.

We therefore interpret the decrease in maternal microneme signal observed between stages 1 and 2 in Figure 2B primarily as a consequence of redistribution and dilution rather than degradation, consistent with the stable fluorescence intensity of individual micronemes (Figure 3). Regarding rhoptries, we note that the majority (~90%) are incorporated into daughter parasites before budding is complete, limiting their accumulation within the RB and suggesting that RB-associated trafficking primarily reflects redistribution rather than bulk degradation.

(4) To convincingly demonstrate that the redistribution of micronemes and rhoptries was due to recovery of MyoF protein levels after auxin washout, a Western blot should be performed to show MyoF protein levels over time. In addition, the decrease in mMIC2 protein levels in the residual body in Figure 8F should be measured and normalized for photobleaching. Both apical and basal signals appear to be reduced over the time course of imaging.

We agree with the reviewer that demonstrating MyoF recovery following auxin washout is important. Rather than performing a Western blot, we monitored MyoF recovery by immunofluorescence using the HA tag in the MyoF-mAID-HA strain, allowing direct correlation between MyoF reappearance and microneme redistribution at the single-vacuole level. These data are now included in Figure 8B, with the corresponding MyoF presence–phenotype association analysis presented in Figure S10D.

Regarding photobleaching, we agree that fluorescence loss during time-lapse imaging is an important consideration. However, in this experiment, changes in fluorescence intensity reflect not only photobleaching but also biological redistribution of micronemes and movement of parasites in and out of the imaging plane. In the absence of a stable internal reference fluorophore, applying a standard photobleaching correction could therefore introduce additional inaccuracies. For this reason, we did not quantify fluorescence intensity during the redistribution phase.

Instead, to assess whether maternal microneme signal is lost during RB retention and redistribution, we quantified the fluorescence intensity of individual maternal MIC2-positive micronemes following 24 h of MyoF depletion and subsequent auxin washout (Figure S10A,B). No significant difference was observed compared with control maternal micronemes, supporting the conclusion that redistribution occurs without substantial loss of the maternal microneme pool.

Reviewer #3 (Public review):

Summary:

Knoerzer-Suckow et al. explore the mechanisms of organelle inheritance during endodyogeny in Toxoplasma gondii using an innovative dual-labeling approach to track the distribution of maternal organelles into daughter parasites. They can clearly distinguish between maternal and daughterderived organelles using their dual-labeling Halo Tag approach. They reveal that different organelles are trafficked to daughter parasites in three broad patterns, which they have binned into groups. Their findings reveal a role for MyoF in the inheritance of micronemes and rhoptries, and notably, they observe that the inner membrane complex (IMC) is not recycled. Instead, the IMC undergoes a pronounced relocalization to the posterior of the maternal cell, where it is likely targeted for degradation.

Strengths:

The data surrounding their MyoF knockdown experiments, IMC degradation, and trafficking of MIC2 after auxin washout are compelling. These data add to the knowledge of how organelle inheritance occurs in T. gondii, increasing the field's understanding of endodyogeny.

Weaknesses:

(1) The evidence provided to support the claim that microneme and rhoptry inheritance specifically traffics through the residual body does not sufficiently substantiate the claim. The temporal resolution of the imaging is inadequate to precisely trace the path of microneme and rhoptry inheritance. From the data shown in the manuscript, it can be concluded that at least some of the micronemes and rhoptries might be recycled through the residual body, but it is unclear whether many or most of these organelles do so.

We thank the reviewer for this important comment and refer also to our response to Reviewer 1 above.

Previous work has demonstrated F-actin-dependent trafficking of micronemes within the residual body (RB) (Periz et al., 2019). Consistent with these findings, our data support a model in which RB-mediated trafficking contributes to maternal microneme recycling. We acknowledge, however, that the temporal resolution of our imaging does not allow continuous tracking of every individual organelle throughout the entire replication process.

In contrast, our observations indicate that the majority of maternal rhoptry material is incorporated into daughter cells before replication is complete and therefore does not necessarily transit through the RB under normal conditions (Figure 6). Nevertheless, rhoptry inheritance remains dependent on the actin–MyoF trafficking machinery, as MyoF depletion results in the accumulation of rhoptry material within the RB (Figures 6 and 7).

Taken together, our data support a model in which the RB serves as an important recycling hub for maternal micronemes and can, under conditions of impaired trafficking, also transiently accommodate rhoptry material. However, our imaging resolution does not allow us to conclude that all microneme or rhoptry inheritance obligatorily transits through the RB, and we have revised the manuscript to reflect this limitation more explicitly.

(2) The absence of specific markers for the residual body brings into question whether microneme inheritance occurs through a discrete residual body or simply via the basal end of the maternal parasite. The authors need a robust way to visualize and define the residual body to claim that micronemes and rhoptries are specifically transported through this structure.

We agree with the reviewer that the absence of a dedicated residual body (RB) marker remains a limitation and that such a tool would improve the precision of our analyses. To date, no specific RB marker has been identified (see also our response to Reviewer 1). The most reliable proxy currently available is the F-actin chromobody, which labels the dense F-actin network associated with the RB. Using this approach, previous work demonstrated F-actin-dependent trafficking of micronemes within the RB (Periz et al., 2019).

Building on these findings, our data support a model in which RB-associated trafficking contributes to maternal microneme recycling, whereas rhoptries are more frequently incorporated directly into daughter cells without obvious RB transit. In addition, functional perturbation of the actin–MyoF transport machinery, through MyoF depletion and subsequent recovery, supports the interpretation that the RB represents a discrete actin-associated compartment involved in organelle redistribution. Nevertheless, we acknowledge that our current imaging resolution does not allow us to determine the extent to which all microneme or rhoptry inheritance occurs through the RB, and we have revised the manuscript accordingly.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comments for revision where either the clarity or accuracy could be improved:

(1) The methods could do with some further detail with respect to the fluorescence intensity measurement. For example, where the Z-series was taken, and for measurements, were maximum projects taken or single Z-planes? Were all measurements made on unprocessed images, or was any deconvolution, etc, undertaken?

We updated the Materials and Methods for better clarity and now read as: “Parasites were labeled as described above and allowed to replicate for 24 h on HFF-coated Ibidi live-cell dishes. Approximately 15 fields of view were imaged using Z-stacks spanning 3 μm centred on the vacuoles. For each replication stage (1, 2, 4, and 8 parasites per vacuole), individual tachyzoites were sampled across multiple vacuoles.

Maximum-intensity projections were generated from non-deconvolved images. Fluorescence intensity (FI) was quantified as the maximum grey value measured within regions of interest (ROIs) drawn on individual tachyzoites from each vacuole stage. ROIs excluded overlapping parasites, neighbouring vacuoles, and regions with atypical signal intensity. For each biological replicate, up to 25 tachyzoites per replication stage were analyzed, and the mean FI value was calculated for each stage. The highest mean FI observed among the stages within a replicate was defined as 100%, and FI values for the other stages were expressed relative to this maximum. Relative FI values were then averaged across three independent biological replicates. Data are presented as mean ± SD.”

(2) Line 93: Is more JF549 added at each of stages 2, 4, and 8? I assume so to get the progressive increase, but it would help to clarify this here.

As illustrated in Figure 1a, the second dye is added only once, after 24 h of replication, and is then washed off before imaging. It is not maintained throughout the replication steps. The observed increase in signal is related to the presence of newly synthesized (de novo) proteins generated during replication. The Halo tags of these new proteins are initially free of ligand, as no ligand is present during replication. During the second labelling step, all free Halo tags can bind the dye. The signal intensity at each replication step therefore reflects the amount of de novo material present, which is higher at step 4 than at step 2, because the proteins generated de novo during stage 2 are also present in stage 4. The signal will be determined by both the number of newly produced molecules and their concentration at the same localization.

(3) Line 103: Check that the Carruthers and Sibley, 1997, ref for Tic20 in the apicoplast is correct. I don't think this could be correct given the date.

The reference it will be corrected to G van Dooren et al. 2008.

(4) Figure legends: It would be useful to state what form of microscopy was used in each figure.

Following the reviewer's advice the legends has been updated.

(5) Figure 2, S2: How are single organelles tracked, such as rhoptries? I'd assume that a cell will gain new de novo organelles as well, and that this would reduce the signal per cell. Stage 2 has a rhoptry signal in both daughters, so I'd expect the signal to be roughly half for the whole cell, unless the authors can resolve individual rhoptries (which would surprise me with this microscopy). If individual rhoptries were resolved, how was this done, and what was the confidence in this (were there controls?)

We thank the reviewer for this important point. We do not resolve individual rhoptries with the imaging conditions used in this study. Instead, fluorescence intensity was measured as the maximum grey value within a representative region of interest (ROI) encompassing the apical rhoptry signal while excluding overlapping parasites and regions with atypical fluorescence intensity. The same ROI selection strategy was applied consistently across all replication stages, allowing direct comparison with stage 1 parasites.

The analyses presented in Figures 3 and S2 show an increasing proportion of tachyzoites lacking detectable maternal rhoptry signal as replication progresses, while the fluorescence intensity of the remaining maternal signal remains relatively stable. Together, these observations are consistent with the redistribution of intact maternal rhoptries rather than a progressive loss of rhoptry fluorescence. 

(6) Line 150: it is unclear what is meant by 'regulated partitioning'. The more equal inheritance of micronemes versus rhoptries might not indicate a 'regulated partitioning' but just a more uniform distribution, given the larger number of micronemes versus rhoptries.

We agree with the reviewer that this statement required clarification, and we have revised the text accordingly. Our intention was to emphasize that microneme inheritance appears to be a regulated process, rather than to directly compare it with rhoptry inheritance. The observed differences between these organelles are likely influenced, at least in part, by their different abundances.

Across successive rounds of replication, daughter parasites consistently inherit comparable amounts of maternal micronemes, even at later replication stages (Figure S4). Given that a single mother parasite contains approximately 30–40 micronemes, whereas successive rounds of endodyogeny can generate up to 32 daughter parasites, a purely stochastic segregation would be unlikely to produce the relatively uniform distribution observed (~1–2 maternal micronemes per tachyzoite). To support this interpretation, we performed an additional probability-based analysis, which indicates that the observed redistribution patterns are unlikely to arise by chance alone. We therefore interpret these findings as supporting the existence of mechanisms that promote balanced microneme inheritance during parasite replication.

(7) Line 184: How is the maternal signal measured without detecting the internal daughter signal? Is this an average signal for the full parasite, or just for a cross-section of the IMC? And if the latter, how are the different profiles of mother and daughter accounted for? Also, the abbreviation in the brackets doesn't make sense here.

We thank the reviewer for this important point. We have revised the Materials and Methods section to provide a clearer description of the fluorescence intensity (FI) measurements and added a new supplementary figure (Figure S11) illustrating the analysis workflow.

Briefly, FI measurements were performed on maximum-intensity projections generated from Z-stack images without deconvolution. A representative region of interest (ROI) was selected, and the maximum grey value was used for quantification. This approach minimizes variability arising from differences in ROI size and provides a robust metric for comparison across replication stages.

Daughter cell fluorescence was measured using the same approach while excluding overlapping signals from neighboring daughter cells and the maternal IMC. Maternal and daughter signals were distinguished based on their spatial localization and fluorescence labeling. Finally, the abbreviation in brackets has been corrected for clarity.

(8) Line 191: Subheading a bit unclear. Distinct from other organelles, or are miconeme and rhoptry pathways distinct from each other?

We agree with the reviewer and have updated the subheading to “Whole-organelle inheritance of micronemes and rhoptries occurs via distinct recycling pathways”

(9) Line 193: The site of disassembly of the IMC (suggested RB here) might not be the same as the site of degradation. I suggest using 'disassembly' instead here.

We agree that “disassembly” is an appropriate term to describe the breakdown of the IMC at the residual body (RB). However, we also believe that the RB represents the primary site of IMC degradation, for two reasons. First, if IMC material were not degraded at this site, we would expect to detect Halo-positive signal elsewhere following IMC collapse, which we do not observe. Second, transport of IMC material to an alternative degradation site would be required, but no IMC-positive vesicles are observed, arguing against significant redistribution. Together, these observations support the conclusion that the RB is both the site of disassembly and degradation of maternal IMC.

(10) Line 215: The conclusion for a difference in timing of microneme and rhoptry segregation is not clearly supported by the data presented. Also, if there are more micronemes than rhoptries, then the frequency of observing a microneme being trafficked through the RB would need to be higher than for rhoptries if the mechanisms were the same. So, a difference in frequency here cannot be used to argue for a different mechanism.

We agree with the reviewer and the text have been edited to soften our conclusion. 

(11) Line 234: 'segregation' might be a better term than 'recycling' here because it is actually the sorting into daughter cells that is the important process.

The text have been edited

(12) Line 235: I don't think this can be what the authors intend to say. If the maternally-inherited rhoptries are not trafficked through the RB (every time), then how do they get into the daughters? Perhaps this is a case where a clear definition of the RB is required.

Our observations indicate that maternally inherited rhoptries are frequently incorporated into daughter cells before collapse of the mother cell and establishment of the residual body (RB). Although F-actin is enriched within the RB, an actin network is also present throughout the parasite cytoplasm, where MyoF is likewise localized. We therefore propose that, unlike micronemes, rhoptries do not necessarily transit through the RB during every replication cycle but can be incorporated directly into developing daughter cells while still relying on the same actin–MyoF-dependent trafficking machinery.

(13) The MyoF Rescue, the experimental plan is not fully described in order to be clear. If the endomembrane architecture was disrupted by MyoF depletion, and this secondary effect caused the segregation phenotype, restoration of MyoF might also simply restore the endomembrane system. So a direct role for MyoF doesn't seem to have been tested in this case.

We appreciate the reviewer's concern that the segregation phenotype could, in principle, arise indirectly from disruption of endomembrane architecture following MyoF depletion. However, although Golgi morphology is altered in MyoF-depleted parasites, its core functions appear largely preserved. This is supported by the normal biogenesis of de novo micronemes, their correct targeting to the apical pole, their efficient secretion, and the previously reported preservation of parasite invasion. In addition, Golgi markers are not detected in the residual body, where maternally inherited micronemes accumulate, arguing against Golgi-mediated trafficking as the primary cause of the segregation phenotype.

Taken together, these observations support the interpretation that the segregation defects are more likely to reflect a direct role of MyoF in organelle trafficking and inheritance than a secondary consequence of generalized disruption of endomembrane organization.

(14) Line 279: Why call it a checkpoint? What is the evidence for its presence here being sensed before a further process is activated, which is what a checkpoint does?

We agree the reviewer that checkpoint is a misleading term and have been updated to trafficking hub. 

(15) Line 287 confuses replication of the daughters from cytokinesis, which only happens when each cell loses cytoplasmic connectivity with the other.

We will clarify this point. In Toxoplasma gondii, cytokinesis represents the final step of daughter cell formation, during which the two fully assembled daughter parasites separate from the mother cell following collapse of the maternal cytoplasm. Historically, the residual body was proposed to arise simply as leftover material from this process. However, multiple studies have now shown that residual body formation is an active and regulated process, dependent on specific cytoskeletal and trafficking factors. Importantly, although cytokinesis marks the physical separation of daughter cells from the mother, parasites within a vacuole remain connected via the residual body and continue to share cytoplasmic and plasma membrane components until egress. 

(16) Line 298: I don't think there is direct evidence of degradation in the RB. There might be disassembly, but degradation implies proteolysis, which hasn't been tested for.

We agree with the reviewer that our data do not provide direct biochemical evidence of proteolysis within the residual body (RB) and primarily demonstrate disassembly of the maternal IMC at this site. However, several observations are consistent with local degradation. Following IMC collapse, we do not detect Halo-positive signal elsewhere in the parasite, nor do we observe IMC-positive vesicles or other structures that would suggest transport to a distinct degradation compartment.

In addition, previous work identified the E3 ubiquitin ligase CSAR1 as a mediator of protein turnover within the RB, supporting the idea that this compartment is associated with degradation-related processes (O'Shaughnessy et al., 2023). While we cannot formally demonstrate proteolysis, these observations support a model in which IMC disassembly is closely coupled to local degradation within the RB.

(17) The paragraph structure gets a bit confusing at times. See single sentence paragraph, Line 224. Does this sentence justify its own paragraph?

The text has been edited.

(18) Make sure Toxoplasma gondii is in italics throughout.

The text has been edited

(19) Line 279 cites Figure 10. But there is none.

The text has been edited

(20) I advocate introducing a few new acronyms, like DCs. I find that this ultimately reduces the ease with which readers read the work if they don't learn them all quickly.

We agree that excessive use of acronyms can negatively impact readability. In the present manuscript, all abbreviations used in the text are introduced at their first occurrence in the Introduction, including DCs (line 32), IMC (line 41), PV (line 35), ER (lines 38–39), RB (line 50), and IVN (line 49). We have carefully limited the use of abbreviations to commonly used terms in the field and to those that recur frequently throughout the manuscript, with the aim of balancing clarity and readability. Nevertheless, we are happy to reduce or remove specific abbreviations if the reviewer feels this would further improve clarity.

Reviewer #2 (Recommendations for the authors):

(1) Descriptions of methodology and statistical analysis were incomplete as follows:

(1a) It was unclear how the fluorescence intensity measurements (used to evaluate inheritance vs. new synthesis) were carried out. The y-axis on the graph is labeled average fluorescence intensity (% of max intensity). However, it does not state what was averaged (average fluorescence per vacuole?) and what was max intensity (max pixel intensity in each image or time point with the highest average intensity, relative to the other time points?)

We agree with the reviewer that the original description of the fluorescence intensity (FI) measurements lacked clarity. We have therefore revised the Materials and Methods section and added a new supplementary figure (Figure S11) illustrating the analysis workflow.

Briefly, vacuoles were imaged as Z-stacks, and maximum-intensity projections were used for analysis. FI was quantified as the maximum grey value measured within representative regions of interest (ROIs) drawn on individual tachyzoites, rather than as an integrated fluorescence signal across the vacuole. This approach minimizes variability arising from differences in ROI size and allows direct comparison between replication stages.

For each biological replicate, up to 25 tachyzoites per replication stage were analyzed. The mean FI for each stage was normalized to the highest mean value within that replicate, and data from three independent biological replicates were subsequently averaged.

(1b) Given the uncertainties with how these measurements were performed, it is difficult to interpret the data. For example, one would expect that the fluorescence intensity of newly synthesized IMC1 in 8-parasite vacuoles would be 4 times higher than that of a 2-parasite vacuole; however, based on the graph in Figure 1B, the measured increase was only 30%.

We agree that the original description of the fluorescence intensity (FI) measurements required further clarification and have revised the Materials and Methods accordingly. As the reviewer correctly notes, a fourfold increase in FI between 2- and 8-parasite vacuoles would be expected if total IMC fluorescence across the entire vacuole had been measured. However, this was not the parameter quantified.

Instead, FI was measured as the maximum grey value within representative regions of the daughter IMC, providing a per-cell rather than a whole-vacuole measurement. Using this approach, FI increases between the 2- and 4-parasite stages and then reaches a plateau.

This behavior is consistent with the biology of IMC biogenesis. Although the total amount of IMC per vacuole increases with parasite number, the amount of IMC protein incorporated into each daughter parasite remains relatively constant. Consequently, once daughter IMCs are fully assembled from de novo-synthesised material, additional rounds of replication increase the total IMC content per vacuole but not the fluorescence intensity measured for individual parasites.

(1c) T. gondii replicates in an asynchronous manner, so that at the 24-hour time point, a single dish can contain vacuoles containing 2, 4, and 8 parasites. This should be stated explicitly so readers unfamiliar with T. gondii's growth patterns can understand how the experiment was performed.

We agree with the reviewer and have updated the text line 93. “As Toxoplasma gondii replicates in an asynchronous manner, after 24 of replication, vacuoles containing 1, 2, 4, and 8 parasites can be observed in a single dish.”

(1d) Colocalization package in Fiji used for ANKER1-Halo with HDEL-GFP and MIC2/RON2 with CbEmeraldFP should be specified.

We thank the reviewer for this suggestion. Following this recommendation, we performed Pearson correlation analysis for the ANKER1–HDEL-GFP experiment using the Coloc 2 plugins of FiJi. ANKER1Halo and HDEL-GFP showed a strong spatial correlation (Pearson's R = 0.92 ± 0.04, n=30 parasites from three independent biological replicates), supporting localization of ANKER1 to the ER.

We note, however, that this analysis should be interpreted as evidence for co-distribution within the same organelle rather than direct molecular colocalization, as ANKER1 is a transmembrane protein whereas HDEL-GFP labels the ER lumen.

For all the rest of our analysis, no automated colocalization package or plugin in Fiji was used for the analyses involving ANKER1-Halo with HDEL-GFP or MIC2/RON2 with Cb-EmeraldFP. Colocalization was assessed manually across all experiments by inspecting both full Z-stacks and maximum-intensity projections to ensure robust spatial overlap.

For MIC2 and RON2, the presence of signal within the Cb-Emerald–positive filament was scored as either cytoplasmic, on the residual body or absence of colocalisation.

In total, more than 300 and 500 vacuoles were analyzed for MIC2 and RON2–Cb-Emerald colocalization respectively (stable expression of both markers), and more than 150 vacuoles were analyzed for ANKER1-Halo and HDEL-GFP colocalization (transient expression of HDEL-GFP).

This information has now been added to the Methods section.

(1e) Statistical methods should be described on an experiment-by-experiment basis. The authors should justify why a one-tailed t-test was conducted. A two-tailed t-test seems more appropriate.

We agree that statistical methods should be clearly justified on an experiment-by-experiment basis. All the statistical analysis have been performed using two tails and updated in the figures.

(1f) In Figures 5E and 5F, using boxes to indicate the exact areas of the cell that were used in the fluorescence intensity measurements, rather than arrows, would make this data easier to interpret.

The figure has been updated.

Reviewer #3 (Recommendations for the authors):

The current time-lapse images and videos do not clearly demonstrate microneme movement from the maternal parasite apical end to the residual body and back to the apical end of daughter parasites. As such, the route by which micronemes enter daughter parasites remains inconclusive. To strengthen their claims, the authors should employ higher temporal resolution imaging to definitively capture the movement of micronemes from the maternal apical region into the daughters. From the current data, it also seems plausible that the micronemes may be trafficked into the daughters through the conoid as well, as there is no evidence provided showing a movement of micronemes away from the apical end of the maternal parasite before being present in the daughter parasites.

We agree with the reviewer that higher temporal resolution imaging would provide a more definitive view of microneme trafficking. However, long-term live imaging of replicating Toxoplasma gondii requires a compromise between temporal resolution and parasite viability. In our experiments, images were acquired every 15–30 min over periods of up to 16 h, as more frequent acquisition consistently induced phototoxicity and prevented completion of parasite replication.

Despite this limitation, our imaging reliably tracked maternal micronemes over successive rounds of endodyogeny and consistently showed microneme signal associated with the residual body. These observations are in agreement with previous high-temporal-resolution studies, which demonstrated F-actin-dependent microneme trafficking within the residual body over shorter imaging periods (Periz et al., 2019).

We cannot formally exclude the possibility that some micronemes are transferred directly to daughter parasites through the apical end. However, together with previous studies showing enrichment of F-actin at the basal region of developing daughter cells rather than at the apical tip (Periz et al., 2017), our observations support a model in which RB-mediated trafficking contributes to maternal microneme inheritance.

The lack of a clear residual body marker needs to be addressed, as the distinction between the basal end of the maternal cell and a bona fide residual body must be explicitly defined to substantiate the major claim of the study. As it stands, it remains unclear whether micronemes and rhoptries as a whole travel through the residual body to be transported into the daughter parasites.

We agree with the reviewer that a marker specific to the residual body would strengthen this study. Unfortunately, no such marker has been identified to date. The F-actin chromobody is currently the best available proxy, as previous studies have shown that the F-actin network is enriched within the residual body (Periz et al., 2017; Kellermeier et al., 2024). Moreover, high-resolution live-cell imaging has previously demonstrated F-actin-dependent microneme trafficking within this compartment (Periz et al., 2019). We have revised the manuscript to more clearly acknowledge this limitation.

The conclusions drawn from the actin colocalization data in Figure 6C are based entirely on fixed samples, despite all experimental tools being compatible with live-cell imaging. Supplementing the fixed imaging with live cell data would increase its biological relevance. Published studies have shown that fixation of the actin chromobody results in the loss of resolution of an appreciable amount of the cytosolic F-actin network, and while the localizations analyzed here are primarily along the periphery, since the quantification and text make claims about the colocalization within the cytosol, this potential loss of cytosolic F-actin becomes an issue as there may be more actin available for analysis that is lost due to fixation within the cytosol of the parasites.

We thank the reviewer for raising this important point and agree that conventional fixation can compromise preservation of the F-actin network. However, we used the same fixation protocol described by Periz et al. (2019), which allows reliable visualization of the RB-associated F-actin network. We have also corrected the description of the fixation protocol in the Materials and Methods.

Fixation was necessary to image entire vacuoles with sufficient spatial resolution and signal-to-noise ratio for the volumetric analyses presented in Figure 6C. Although some loss of cytosolic F-actin cannot be excluded, this would be expected to reduce, rather than artificially increase, the detection of organelle–actin associations.

Importantly, previous live-cell imaging studies demonstrated F-actin-dependent microneme trafficking (Periz et al., 2019), and our observations are consistent with these findings. Moreover, the defects observed following MyoF depletion provide independent functional evidence that the trafficking events described here rely on the actin–MyoF transport machinery.

The statement of colocalization should be backed up by quantitative coefficients like Pearson's coefficient.

We thank the reviewer for this helpful suggestion. Following this recommendation, we performed a Pearson correlation analysis of ANKER1-Halo and HDEL-GFP using the Coloc 2 plugin in Fiji. ANKER1-Halo showed a strong spatial correlation with HDEL-GFP (Pearson's R = 0.92 ± 0.04, n = 30 parasites from three independent biological replicates), supporting localization of ANKER1 to the ER. As ANKER1 is a transmembrane protein and HDEL-GFP labels the ER lumen, this analysis should be interpreted as evidence of co-distribution within the same organelle rather than direct molecular colocalization.

In contrast, we do not consider Pearson's coefficient appropriate for evaluating the association of micronemes or rhoptries with F-actin. These organelles are predominantly concentrated at the apical pole and, when associated with F-actin, are typically positioned along rather than directly overlapping the filaments. Consequently, Pearson's coefficient would underestimate these biologically relevant associations. We therefore relied on morphological and spatial criteria, which we consider more appropriate for assessing organelle–cytoskeleton interactions.

In addition, from the methods and presented figure images, specifically in Figure 6C for RON2, how the cytosolic and residual body actin is separated is difficult to discern, as there is a clear residual body actin signal overlapping a parasite. The methods for how this was separated and analyzed should be clearer to remove doubts about how this area was measured, as the current description raises concerns about the counting of the residual body actin within the cytosol.

We agree with the reviewer that the distinction between cytosolic and residual body (RB)-associated F-actin required further clarification. All analyses were performed manually, as described in our response to Reviewer 2 (comment 1d). The RB was identified by the presence of thick, bundled F-actin filaments at the basal pole that formed a continuous structure connecting parasites within the vacuole, whereas cytosolic F-actin was defined as the thinner filamentous network within the parasite body.

No automated or threshold-based segmentation was used because the marked differences in filament morphology and fluorescence intensity make reliable thresholding difficult and prone to misclassification. Manual annotation based on spatial localization and filament morphology was therefore considered the most appropriate approach. We have clarified these criteria in the Materials and Methods section.

Line comments:

(1) 113: round to rounds - "did not obtain maternal organelles after successive rounds of replication...".

The text has been updated

(2) 146: grammatical, "As consequence a progressive" -> "As a consequence", or "Consequently".

The text has been updated

(3) 164-166: "Autonomous duplication" implies the separation and duplication of the Golgi occurs on its own, i.e., without any outside intervention, when we know from Carmeille et al. 2021 and Figure 7C here that the Golgi becomes fragmented over rounds of division in the absence of MyoF. I think this is primarily a word choice error with "autonomous".

We agree with the reviewer and the word autonomous has been removed

(4) 184: The wording suggests that DC's refers to daughter IMC's, when DC has already been given as an abbreviation for daughter cells previously.

The text has been updated to correct this error

(5) 189: de novo is not italicized.

The text has been updated

(6) 192: The data shown so far do not show that the RB plays a selective role in organelle recycling.

The text has been edited to fit better our results “Our data suggest that the organelles trafficking through the residual body (RB) have different fate”

(7) 208: State that it depends on F-actin, but never show that it is dependent on F-actin through actin disruption, such as cytochalasin D treatment or a specific conditional disruption of F-actin.

We agree with the reviewer that we did not repeat F-actin disruption experiments (e.g., cytochalasin D or jasplakinolide treatments) in this study. These experiments were performed in our previous work, where pharmacological disruption of F-actin was shown to impair microneme trafficking (Periz et al., 2019). We therefore chose not to repeat these assays.

Instead, the present study provides complementary evidence by demonstrating that depletion of Myosin F (MyoF), a motor that uses F-actin as a transport track (Kellermeier et al., 2024), disrupts the trafficking of both maternal micronemes and rhoptries. Together, our previous F-actin perturbation experiments and the MyoF depletion data presented here support the interpretation that these trafficking events depend on the actin–MyoF transport machinery. 

(8) 209: This suggests that the chromobody was transiently expressed in the RON2-Halo line, but the methods suggest MIC2-Halo and RON2-Halo were integrated into a parasite line stably expressing Cb-Emerald.

The text has been edited.

(9) 229: The section is confusing with the mention of (now maternal). If I understand correctly, the point being made is that the de novo synthesized MIC2 at stage 2 is now the maternal MIC2 for stage 4, but coloring-wise within the figure, the now maternal MIC2 at stage 4 from stage 2 would still be green. The methods suggest these images were all taken simultaneously, and not at specific timepoints of the same vacuole, so the now maternal line remains confusing.

The text has been revised for clarity and now reads: “Because Toxoplasma gondii replicates asynchronously, vacuoles at different replication stages coexist within the same culture after 24 h. The second labeling step marks all proteins synthesized since the beginning of the experiment, allowing discrimination between proteins present in the original mother parasite and those synthesized during subsequent replication cycles. As daughter parasites form, they inherit material from their mother, such that proteins synthesized during one replication cycle become maternal proteins in the next. Under MyoF depletion, these newly synthesized protein pools accumulate within the residual body instead of being redistributed to daughter parasites during subsequent rounds of replication (Figure 7, stage 4).”

(10) 238: The sentences here indicate that Golgi inheritance occurs without issue: "golgi inheritance remained unaffected by MyoF depletion". But, it is evident from the images shown that the Golgi is extremely fragmented, with many more Golgi fragments by stage 8 than there are parasites. This could be solved by rewording and including a line along the lines of "in accordance with the results found in Carmeille et al. 2021".

The reference to this article is already stated later in the text now line 299-303 “This active role is further supported by the dependence of RB-mediated recycling on F-actin and the class XXII myosin MyoF, which we show to be essential for retrieval of maternal MIC2 and RON2 but dispensable for Golgi inheritance although we noticed a fragmentation of the Golgi, which has been described to depend on MyoF (Carmeille et al., 2021).”

(11) 319: missing a comma, "Many of these, particularly...".

The text has been edited.

(12) 437: Images -> imaged.

The text has been edited.

(13) 439: a fresh media -> and fresh media.

The text has been edited.

(14) 439: Replication -> replicate.

The text has been edited.

(15) 440: images -> imaged.

The text has been edited.

Other grammatical issues within the methods:

(1) Figure 5C: Within the y-axis label of Figure 5C, there is an asterisk with no asterisk explanation within the legend.

We thank the reviewer for pointing out this oversight. The figure legend has been updated to include an explanation of the asterisk, providing a clearer understanding of the results.

(2) Figure 5E: The addition of an IMC1 label to match the magenta color would be helpful to readers.

The figure has been updated

(3) Figure 6D: No statistics showing significance of colocalization.

We thank the reviewer for this comment. In Figure 6D, we report the frequency of observed colocalization between organelles (MIC2 and RON2) and F-actin filaments, based on manual analysis across >300 vacuoles for MIC2 and >500 vacuoles for RON2. Specifically, we observed cytoplasmic F-actin colocalization in 94% of vacuoles for MIC2 and 79% for RON2, and residual body F-actin colocalization in 85% of vacuoles for MIC2 and 11% for RON2. This analysis is descriptive and is not intended to compare MIC2 versus RON2 quantitatively; rather, it illustrates the general association of these organelles with F-actin filaments. Standard statistical measures such as Pearson correlation are not meaningful in this context because the organelles are punctate and primarily localized along filaments rather than overlapping continuously. Importantly, the percentages reported represent the fraction of vacuoles in which colocalization can be observed, not the percentage of colocalization between Cb-Emerald and MIC2/RON2 within individual vacuoles.

(4) Figure 7: The legend title of Figure 7 is at the end of the legend of Figure 6.

The text has been edited.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Here, Pinto and colleagues set out to investigate whether the cow udder is a potential mixing site for the influenza virus. The authors have demonstrated that bovine mammary epithelial cells can be infected with both avian and human influenza A viruses, supporting the idea that the cow udder may be a potential site for reassortment. Furthermore, they demonstrate that the bovine-adapted IAV replicates to similar titers in avian epithelial cells when compared to an AIV precursor virus. Thus, suggesting there is no fitness trade-off, and confirms the potential for spill-back of the cattle B3.13 into poultry, which has already been observed. Overall, I believe the authors achieved their aims. However, there are instances in which the results do not entirely support the conclusions (noted in weaknesses). Given the ongoing questions surrounding highly pathogenic avian influenza A virus in dairy cows, this work provides valuable evidence for the potential of the cow udder as a site of reassortment. These findings highlight the need for surveillance of influenza A virus incursions into livestock species, particularly cows. Some specific strengths and questions regarding weaknesses have been outlined below.

Strengths:

(1) The authors use a diverse range of cell types and influenza A virus strains, as well as a wide range of techniques to address the questions at hand.

(2) The use of cells from multiple bovine breeds for the MAC-T, bMEC and explants suggests the phenomenon is not unique to a single breed.

(3) The results suggesting there is no fitness trade-off for Cattle Texas in an avian host are interesting, and confirm the potential for spill-back of the cattle B3.13 into poultry, which has been observed.

Weaknesses:

I have listed my complete questions/concerns below. However, there are two main weaknesses of the article in its current state. Firstly, there is no apples-to-apples comparison in terms of determining a preference for IAV to infect the cow udder over other organs (Q4). The mammary gland and respiratory tract are represented by epithelial cells, but for other organs, fibroblasts were chosen. I think the fairer comparison would be to compare epithelial cells from different organs to demonstrate a preference for the mammary gland. Secondly, the main premise of the article relies on bMEC and MAC-T (primary and immortalised mammary epithelial cells), facilitating higher viral growth than the cells from other organs. Yet throughout the article, a 10x higher dose of IAV is used in the bMEC cells compared to everything else (Q6). This raises the question of how much of the results are due to a preference for the mammary epithelial cells, and how much is simply due to the increased dose.

(Q4) When we set out to test if cow mammary gland cells were particularly susceptible to IAV infection compared to other bovine cell types, we used what was available in the Roslin Institute – a mix of primary and continuous cells from various anatomical sites: three epithelial cell types (two mammary, one respiratory tract) two immune cell types and four sets of fibroblasts from various organs. Given the representation of different anatomical sites, cell types and differentiation statuses, we considered this a suitably diverse panel with which to characterise infection dynamics of a broad range of IAVs, before more focussed investigations using the bMEC and explant tissues. Both mammary epithelial cell types grew our library of influenza challenge strains significantly better than the BAT-II respiratory epithelial cells, as well as the two immune cell types and all four fibroblast populations. Of the fibroblast cells, those derived from the brain grew IAV significantly better than the skin and turbinate fibroblasts, while blood-derived macrophages grew virus significantly better than the lymphocytes and non-brain fibroblasts. So there are “apple-to-apple” comparisons as well as apple-to-pear comparisons that give significant differences. We therefore think that our conclusions (in the abstract) that mammary cells are particularly replication competent for IAV, (at the end of the introduction) that “a wide range of cow-derived cells are susceptible” and that (in the results section) that “mammary cells showed the highest susceptibility” are justifiable. However, we agree that testing a wider variety of epithelial cells would be useful and have added text to the Discussion (lines 224-228) to acknowledge this.

(Q6) We used a higher MOI for bMECs because test experiments with WT PR8 and the Cattle Texas 6:2 reassortant virus showed that MOI 0.01 infections gave more variable results than those run at MOI 0.1, perhaps because of the intrinsic variability of mixed primary cell populations. However, the end-point titres between the two conditions were not significantly different, so we therefore chose to go with the higher MOI. Accordingly, we do not think this choice is a confounding issue. This explanation (line numbers 340-345) and a new Supplementary Figure 11 showing the results of the two MOI tests have been added to the manuscript.

Reviewer #2 (Public review):

The authors use a library of influenza A viruses from different strains, classified in lab-adapted, human, avian, and swine according to the animal from which they were isolated. They propose that the cow mammary gland serves as a mixing vessel for influenza A viruses. As a first approach, the authors assess susceptibility to infection across different cell types, including continuous and primary cell lines, bovine mammary cells, and mammary explants. All these cells support polymerase activity. Then, they analyzed changes in the bovine virus's viral fitness relative to an avian precursor. The authors use single-gene replacement to study whether and which RNP segments improve viral transcription. As part of this section, they also test IFN-specific antagonism by NS1 to assess the input of segment 8. Quantitative glycomic analysis was performed on the continuous bovine mammary cell line to demonstrate the presence of both a2,3 and a2,6, which is consistent with their observation that these cells can be co-infected with human and avian IAVs simultaneously. The main question, however, is: what is the glycome in the explants, or directly from tissues?

We report quantitative glycomics for the primary bovine mammary epithelial cells as well as the continuous line the referee highlights. However, we agree with R2 that a detailed glycomic analysis of primary bovine mammary tissue would allow a better understanding of the actual glycosylation status in vivo. This has been undertaken by the authors and is available as a bioRxiv preprint. This is now cited (ref 25) in the relevant part of the results (line 184-185)

Overall, the manuscript is clearly written and provides new insights into the behaviour of the cattle isolate, now compared with a representative group of model or precursor HAs of different origins.

It would be great if a consistent nomenclature for the IAV strains could be used in the study. There is a mix of origin (Texas), animal from which the virus was isolated (mallard), or abbreviations that do not follow guidelines (IAV07). Are the USSR and Udorn not lab-adapted?

We chose the abbreviated names for a variety of reasons. Partly from common usage (e.g. PR8, Udorn), partly for consistency with other already published papers from the FluTrailMap consortia (e.g. Cattle Texas; Dholakia et al 2026), partly to make diversity obvious in certain figures (e.g. H3N1, H5N2 etc) and partly to avoid confusion between viruses that originate from the same geographic area (e.g. AIV07, AIV09, H5N8-20 etc which are all A/Ck/England/isolate numbers). Overall, we found it more confusing to use the expanded nomenclature. Re AIV07 which the referee criticises for not following naming guidelines – if this is a reference to the EURL nomenclature, AIV07 is the abbreviation for the specific virus A/Chicken/England/053052/2021, our representative virus for EURL genotype EA-2020-C, as we say in the text. This nomenclature has now been added to Table 1, to provide a fuller cross-reference for all the names.

As to whether USSR and Udorn are lab-adapted – that depends on definitions. There is a continuum of adaptive changes and/or sequence drift starting from the very first growth cycle of an isolate in the laboratory. The viruses we define here as lab adapted are ones that have been deliberately adapted to other host species or which have very long passage histories in multiple laboratory systems resulting in known functionally significant changes; for example, one lineage of PR8 was passaged 77 times in mice, 717 times in cell culture, 30 times in chick embryos, 5 times in ferrets and a further 50 times in chick embryos (https://www.medscape.com/viewarticle/812621_3?form=fpf), rendering it unarguably lab-adapted. We admit that A/USSR/77 and A/Udorn/307/1972 are probably further along this adaptive pathway than more recent isolates such as A/Norway/3433/2018, but are unaware of any specific reason that would put them into our lab-adapted category.

The experimental setup includes bovine mammary primary and continuous cells, as well as mammary explants. Some of the most significant differences, for example, in viral fitness studies and co-infection experiments, are observed in these explants. Perhaps there could be some additional focus on this observation. The implications in comparison to the results obtained in cultured cells could be described. How will the human and other HA subtype viruses fare in the explants?

We agree that this is an important and interesting question, and had already tested the strains we used for co-infections: human seasonal pdm09 H1N1 “Norway” and low pathogenic avian influenza “H3N1”, in the mammary explants. Both replicate the avian virus to 20-fold higher titres. We have added this information to the revised manuscript as new Figure panels S6E-H, called out on line 200-201 of the results.

Reviewer #3 (Public review):

Summary:

This excellent manuscript by Pinto, Sharp, and colleagues examines bovine tissue tropism for influenza viruses. They find that bovine flu, as well as other strains, has strong replication in mammary tissue. They also map the genetic changes to influenza that improve replication in bovine cells. Overall, the study is well designed and executed, and the results are very timely.

Strengths:

(1) The experiments are well-controlled.

(2) The figures are well-constructed and easy to follow.

(3) The Methods and legends are detailed, with sufficient information.

Weaknesses:

(1) A comparison to human cells would strengthen the overall impact of the results. Are human mammary cells also uniquely susceptible to influenza? Are bovine mammary cells special in some way?

This is an interesting question, but we have not tested mammary gland cells from humans (or any other species of mammal). We have however reported elsewhere (Dholakia et al., Nat Commun. 2026 Jan 16;17(1):1603. doi: 10.1038/s41467-026-68306-6.) that Cattle Texas grows well in a variety of human respiratory cells. Here, we are considering the bovine mammary organ as a potential reassortment site for IAVs because of the ongoing viral mastitis epidemic in US dairy cattle; human mammary organs seem unlikely to create a similar opportunity.

(2) For the virus infection studies with segment 8 swaps, it should at least be noted that some of the phenotypes could be driven by NEP.

We agree; as Table S1 indicates, NEP has two changes (one shared with NS1) between AIV07 and our B3.13 isolate, so we should not have conflated segment and NS1. We have changed the text to acknowledge this throughout the results (lines 127, 137 and 149) and in the discussion (line 243-244).

(3) The data demonstrating that bMEC can support co-infection are compelling and important, but would be strengthened with a comparison from a different cell type or species. Do mammary cells uniquely support higher co-infection?

We have data showing that co-infection also occurs in the continuous MAC-T udder cell line and have now included these data in a revised Figure 4D (described/called out on lines 198-206). We have not tested bovine cells from other organs for co-infection potential as they do not seem to be significant sites of infection in vivo.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) How nasal turbinate and cardiac fibroblasts are acquired/cultures is missing from the methods.

Apologies for the omissions and thank you, because rectifying this brought to light an error in cell naming. The cells originally called bovine cardiac fibroblasts were in fact a second independent preparation of skin fibroblasts. We have corrected the labelling in Figs 1, 2 and S2. The nasal turbinate cells were bought in from ATCC (code CRL-1390). This information has now been added to the methods (line 310).

(2) Please specify what cell types make up the 2D enteroids, the mammary explants and the nasal turbinates.

The composition of the 2D enteroids is described in detail in reference [60]. In precis, they are comprised predominantly of epithelial cells, including Paneth, goblet and enteroendocrine cells, as well as stem cells. This information has been added to the methods (lines 374-376) The mammary explants include duct epithelium, connective and muscle tissue, defined by H&E staining of cut sections (see new Figure S12 and text added to the methods on lines 384-386). We have also added the person who did the histology (Rebecca Ross) as an author and to the credit taxonomy (line 877). The nasal turbinate cells appear to be predominantly fibroblast morphology (Methods line 310-311).

(3) Epithelial cells are the main target for IAV, so why were fibroblasts chosen as a comparison to mammary epithelial cells? This needs justification in text. Without justification, how much can be attributed to the results being mammary-specific, rather than epithelial-specific? The brain (choroid plexus epithelium), heart (epicardium) and skin all contain epithelial cells.

We think this query is what the referee calls “Q4’ in the public part of their review. Please see our answer above.

(4) Figure 1, S1, S2 and S3 seem to suggest that mammary cells are more susceptible to IAV infection than cells from other organs. But Figure 2 demonstrates that when it comes to Cattle Texas and AIV07, most of the cell types show high viral titers. If the question is about whether the cow udder is the primary mixing site, would it not be more relevant to investigate which cell type facilitates the best growth of the potential precursor viruses, similar to Figure 4A?

Figs 1, S1, 2 and 3 all use “full” viruses whereas Fig 2 uses 6:2 reassortants between PR8 and the HPAIVs for biosafety reasons. WT PR8 replicates well in most of the bovine cells tested (Figs S1-3) so we do not see any contradiction. Figure 2 examines the contributions the internal genes make to replication in bovine cells. Re the question over the udder being a potential mixing site – this is where the virus is replicating in the real world; at least in part because of the transmission mechanism, but also because the mammary gland epithelium is highly susceptible to infection, as we show.

(5) It is misleading to compare the bMEC infection of MOI 0.1, to all other infections of MOI 0.01. This is a consistent problem throughout the article - Figures 1, S1, 2, 4. Why was the bMEC infection at a 10x greater dose? The main premise of the article relies on bMEC and MAC-T (primary and immortalised mammary epithelial cells), facilitating higher viral growth than the cells from other organs. If we compare the MOI 0.01 experiments alone, then the evidence relies on the immortalised MAC-T cells, compared to primary cell types. In this case, how much can be said about it being mammary specific, rather than immortalised vs primary? I do wonder, for example, how the epithelial nasal turbinates or type II pneumocytes would compare to the primary mammary epithelial cells if they were at the same MOI.

Please see our answer to this query earlier in the rebuttal.

(6) Why are the 2D enteroids excluded from Figure 1?

We had limited supplies of a difficult-to-grow cell model, so we only used them to test the 6:2 viruses (Fig 2).

(7) The colour scheme for Figure 3 is confusing. In Figure 3A, blue indicates European ancestry, and yellow represents North American ancestry. However, in Figure 3B, these colours now mean something different. To a reader, when there is a colour-coded schematic, it is instinctual to think that this then corresponds to the following panel(s). Since consistently throughout the article, yellow has been used for Cattle Texas, and blue has been used for AIV07, I would suggest choosing different colours to represent European and North American ancestry in Figure 3A

We’ve changed the figure as the referee suggests and modified the Fig 3 legend accordingly (line 895)

(8) I am unsure about the conclusions drawn from the results of Figure 3B. In the results, it is framed as trying to determine which segments contributed to the improved activity of Cattle Texas compared to AIV07. In lines 110-111, "... PB2 or PA from AIV07 significantly decreased Cattle Texas minireplicon activity". If PB2 is indeed significant, there is a missing yellow asterisk in Figure 3B.

Apologies, there was indeed a missing asterisk on the figure; now added.

Given the significance of PA, why was it not investigated in terms of growth kinetics similar to Figure 3C? Was it overlooked because it doesn't have a North American ancestry? The results of Figure 3B suggest that the 4 amino acid mutation in PA has significantly contributed to changes in polymerase activity.

The PA changes do indeed matter for minireplicon activity – the key change is K497R, as detailed in our related publication in Nat Comms (citation 17). However, it is less important than changes in PB2, and the PA segment swap by itself has little effect on overall virus replication.

(9) Similarly, in Figure 3C and lines 116-117, the error bars on the graph are overlapping at 48 hours, suggesting no difference in overall replication. The kinetics are slowed for AIV07 seg1-3, but not for AIV07 seg 1, indicating PB1 does not have an effect. This would then suggest that something in segment 2 or 3 contributes to the slowed kinetics in Figure 3C, which, from the Figure 3B results, is unlikely to be due to PB2. While it was not reassorted, the PA segment is potentially the driver, with its 4 amino acid mutations. I think it is worth performing growth kinetics with and without these 4 amino acid changes in PA.

We agree that visually on a log₁₀ scale, the titres of the “WT” 6:2 Cattle Texas and 5:2:1 segment 1 reassortment appear close, but the average titres are 5 and 7-fold different at 24 and 48h respectively, while a 2-way ANOVA with Dunnet’s multiple comparison post-test gives statistical significance at 48h. We have added this information to the figure and its legend (lines 905-906).

(10) In Figure 3C and E, why did you choose to perform the growth kinetics in the immortalised cell line, when you have access to primary cells? The primary cells would be a more accurate representation of what happens in situ.

The primary cells were difficult to work with and only available intermittently, so we used what was available at the time.

(11) In lines 145-147, "thus overall, the reassortment event that replaced segments 1, 2 and 8 alongside drift adaptations in segment 3 may have contributed to the ability of the B3.13 genotype virus to infect cattle". This is not clearly supported by the evidence presented. In terms of segment 1/PB2, the growth kinetics of Figure 3C have overlapping error bars at 48 hours. Where is any evidence presented for the role of segment 2/PB1? There is no change in Figure 3B.

The referee is correct, calling out seg2 here was an error; we have revised the text (line 144).

Segment 3 is overlooked in Figure 3 (as highlighted in Q9 and 10), and shows no difference in Figure S4.

Please see response to Q8; we think segment 3 contributes via PA adaptation, not via PA-X.

(12) In line 146 "... drift adaptation in segment 3". Make it clear here that you are talking about genetic drift. However, is this likely to be genetic drift? The 4 amino acid mutations are shown to have a significant impact on polymerase activity in Figure 3B, and in Figure 3C, PA potentially contributes to the reduced kinetics. When there are amino acid mutations that correspond to a beneficial phenotypic change, attributing this to drift alone rather than host adaptation is strange.

Yes, wording clarified (line 145). “Drift” was used to distinguish it from reassortment but we agree this was an incorrect term in the context.

(13) Figure 4A MAT-C cells: this is ostensibly the same experiment as Figure 3C in terms of the Cattle Texas and AIV07 viruses. If this is the case, how can you explain the difference in kinetics and overall titer? In Figure 3C, Cattle Texas reaches 10^6, and in Figure 4A it reaches almost 10^9. That's almost 3 log difference. Similarly, in Figure 3C Cattle Texas reaches 10^3, but in Figure 4A it reaches 10^6, a 3-log difference. At 24 hrs, they have roughly a 3-log difference between them in Figure 3C, but in Figure 4A this difference is much smaller. As far as I can tell, these are the same viruses, same dose and same cell model. The t0 titer is also vastly different between the two experiments.

The experiments were done at different times (several months apart, so different cell passage numbers and/or serum batches) and by different people. We have no explanation other than biological variability. However, both groups of experiments include genuine biological replicates done over the course of 2-3 weeks, so in our view represent coherent tests within themselves.

(14) In Figure 4, why weren't the a-2,6 a-2,3 proportions analysed for the explants and/or used for the co-infection experiment? It showed the greatest difference between the Cattle Texas and precursor viruses in Figure 4A.

Our data on the proportion of 2,6 and 2,3 SA in bovine udder tissue are now available in a separate preprint (now cited as [25] in our MS). We did not use the explants for co-infection experiments because it would have been technically difficult to read out the outcome by flow cytometry.

(15) Figure 4D requires a supplementary figure demonstrating the gating strategy, including one of the samples as an example.

We have compiled a figure of this and added it as new Figure S13 (called out line 556).

(16) In Figure 4D, why was an MOI of 5 chosen instead of the MOI of 0.01 used throughout the article for MAC-T cell infection? An MOI of 5 (so in a co-infection, a total of 10 virus particles per cell) is completely overloading the cells. At this dose, 10% of the cells were able to be co-infected, but how representative is this of a real co-infection scenario? While it demonstrates it is possible, it potentially remains highly unlikely, similar to the discussion around the swine respiratory tract in lines 235-240.

We had also performed the co-infections at lower MOI (1) with very similar results – this is now included in Figure 4D. Furthermore, we redid the experiments at a lower MOI of 0.05 and still see co-infection; this now replaces the MOI 5 data in Figure 4D. The text has been revised accordingly (lines 202-205)

(17) In Figure 4D, why were immortalised cells used when primary bMEC and mammary explants are available? Primary cells would provide more convincing evidence for the potential of the cow udder to be a mixing vessel. Considering that throughout the paper, a 10x higher viral dose is used in the bMEC culture, I wonder if you would need a significantly higher MOI than 5 to produce similar results in a co-infection experiment. The bMEC also has a more even a-2,3 to a-2,6 ratio compared to MAC-T in Figure 4C.

The bMECs in the original figure are primary cells. In response to other queries, we now include data from the immortalised MAC-T cell line as well.

Reviewer #2 (Recommendations for the authors):

Figure 1A, the coloured underline to discriminate continuous and primary cells is lost upon printing... perhaps another way is better?

We have changed the primary cells to italic text to make the distinction clearer.

We have made some other minor changes to wording to correct grammatical errors or improve clarity as we went through.

Reviewer #2 (Public review):

Summary:

The authors use simulations and empirical data fitting in order to demonstrate that informing a decision model using noisy single-trial estimates of an underlying fixed non-decision time can guide the model to more reliable parameter estimates, especially when the model has collapsing bounds.

Strengths:

The paper is well written and motivated, with clear depth of knowledge in the areas of neurophysiology of decision-making, sequential sampling models, and in particular, the phenomenon of collapsing decision bounds.

Two large-scale simulations are run to test parameter recovery, and two empirical datasets are fit and assessed; the fitting procedures themselves are state-of-the-art, and the study makes use of a very new and well-designed ERP decomposition algorithm that provides single-trial estimates of the duration of diffusion; the results provide inferences about the operation of decision bound collapse - all of this is impressive.

Weaknesses:

This is an interesting and promising idea, but a very important issue is not clear: it is an intuitive principle that information from an external empirical source can enhance the reliability of parameter estimates for a given model, but how can the overall BIC improve, unless it is in fact a different model?

Comment on revised version.

Thanks to the authors for their responses and inclusion of additional analyses and simulations. Thanks, in particular for clarifying a crucial detail, that the ndt-informed model actually assumes, like the uninformed model, that there is no variability in the non-decision time, and the idea is that the variable single-trial measurements of non-decision time are noisy estimates of an underlying, constant ndt. The revised paper itself has not made this clear - for example, throughout the Intro, there is no statement that the behavioural model assumes a trial-invariant ndt, and line 231 still calls tau the 'mean' non decision time, implying there is a distribution rather than an invariant single value in the behavioural model.

One implication of the above is that if the lognormal sigma is purely measurement noise that does not relate to actual variation in the underlying decision process generating behaviour, then the HMP latencies should not relate to behaviour, e.g. shorter latencies predicting shorter RT. I assume that even if the authors did find such a relationship, the principle still stands that a model with fixed ndt is more accurately fit when there are single-trial ndt estimates whose mean provides a constraint on that ndt value, than without such measurements. Still, given ndt variability is a core feature of many decision models, the authors could comment on whether the strategy would work in theory for a model with ndt variability (in the behavioural part), where the single trial estimates would then presumably reflect a mix of measurement noise and genuine ndt variability.

Another more important implication is that since it is in fact the same model being compared with and without the HMP data guiding the fixed ndt estimate, the reason the fit quality improves with HMP-information is not because it is a better model per se (it is the same model) but because without the HMP guidance, the search algorithm somehow gets lost and fails to find the 'optimal' parameter vector. That is, the parameter vector (just the parameters that relate to the behavioural model itself, not the HMP lognormally-distributed noise associated with VEP measurements) identified as optimal in the HMP-informed version of the model exists in the parameter space of the model without HMP information, but it is just not found? I raised this implication before, and it is still not clear whether it applies. I'm sorry to press on it, but it is critical for readers to understand why it is that neural information can improve overall model fit. Again, the enhancement of parameter recovery (like in Nunez 2025) makes sense, but the enhancement of the "model's fit to behavioural data" does not, without pointing to a deficiency in the search algorithm / fitting procedure.

The authors state in their replies that the onset of bound collapse is set at accumulation onset and imply that setting it instead at stimulus onset could "mathematically resolve the issue" but they don't do it because it is implausible. It is in fact not only plausible but clearly evidenced in empirical data - collapsing bounds are implemented neurally through urgency signals, and these can begin to dynamically build toward threshold well before, let alone at, stimulus onset. There is nothing bizarre about this - we can prepare movements without sensory input, and indeed even if choosing actions based on a sensory discrimination, motor preparation can launch well before the sensory evidence (e.g. Stanford, Salinas et al 2010) and this in effect collapses the bound on cumulative evidence for triggering action before any evidence actually arrives. So, Urgency/bound-collapse does not need to be triggered by a stimulus; it can start in anticipation of the stimulus. It seems critical, therefore, for the authors to clarify this point - does re-defining the onset of the collapse at stimulus onset remove the trade-off and render unnecessary the neurally-informed ndt estimation?

Related to this, it is still not clear how bias in the estimation of nondecision time would not be a problem. What if, for example, it is the end of the N2 rather than the peak of the N2 that marks accumulation onset, and/or there is an additional fixed motor time that adds to the N2-based marker to make the full nondecision time that applies in the underlying decision process. By definition (and I think this is essentially what the authors' new simulations verify), because of the trade-offs, this bias would simply be absorbed in shifted estimates of theta and lambda describing the bound collapse function. But wasn't the whole point of the exercise to more accurately estimate those parameters? The obvious implication is that the parameter-estimation accuracy of the ERP-informed model is determined by the accuracy with which the proposed ERP marker directly pinpoints the full nondecision time without bias, but this is not at all obvious in the paper as written. Importantly, in the example scenario I describe above where accumulation onsets when N2 ends, there may still be a perfect correlation of N2 peak latency with underlying ndt across trials - they could still be very strongly "linked" statistically, but we can't know what size offset might be involved.

Author response:

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

Reviewer #1 (Public review):

Summary:

This paper proposes a non-decision time (NDT)-informed approach to estimating timevarying decision thresholds in diffusion models of decision making. The manuscript motivates the method well, outlines the identifiability issues it is intended to address, and evaluates it using simulations and two empirical datasets. The aim is clear, the scope is deliberately focused, and the manuscript is well written. The core idea is interesting, technically grounded, and a meaningful contribution to ongoing work on collapsing thresholds.

Strengths:

The manuscript is logically structured and easy to follow. The emphasis on parameter recovery is appropriate and appreciated. The finding that the exponential NDT-informed function produces substantially better recovery than the hyperbolic form is useful, given the importance placed on identifiability earlier in the paper. The threshold visualisations are also helpful for interpreting what the models are doing. Overall, the work offers a well-defined, methodologically oriented contribution that will interest researchers working on time-varying thresholds.

We appreciate the positive and constructive feedback. We have addressed your comments in the revised manuscript, as detailed in our responses to the specific comments below.

Weaknesses / Areas for Clarification:

A few points would benefit from clarification, additional analysis, or revised presentation:

(1) It would help readers to see a concrete demonstration of the trade-off between NDT and collapsing thresholds, to give a sense of the scale of the identifiability problem motivating the work.

Thank you for this constructive suggestion. We conducted a new simulation study in which we considered the non-decision time as a fixed parameter and estimated the remaining parameters of the collapsing threshold model. In this simulation study, we contaminated the non-decision time with noise at six levels (i.e., 0%, 2%, 4%, 6%, 8%, and 10%). The simulation results showed that increasing the noise level in non-decision time worsens the estimation of the starting threshold and decay rate parameters, indicating a trade-off between non-decision time and collapsing threshold parameters. The results of this simulation are presented in Appendix 1 in the new version of the manuscript.

(2) Before moving to the empirical datasets, the manuscript really needs a simulation-based model recovery comparison, since all major conclusions of the empirical applications rely on model comparison. One approach might be to simulate from (a) an FT model with across-trial drift variability and (b) one of the CT models, then fit both models to each of the simulated data sets. This would address a longstanding issue: sometimes CT models are preferred even when the estimated collapse in the thresholds is close to zero. A recovery study would confirm that model selection behaves sensibly in the new framework.

We are grateful for this constructive comment. The revised manuscript includes a model recovery study (see Simulation study 2, in particular Table 1 and the accompanying text). In this simulation, as the reviewer suggested, we generated data from FT-DDM with across-trial variability in drift rate and CT-DDM with hyperbolic and exponential collapsing thresholds. Then, for each generated dataset, we fitted two models and classified the datasets based on goodness-of-fit and estimated decay rate. The results show that incorporating the decay rate, which can be reliably estimated by the NDT-informed modeling framework, significantly improves the precision of model recovery.

(3) An additional subtle point is that BIC is defined in terms of the maximised log-likelihood of the model for the data being modelled. In the joint model, the parameter estimates maximise the combined likelihood of behavioural and non-decision-time data. This means the behavioural log-likelihood evaluated at the joint MLEs is not the behavioural MLE. If BIC is being computed for the behavioural data only, this breaks the assumptions underlying BIC. The only valid BIC here would be one defined for the joint model using the joint likelihood.

We thank the reviewer for raising this important methodological point. We agree that, strictly speaking, the behavioral log-likelihood evaluated at the joint maximum likelihood estimates is not guaranteed to be equal to the behavioral maximum likelihood estimate. Therefore, if one were to interpret BIC_Behavior for joint (NDT-informed) models as a conventional BIC derived from a purely behavioral maximum likelihood fit, this would indeed violate the standard assumptions underlying BIC. Our intention, however, was not to claim that BIC_Behavior represents a formally valid BIC in the strict information-theoretic sense. Rather, we used it as a diagnostic measure to assess how well the jointly estimated parameters account for the behavioral data relative to the uninformed models. Importantly, in our datasets, the behavioral log-likelihood evaluated at the joint estimates is higher than that obtained from the uninformed models. This suggests that the additional constraint introduced by the non-decision time information helps guide the optimization procedure toward parameter regions that provide a better account of the behavioral data. In other words, uninformed models appear to converge to suboptimal parameter estimates, but the joint modeling framework helps regularize the estimation process and yields better estimates of the optimal parameters. We fully acknowledge that this use of BIC_Behavior for the joint models departs from standard practice in the cognitive modeling literature. For this reason, we rely primarily on the joint likelihood–based model comparison as the formally valid criterion. The behavioral BIC is reported only to provide additional intuition regarding the goodness of fit on behavioral data and is used exclusively to compare NDT-informed models with their uninformed counterparts under identical evaluation criteria.

Also, to warn readers about this limitation, we included the following statement in the section where we defined BIC measures:

“It is worth noting that comparing joint and behavioral models using BIC_Behavior is uncommon and constitutes a limitation of the model comparison study.”

(4) Table 1 sets up the Study 1 comparisons, but there’s no row for the FT model. Similarly, Figures 10 and 13 would be more informative if they included FT predictions. This matters because, in Study 1, the FT model appears to fit aggregate accuracy better than the BIC-preferred collapsing model, currently shown only in Appendix 5. Some discussion of why would strengthen the argument.

In the revised manuscript, we have included the results for NDT-informed FT-DDM in the main text. However, we kept the FT-DDM with drift variability in the appendix, since none of the models in the main text include drift rate variability.

(5) In Figure 7, the degree of decay underestimation is obscured by using a density plot rather than a scatterplot, consistent with the other panels of the same figure. Presenting it the same way would make the mis-recovery more transparent. The accompanying text may also need clarification: when data are generated from an FT model with across-trial drift variability, the NDT-informed model seems to infer FT boundaries essentially. If that’s correct, the model must be misfitting the simulated data. This is actually a useful result as it suggests across-trial drift variability in FT models is discriminable from collapsing-threshold models. It would be good to make this explicit.

Regarding the visualization of decay rate estimation in Figure 7, we would like to clarify that, in the data-generating process for the FT model with across-trial drift variability, the decay rate is fixed at zero. That is, unlike the other parameters, there is only a single true value on the x-axis. If we were to present the decay rate recovery using a standard scatter plot (true vs. estimated values), all points would lie vertically above the single true value (zero), resulting in a vertical strip of points. While such a plot would technically be consistent with the other panels, it would not clearly convey the distributional properties of the estimated decay rates, specifically, which values are more likely under model misidentification. For this reason, we chose a density plot to more transparently illustrate the distribution of inferred decay rates when the true generating process is an FT model. We believe this representation more effectively communicates the extent and structure of mis-recovery. To avoid confusion, we have added a clarifying footnote in the revised manuscript explaining why a density plot was used in this specific panel.

Regarding distinguishing fixed-threshold models from collapsing-threshold models, as suggested in your comment 2, we conducted an additional simulation, and the results showed that when using the NDT-informed diffusion model, we can distinguish between both models with high accuracy. Specifically, we showed that incorporating the estimated decay rate value provided by the NDT-informed modeling approach can significantly improve the model recovery accuracy.

(6) Given the large recovery advantage of the exponential NDT-informed function over the hyperbolic one, the authors may want to consider whether the results favour adopting the former more generally. Given these findings, I would consider recommending the exponential NDT-informed model for future use.

Consistent with the reviewer’s argument, we included the following text in the general discussion:

“Importantly, the exponential collapsing threshold exhibited substantially better parameter recovery and superior model recovery performance, suggesting that this specification may be preferable in future cognitive modeling applications.”

(7) In Study 2 (Figure 13), all models qualitatively miss an interesting empirical pattern: under speed emphasis, errors are faster than corrects, while under accuracy emphasis, errors become slower. The error RT distribution in the speed condition is especially poorly captured. It would be helpful for the authors to comment, as it suggests that something theoretically relevant is missing from all models tested.

Thank you for mentioning this point. Because the models considered in the main text do not include across-trial variability in the starting point, the model cannot predict the fast error pattern observed in the speed condition of the second study. In the revised manuscript, we included a note on this point:

“The NDT-informed models’ predictions are depicted in Figure 13. This figure shows that the FT-DDM overestimates the last RT quantiles for both correct and incorrect responses in both speed and accuracy conditions. However, the qualitative predictions of CT-DDMs align more closely with the empirical data. It is also worth noting that all the considered computational models misfit the incorrect responses in the speed condition. This misfit is to be linked to the presence of fast errors, specifically in the speed condition. Including the starting-point variability parameter in the model enables the model to predict fast errors. However, as the aim here was not merely to fit the data with the best possible model, but to test the NDT-informed modeling framework, we did not include starting-point variability in the model.”

(8) The threshold visualisations extend to 3 seconds, yet both datasets show decisions mostly finishing by 1.5 seconds. Shortening the x-axis would better reflect the empirical RT distributions and avoid unintentionally overstating the timescale of the empirical decision processes.

In the new version of the manuscript, we shortened the x-axis in these plots. See Figures 9 and 12 in the new version of the manuscript.

Reviewer #1 (Recommendations for the authors):

(1) The manuscript should explicitly state how critical the log-normal assumption for NDT is, and whether there are caveats if it doesn’t hold.

We agree with this suggestion. Therefore, we conducted an additional simulation study in which we assumed a normal distribution for non-decision time measurements and replicated the main results reported in simulation study 1 (see Appendix 8 in the new version of the manuscript). These simulation results reveal that independent of distributional assumptions on non-decision time measurements, constraining non-decision time can improve the estimation of the collapsing threshold.

(2) On page 14, one paragraph refers to five models and another to six. It is unclear which is correct.

We are sorry for the confusion. In the new version of the manuscript, we addressed this issue.

(3) In the Discussion: Hawkins & Heathcote (2021) found that NDT estimates in the TRDM recover well, but the timer-offset parameter does not (and hence is set to a fixed value). It would be interesting to test whether the NDT-informed approach could extend to that parameter. The TRDM can also generate error RT distributions that are faster than correct RT distributions, which is the qualitative pattern that none of the present models capture in the speed condition of Study 2.

We appreciate the reviewer’s suggestion, as it would be another important demonstration of the framework we built in the paper. Nevertheless, given the number of models already considered in the manuscript and the focus on collapsing threshold diffusion models, we believe that this addition would blur the focus of the present manuscript. Therefore, we have decided not to include TRDM in the manuscript. Nevertheless, we have addressed the reviewer’s concern regarding the non-decision time estimation in the TRDM in the revised manuscript:

“Notably, this model can also predict faster error responses than the correct response, the pattern that is observed in the speed condition of Study 2. However, the authors reported poor parameter recovery for the onset of the timing process (Hawkins and Heathcote, 2021). Thus, the reliability issue here specifically concerns the estimation of the shift parameter of the timing accumulator. Informing the model with external estimates of non-decision time might, therefore, improve parameter recovery in this model as well.”

Reviewer #2 (Public review):

Summary:

The authors use simulations and empirical data fitting in order to demonstrate that informing a decision model on estimates of single-trial non-decision time can guide the model to more reliable parameter estimates, especially when the model has collapsing bounds.

Strengths:

The paper is well written and motivated, with clear depth of knowledge in the areas of neurophysiology of decision-making, sequential sampling models, and, in particular, the phenomenon of collapsing decision bounds.

Two large-scale simulations are run to test parameter recovery, and two empirical datasets are fit and assessed; the fitting procedures themselves are state-of-the-art, and the study makes use of a very new and well-designed ERP decomposition algorithm that provides single-trial estimates of the duration of diffusion; the results provide inferences about the operation of decision bound collapse - all of this is impressive.

We appreciate your feedback and comments. Below, we provided a response for each comment.

Weaknesses:

(1) This is an interesting and promising idea, but a very important issue is not clear: it is an intuitive principle that information from an external empirical source can enhance the reliability of parameter estimates for a given model, but how can the overall BIC improve, unless it is in fact a different model? Unfortunately, it is not clear whether and how the model structure itself differs between the NDTinformed and non-NDT-informed cases. Ideally, they are the same actual model, but with one getting extra guidance on where to place the tau and/or sigma parameters from external measurements. The absence of sigma (non-decision time variance) estimates for the non-NDT-informed model, however, suggests it is different in structure, not just in its lack of constraints. If they were the same model, whether they do or do not possess non-decision time variability (which is not currently clear), the only possible reason that the NDT-informed model could achieve better BIC is because the non-NDT-informed model gets lost in the fitting procedure and fails to find the global optimum. If they are in fact different models - for example, if the NDT-informed model is endowed with NDT variability, while the non-NDT-informed model is not - then the fit superiority doesn’t necessarily say anything about an NDT-informed reliability boost, but rather just that a model with NDT variability fits better than one without.

To respond to this comment, we would like to note that the structural difference between NDT-informed and uninformed models is the assumption about non-decision time. In principle, the behavioral parts (i.e., parameters related to the diffusion part) of both NDT-informed and uninformed models are identical. However, during the estimation, the non-decision time in the NDT-informed model is subject to an additional constraint imposed by the neural data. In other words, in the uninformed model, non-decision time is estimated using the behavioral data by maximizing the likelihood of a CT-DDM. However, the NDT-informed model incorporates an additional data type, resulting in a different likelihood function (see Equation (3)). Specifically, in the NDT-informed model, we make an additional assumption regarding the non-decision time: it is set to the mean of the trial-level non-decision time measurements distribution derived from neural data (Equation (3) specifies the joint model structure). This additional assumption constrains the search space of the non-decision time parameter in the NDT-informed model. As in the main text, we assumed that non-decision time measurements obtained from neural data are log-normally distributed, where sigma is the shape parameter of the log-normal distribution. Therefore, sigma can represent the variability of the non-decision time measurements, and it is not the trial-to-trial non-decision time variability parameter. Indeed, the non-decision time parameter is fixed across trials in both models. Also, it should be clear from Equation (3) that sigma only appears in the second term of the joint likelihood, which corresponds to non-decision time measurements and not the CT-DDM term. Therefore, the behavioral parts of the NDT-informed models and Uninformed models are identical, and the NDT-informed models include one additional parameter (i.e., sigma) corresponding to the variability in non-decision time measurements.

Also, to explain how constraining non-decision time improves the BIC, we would like to clarify that constraining non-decision time using an additional data source constrains the search space for non-decision time, thereby leading to better parameter identification and, consequently, a better fit to behavioral data. We included the following text in the discussion section to make this explicit.

“This improvement likely reflects more accurate parameter estimation enabled by the additional information. In other words, constraining the non-decision time using neural measurements led the optimizer to estimate the CT-DDM parameter more accurately and, as a result, improve the fit to empirical data.”

(2) One reason this is unclear is that Footnote 4 says that this study did not allow trial-to-trial variability in nondecision time, but the entire premise of using variable external single-trial estimates of nondecision times (illustrated in Figure 2) assumes there is nondecision time variability and that we have access to its distribution.

We are sorry for the confusion. To respond to this comment, we would like to highlight that this modelling approach does not include any mechanism for across-trial variability in the behavioral part, as the likelihood of the choice behavior (see Equation (3)) does not include any variability parameter. As mentioned before, sigma represents the variability in non-decision measurements. However, the model does not propagate the across-trial variability of the neural data on the behavior side (unlike the models in Ghaderi-Kangavari et al. 2023). In other words, in this approach, none of the diffusion model’s parameters include across-trial variability, and we have only considered and estimated neural data variability in the NDT-informed model. Also, to improve the manuscript’s coherence, we removed this footnote.

(3) It is good that there is an Intro section to explain how the tradeoff between NDT and collapsing bound parameters renders them difficult to simultaneously identify, but I think it needs more work to make it clear. First of all, it is not impossible to identify both, in the same way as, say, pre- and postdecisional nondecision time components cannot be resolved from behaviour alone - the intro had already talked about how collapsing bounds impact RT distribution shapes in specific ways, and obviously mean (or invariant) NDT can’t do that - it can only translate the whole distribution earlier/later on the time axis. This is at odds with the phrasing “one CANNOT estimate these three parameters simultaneously.” So it should be first clarified that this tradeoff is not absolute. Second, many readers will wonder if it is simply a matter of characterising the bound collapse time course as beginning at accumulation onset, instead of stimulus offset - does that not sidestep the issue? Third, assuming the above can be explained, and there is a reason to keep the collapse function aligned to stimulus onset, could the tradeoff be illustrated by picking two distinct sets of parameter values for non-decision time, starting threshold, and decay rate, which produce almost identical bound dynamics as a function of RT? It is not going to work for most readers to simply give the formula on line 211 and say ”There is a tradeoff.” Most readers will need more hand-holding.

We are grateful for this comment. In response to this comment, which was also partly mentioned by the first reviewer, we first highlight that, in the presence of a nonlinear collapsing threshold, the effect of non-decision time is no longer linear, as it forces the threshold to take a specific value at the final stopping point. To illustrate the tradeoff between imprecise non-decision time estimation and collapsing threshold estimation, we conducted a simulation study. The results for the simulation study are presented in Appendix 1. In this study, we contaminated the non-decision time with noise at six levels (i.e., 0%,2%,4%,6%,8%, and 10%). The simulation results showed that increasing the noise level in non-decision time worsens the estimation of the starting threshold and decay rate parameters, indicating a trade-off between non-decision time and collapsing threshold parameters.

Regarding the second point, we would like to clarify that in this paper, consistent with other works on collapsing threshold, we assumed that the collapsing starts with evidence accumulation and not with stimulus onset, as the decision makers need a short amount of time for perceiving and encoding the stimulus (i.e., perceptual encoding time). Fixing the collapsing onset to the stimulus onset introduces an ad hoc assumption into the model (that the encoding time is zero), which is cognitively implausible. Therefore, although this assumption can mathematically resolve the issue, it is not cognitively plausible. However, one important point we did not consider in the previous version is the two-stage accumulation process models in which the collapsing onset occurs later than the evidence-accumulation onset. We have discussed the estimation of such models as a limitation in the general discussion:

“The collapsing threshold dynamics considered in this work (e.g., exponential and hyperbolic) impose a monotonically decreasing threshold over time. Although these dynamics are theoretically well motivated (Fudenberg et al., 2018; Frazier and Yu, 2007) and have been employed in several previous studies (e.g., Olschewski et al., 2025; Milosavljevic et al., 2010; Voskuilen et al., 2016), some research has proposed delayed-collapsing threshold models (e.g., Diederich and Oswald, 2016), in which the onset of threshold collapse does not coincide with the onset of evidence accumulation. Estimating such delayed-collapsing models may require more than simply constraining non-decision time, as the onset of threshold collapse must also be identified. A promising approach for addressing this challenge is the HMP method, which may provide additional temporal information about distinct cognitive processing stages. In particular, HMP may allow the onset of threshold collapse to be estimated as a separate cognitive stage. Future research should therefore investigate the estimation of multi-stage evidence accumulation models (e.g., Diederich and Oswald, 2016; Diederich and Colonius, 2021) within the HMP framework.”

(4) A lognormal distribution is used as line 231 says it “must” produce a right-skew. Why? It is unusual for non-decision time distribution to be asymmetric in diffusion modeling, so this “must” statement must be fully explained and justified. Would I be right in saying that if either fixed or symmetrically distributed nondecision times were assumed, as in the majority of diffusion models, then the non-identifiability problem goes away? If the issue is one faced only by a special class of DDMs with lognormal NDT, this should be stated upfront.

We would like to clarify that this assumption is about the non-decision time measurements and not about the across-trial variability parameter of non-decision time. Although for computational convenience, non-decision time is often assumed to follow a normal distribution in diffusion modelling literature, some empirical studies have shown that the perceptual encoding time and total approximated non-decision time follow a right-skewed distribution. Moreover, as HMP estimations of non-decision time are usually right-skewed, we formalized the model with a log-normal distribution. However, we would like to note that the identifiability issue in collapsing-threshold diffusion models is not related to the distributional assumption over the non-decision time measurements, as poor parameter recovery of the collapsing threshold was also reported in Evans et al. (2020). To show that the distributional assumption about the non-decision time measurements does not affect the results, we conducted an additional simulation study in which we assumed a normal distribution for non-decision time measurements and showed that constraining non-decision time improves parameter recovery for collapsing threshold parameters. The results for this simulation are presented in Appendix 8 in the new version of the manuscript. We also revised line 231 as follows (see line 236 in the new version):

“Empirical studies on non-decision time measurement usually have reported a right-skewed distribution for their measurements (e.g., Weindel, 2021; Weindel et al., 2025). For instance, the measured perceptual encoding time and motor execution time reported by Weindel et al. (2025) are right-skewed. Therefore, we assume that the observed non-decision time measurements Z_n follow an approximate log-normal distribution, which is right-skewed (we will discuss how this distributional assumption can affect the results later). Thus, we model the non-decision time measurements Z_n, using a log-normal distribution with parameters µ and σ_z. The available measurements (i.e., observed data) at trial n can be represented as

follows:”

(5) In the simulation study methods, is the only difference between NDT-informed and non-informed models that the non-NDT-informed must also estimate tau and sigma, whereas the NDT-informed model “knows” these two parameters and so only has the other three to estimate? And is it the exact same data that the two models are fit to, in each of the simulation runs? Why is sigma missing from the uninformed part of Figure 4? If it is nondecision time variability, shouldn’t the model at least be aware of the existence of sigma and try to estimate it, in order for this to be a meaningful comparison?

As mentioned in the response to your first comment, the difference between NDT-informed and uninformed models is the access to an additional source of data related to non-decision time, and sigma represents the shape parameter of the non-decision time measurements distribution. Therefore, sigma belongs only to the NDT-informed model, and, as in the uninformed model, there is no additional data source, so the model does not include sigma.

(6) I am curious to know whether a linear bound collapse suffers from the same identifiability issues with NDT, or was it not considered here because it is so suboptimal next to the hyperbolic/exponential?

Thank you very much for this comment. The main reason we did not include linear collapsing threshold models was the assessment by Evans et al. (2020), which indicated that, with sufficient trials, these models can be estimated reasonably well. However, to investigate whether constraining non-decision time can also improve the estimation of linear collapsing threshold models, we conducted an additional simulation study, which is reported in Appendix 3 in the new version of the manuscript. The simulation results confirm those reported by Evans et al. (2020) and show that the parameters of the uninformed linear models can be identified using more than 500 trials. Constraining the non-decision time using the NDT-informed diffusion modeling framework still improves parameter estimation in the linear collapsing threshold model and reduces the required number of trials for reliable estimation to 250. Especially, the estimation of the starting threshold improves significantly.

(7) The approach using HMP rests on the assumption that accumulation onset is marked by the peak of a certain neural event, but even if it is highly predictive of accumulation onset, depending on what it reflects, it could come systematically earlier or later than the actual accumulation onset. Could the authors comment on what implications this might have for the approach?

Thank you for mentioning this point. We first would like to point out that Weindel et al. (2024) showed that HMP can predict the underlying generative distribution of cognitive states with high precision and without systematic bias. Second, it is worth highlighting the results reported in Appendix 5 (i.e., “Bias in non-decision time measurements”). In this appendix, we discussed how bias in non-decision time measurements (i.e., systematic underestimation or overestimation) affects the estimation of the collapsing threshold. Particularly, see Figure 3 in Appendix 5. To make these results clearer in the main text, we included the following paragraph at the end of the results section in simulation study 1:

“Additionally, we examined the effect of systematic bias in non-decision time measurement on parameter recovery. Appendix 5 presents the parameter recovery simulation results in the presence of biased non-decision time measurement (i.e., systematically underestimated or overestimated). The results revealed that, even in the presence of biased non-decision time measurement, the actual generating parameters show a high correlation with the estimated parameters. Underestimation in non-decision time leads to overestimation in the starting threshold and decay rate. Conversely, overestimation in non-decision time leads to underestimation in both the starting threshold and non-decision time.”

(8) Figure 7: for this simulation, it would be helpful to know the degree to which you can get away with not equipping the model to capture drift rate variability, when the degree of that d.r. variability actually produces appreciable slow error rates. The approach here is to sample uniformly from ranges of the parameters, but how many of these produce data that can be reasonably recognised as similar to human behaviour on typical perceptual decision tasks? The authors point out that only 5% of fits estimate an appreciable bound collapse but if there are only 10% of the parameter vectors that produce data in a typical RT range with typical error rates etc, and half of these produce an appreciable downturn in accuracy for slower RT, and all of the latter represent that 5%, then that’s quite a different story. An easy fix would be to plot estimated decay as a scatter plot against the rate of decline of accuracy from the median RT to the slowest RT, to visualise the degree to which slow errors can be absorbed by the no-dr-var model without falsely estimating steep bound collapse. In general, I’m not so sure of the value of this section, since, in principle, there is no getting around the fact that if what is in truth a drift-variability source of slow errors is fit with a model that can only capture it with a collapsing bound, it will estimate a collapsing bound, or just fail to capture those slow errors.

Thank you for this comment. We would like to first note that the aim of this section is to illustrate that NDT-informed modeling enables us to distinguish between CT-DDM and FT-DDM with drift variability (i.e., the two competing models that are relatively hard to distinguish). Therefore, we changed the name of this section to “Simulation study 2: Model recovery”. In the new version of the manuscript, we included a cross-model fitting simulation and a model recovery simulation in this section. The estimated decay rates in the cross-model fitting study indicate that, when the underlying generating model is FT-DDM with drift variability, parameter estimation using the NDT-informed approach yields precise inference. This is due to the estimated decay rate, which is very close to zero. The model recovery results also confirmed that incorporating the decay rate value into the model inference improves precision.

Moreover, to address the concern regarding the slow-error pattern in the simulated data, we examined the relationship between the slow–fast accuracy difference and the estimated decay rate. Specifically, we computed the difference between the accuracy of responses with response times below the median (ACC1) and those above the median (ACC2), and plotted this difference against the estimated decay rate. Author response image 1 presents the resulting scatter plot, with color indicating the drift rate. As shown in Author response image 1, incorrect inferences about the decay rate primarily occur at high drift rates. This pattern emerges because high drift rates produce very fast responses, leaving little time for the threshold to meaningfully collapse. Consequently, the behavioral signatures of collapsing-threshold and fixed-threshold models become increasingly similar under high drift conditions.

Author response image 1.

Illustration of the difference between the accuracies of responses with response time below the median and those with response time above the median against the estimated decay rate. Colour shows the drift rate value.

Reviewer #2 (Recommendations for the authors):

(1) Abstract: improves fit to behaviour in what way? Reliability or absolute quant fit to behavior? I.e., is it just helping constrain it so it finds the global opt?

(2) Line 72 - Are these “neuroimaging” studies? Perhaps use the broader term “neuroscience.”

(3) Line 95 - It’s important because it may confuse readers how something dynamic like a collapsing bound could be resolved with, say, fMRI.

(4) Line 85 – “greater variability”... in what?

(5) Line 87 -Revise to avoid misconstruing a time on task effect - e.g., “higher error rate for trials with longer RT” is more explicit.

(6) Line 89-94 - It’s not clear what findings are being referenced here.

(7) Line 103 - External biases such as priors and relative value?

(8) Line 175 - Clarify this applies to any ddm, not just ctddm.

(9) Line 268 - Explain what portion N200 accounts for.

(10) Line 327 - Is this equation supposed to be for Delta-X, as opposed to X(t+delta-t)? If you want X(t+delta-t) on the LHS, then X(t) must be added to the RHS.

We are very thankful for such a precise evaluation and constructive comments. We addressed all the comments raised by the reviewer in the revised manuscript.

Reviewer #3 (Public review):

Summary:

The current paper addresses an important issue in evidence accumulation models: many modelers implement flat decision boundaries because the collapsing alternatives are hard to reliably estimate. Here, using simulations, the authors demonstrate that parameter recovery can be drastically improved by providing the model with additional data (specifically, an EEG-informed estimate of nondecision time). Moreover, in two empirical datasets, it is shown that those EEG-informed models provide a better fit to the data. The method seems sound and promising and might inform future work on the debate regarding flat vs collapsing choice boundaries. As an evidence-accumulation enthusiast, I am quite excited about this work, although for a broader audience, the immediate applicability of this approach seems limited because it does require EEG data (i.e., limiting widespread use of the method or e.g., answering questions about individual differences that require a very large N).

We are very grateful for your positive evaluation and your comments.

Reviewer #3 (Recommendations for the authors):

This is a very decent study, very well written and properly executed. Most of my comments below are suggestions for the authors as to how to make the story more compelling.

(1) I think the authors can do more to explain why the NDT-informed models fit better to empirical data. If the NDT-estimates are equal to the ground truth, then isn’t it possible that such models win simply because they have one parameter less? However, this is not what the authors are claiming, though, on l.567 it says that the fit is better because parameters are better estimated. I think it should be possible to dissociate these two accounts.

Thank you for this important comment. For clarification, both NDT-informed and uninformed models estimate the non-decision time parameter, and neither treats it as equal to the ground truth. However, the difference between these two models is that, in the NDT-informed model, the non-decision time is subject to an additional constraint; therefore, the number of behavioral parameters (i.e., parameters of the diffusion part) is identical for both NDT-informed and uninformed collapsing threshold models. Although the number of behavioral parameters is identical in the NDT-informed model, one parameter is constrained, thereby limiting the model’s complexity and flexibility compared to uninformed models. Consequently, the improvement in the fit can only be attributed to better parameter estimation in the NDT-informed models, resulting from constraining the non-decision time using neural measurements. To clarify that in the manuscript, we included the following text in the revised version:

“This improvement likely reflects more accurate parameter estimation enabled by the additional information. In other words, constraining the non-decision time using neural measurements led the optimizer to estimate the CT-DDM parameter more accurately and, as a result, improve the fit to empirical data.”

(2) Given that so much of the writing focuses on the conclusion that collapsing boundary models ¿ flat models, it is very odd that there is no comparison to a flat boundary model reported in the text. Why is the model in Supplement 5 not just included in the main text (and in Table 1)? This would make it so much easier for the reader.

To address this comment and also the similar point raised by Reviewer 1, we included the NDT-informed FT-DDM in the results section and compared the FT-DDM with CT-DDMs with respect to BIC_Joint. However, we retained the other FT-DDM in the appendix because this model includes across-trial variability in drift rate, whereas the models in the main text do not.

(3) I would have appreciated a bit more background about the importance of the number of trials per participant. Given that the proposed method requires collecting EEG data (which is time and labour-intensive) I wonder to what extent you get similar improvements in parameter recovery by collecting more data per participant (which is usually cheap). Put differently, I would appreciate an additional matrix in Figure 5 for vanilla models.

The new version of Figure 5 in the revised manuscript now contains the goodness of parameter recovery for the uninformed CT-DDMs for different numbers of trials. As the simulation results suggest, even with 1000 trials, the parameters of the uninformed CT-DDMs are still not reliably identifiable. Therefore, these results suggest that although increasing the number of trials can slightly improve the parameter recovery of the CT-DDMs, it cannot fully resolve the reliability issue in their parameter recovery.

In addition, it is worth clarifying that, although the paper focuses on extracting non-decision time from the EEG signal using the HMP method, as discussed in the general discussion, the NDT-informed approach can also be employed with purely behavioral methods.

(4) L116-117: minor detail: I don’t think it’s fair to write that it’s an open question whether or not thresholds collapse. I think it’s fair to say that this is hard to show, and that the conditions under which it appears are unclear; but saying that it’s still unclear whether this occurs at all seems unfair with regard to previous work.

Thank you for mentioning this point. We revised the mentioned sentence as follows in the new version of the manuscript:

“This issue is particularly critical given that the conditions under which individuals adjust their decision thresholds during a single trial remain an open question.”

(5) Figure 5: Minor detail: It would be useful to mention in the figure or caption how many trials underlie these simulations, which is now somewhat buried in the text.

As Figure 5 shows sensitivity to the number of trials, and the number of trials is explicitly mentioned in the figure, we assume that the reviewer intended Figure 6. In the revised manuscript, we explicitly specify the number of trials for the results reported in Figure 6. We simulated 500 trials for each noise level in this graph.

(6) Figure 10 and similar figures: I tried to figure out how corrects and incorrects differ, but couldn’t see the difference. Can the authors use something more colorblind friendly (hope I didn’t give up on being anonymous here)?

We are so sorry for the inconvenience. In the revised manuscript, we used different symbols to distinguish correct and incorrect data.

Author response:

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

eLife Assessment

This important study investigates the peptide-binding principles of promiscuous chicken MHC molecules. The data from crystallography, mass spectrometry, and modeling are convincing. However, the presentation would benefit from streamlining and clear links between data and conclusions. This paper will be of broad interest to immunologists and those interested in vaccine development.

Overall, we are delighted and grateful to the eLIFE editors and the two reviewers for the careful and thoughtful assessments and reviews of our paper. We are glad that the strengths of the paper were apparent and appreciated. And of course, every paper has weaknesses, especially for a story as complex as this one.

We made only minor changes to accommodate the reviewer comments, along with additions for which we only became aware upon this submission of a revised manuscript. In particular, we shortened the title and abstract to fit what is usual for an eLIFE paper, added Key Resources table with accompanying references, changed the numbering of the figures throughout the manuscript to ensure that each page represented a figure (rather than panels of a figure), moved the figure legends from the embedded figures to a list near the end of the manuscript, and split the supplemental spreadsheet into two renamed Data Source files.

Before answering the comments and questions directly, perhaps a few points would help clarify why the paper is as it is.

First, the experiments cover over three decades of work, with the first gas phase sequencing results done in 1992. Unlike some of the chicken class I alleles which immediately gave completely clear stringent motifs (B4, B12 and B15 in Wallny et al 2006 PNAS, B19 in Han et al 2023 J Immunol), we harvested nothing but confusion from the B21 class I results (Fig. 1). Initially, we thought that the lack of a clear motif for B21 was due to multiple well-expressed class I molecules but only one dominantly-expressed class I molecule was found (Wallny et al 2006 PNAS, Shaw et al 2007 J Immunol) and, to our surprise, bacterially-expressed BF2*21:01 heavy chain and b₂-microglobulin refolded with two synthetic peptides without sequence in common, and the crystal structures showed that this molecule remodeled the binding site to accommodate two such disparate peptides (Koch et al 2008 Immunity). This was the beginning of our understanding of the spectrum of class I alleles from promiscuous generalists to fastidious specialists, which we have explored in a series of further papers (in particular, Chappell et al 2015 eLIFE, Tresgaskes et al 2016 PNAS, Kaufman 2018 Trends Immunol, Tregaskes and Kaufman 2022 Mol Immunol).

Second, over these many years, we continued to explore the binding properties of BF2*21:01 in ever more detail, resulting in the current manuscript. We learned only slowly how to probe this unexpected promiscuity, unprecedented in the MHC literature, so that the experiments proceeded with our best understanding at the time, including taking advantage of new approaches as they become available. Each experiment built on the previous set of experiments and each brought us closer to an understanding.

Third, having amassed a collection of data, we chose eLIFE exactly because it allows us to present the entire story from beginning to end without compromise, not just the highlights with the major points illustrated by a few main figures and with the supporting data in many supplementary figures. We include all the data, because it is all part of the story, and so interested researchers to look at the data from their own perspective. Although mostly we provide bar graphs, we include spreadsheets for the raw data (or close to them) for the final experiments (illustrated by Figs. 10 and 14-22) in the two source data files, so these can be assessed easily by others in the field, perhaps using approaches that we may not feel competent to perform.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Combining in vitro refolding, SEC-based assembly assays, peptide-library screening, MALDI-TOF, LC-MS/MS, structural analysis and immunopeptidomics, this manuscript investigates the peptide-binding principles of the promiscuous chicken MHC-I molecule BF2*21:01.

Strengths:

Although the peptide motif of BF2*21:01 is highly complex, this manuscript identified several principles, including a preference for 10-mer peptides, co-variation between P2 and Pc-2, effects of P3 and Pc-3, and a strong cellular preference for Leu at Pc. The results are important for avian MHC biology and poultry vaccine epitope prediction.

Weaknesses:

The manuscript is sometimes difficult to follow because the authors present a large amount of peptide-library, structural and immunopeptidomics data. without always clearly explaining how these datasets support the proposed simplifying principles.

We are delighted and grateful to the reviewer 1 for the careful and thoughtful comments and questions concerning our manuscript. We are glad that the strengths of the paper were apparent and appreciated, and acknowledge the weaknesses that come with such a complex story with experiments performed over decades.

Major Issues - Points Requiring Clarification or Additional Support:

(1) Line 282-301, 537-545）

The immunopeptidomics conclusions are mainly based on one B21 cell line with one biological replicate and at least two technical replicates. Given the complexity of the BF2*21:01 peptide repertoire, this is a major limitation. The authors should either provide additional biological replicates or clearly state this limitation in the Abstract, Results and Discussion.

This limitation is clearly stated in lines 537-545, as part of a paragraph covering the various ways in which the data presented in this manuscript could be improved. In fact, we have performed immunopeptidomics of several different B21 cell types, with many replicates and found similar data as presented, giving us confidence in our interpretations. However, these other experiments belong in different stories, so it is not appropriate that the data be reported in this manuscript.

(2) (Lines 290-313）

The B21 cell preparations contain both BF2 and the lowly expressed BF1 molecule. Some peptides, especially 8-mers or peptides with atypical motifs, may derive from BF1*21:01. The authors should clarify how BF2*21:01-bound peptides were distinguished from possible BF1-derived peptides, or interpret the immunopeptidomics motif more cautiously. The authors should also provide or cite evidence confirming the B21 haplotype identity of the cell line and chicken materials used for immunopeptidomics.

The concern about the contribution of BF1*21:01 to the immunopeptidomics is clearly stated in the manuscript, both lines 290-313 and as part of the paragraph describing the limitations of the experiments (lines 542-543). In fact, the expression of BF1 molecules has long been known to be less than 10% of BF2 molecules at the RNA level, and much less at the protein level (Wallny et al 2006 PNAS, Shaw et al 2007 J Immunol). The proportion of 8mers identified by immunopeptidomics is also low (Fig. 14), and it is not impossible that most 8mers are due to BF1*21:01. We have used assembly assays with peptide libraries, immunopeptidomics and a crystal structure to determine the peptide motif for typical BF1 molecules, of which BF1*21:01 is one and found it may contribute to 8mer peptides but very seldom to longer peptides. This work is unpublished but gives us confidence that the characteristics of BF2*21:01 are not misrepresented by the data in this manuscript.

The sources of the chicken samples and the cell lines are described in detail under Materials and Methods (lines 577-590), citing relevant publications.

(3) (Lines 217-221, 243-253)

The authors acknowledge that MALDI-TOF cannot reliably distinguish peptide combinations with identical or similar masses, nor determine residue positions in some cases. Therefore, MALDI-TOF results should not be overinterpreted as precise evidence for residue preference. The authors should clearly indicate which conclusions are supported by LC-MS/MS.

As described, the experiments follow each other in temporal sequence, so that we started with single peptides, then peptide libraries that varied in one position, then peptide libraries that varied in two positions first analysed by MALDI-TOF and later by LC-MS/MS. The final experiment (Fig. 10, with the original data in the supplementary spreadsheet) directly compares MALDI-TOF and LC-MS/MS results for six peptide libraries, so that the strength of the evidence for residue preference is clear. Throughout the manuscript, we do our best to not to overstate conclusions based on the data of any particular experiment.

(4) (Lines 297-301, 316-330)

The authors suggest that longer peptides may bulge in the middle or extend out of the groove at the C-terminal end. The rationale for the C-terminal extension is not clearly explained. Why is the C-terminal extension considered rather than the N-terminal extension? If the binding register is uncertain, long peptides should be analyzed separately from canonical-length peptides.

When the first sequence of a chicken class I cDNA was determined, an immediate mystery was why one of the so-called invariant residues that coordinate the N- and C-termini of the bound peptide is not conserved (Kaufman et al 1992 J Immunol). In fact, this residue Tyr at position 86 in HLA-A2 and the equivalent position in all mammalian classical class I molecules is an Arg in the classical class I molecules of all non-mammalian vertebrates and is common with class II molecules (Kaufman et al 1995 Semin Immunol). Similar to class II molecules, this Arg in chicken class I molecules allows the peptide to extend out of the C-terminus, as shown by a crystal structure (Xiao et al 2018 J Immunol). The concern that we might be misidentifying the C-terminal amino acid was the basis for the analysis in Figs. 23 and 24, but in the absence of crystal structures, we are not able to provide a final answer this question. Perhaps relevant is the fact that a chicken class II molecule can bind exactly the same peptide in two conformations, one with a canonical 9mer core and the other with an unexpected 10mer core (Goryanin et al 2026 J Virol).

By contrast, N-terminal extensions are only found for some class I alleles and thus far depend on the substitution of small amino acid sidechains for W166 (Li et al 2011 J Virol for bovine, Ma et al 2020 J Immunol for Xenopus, Wei et al 2022 J Immunol for ovine). Thus far, no chicken BF2 sequences have this substitution, consonant with the many crystal structures, including those for BF2*21:01 (Koch et al 2008 Immunity, Chappell et al 2015 eLIFE, this manuscript). However, in unpublished data, we find that most BF1 sequences have sequence differences that could allow N-terminal extensions, although we have no crystal structures to support this possibility.

(5) (Lines 406-439)

In vitro assembly assays show that several hydrophobic residues can be tolerated at Pc, whereas immunopeptidomics shows a strong Leu preference at this position. The authors should clarify whether this Leu preference reflects intrinsic BF2*21:01 binding specificity, TAP-mediated peptide transport, antigen processing, peptide loading, or a cell-line-specific effect. Additional experimental support, such as TAP transport analysis, would strengthen this conclusion.

The preference for Leu at the final position of the peptide by immunopeptidomics of the B21 cell line is strong but not absolute and is certainly affected at the least by the length of the peptide (Figs. 23 and 24). Unpublished immunopeptidomics results (mentioned above) show that this is not a cell line-specific result. The evidence from assembly assays of various peptides is that several hydrophobic amino acids are tolerated with sufficient stability of BF2*21:01 that they are detected in the assay (Figs. 3, 5, 9 and 10). Thermostability assays (Fig. 6) show that peptides with these same hydrophobic amino acids are stable to at least body temperature of chickens. These experiments show that such stability is peptide-dependent (that is, whether a particular amino acid is tolerated depends on the stability conferred by the rest of the peptide). Finally, peptide translocation assays using B21 cells have been done (Tregaskes et al 2016 PNAS) and show that peptides with several hydrophobic amino acids can be pumped into the lumen of the endoplasmic reticulum. However, the assays are with single synthetic peptides, so the data are not extensive enough to separate the effects of the final amino acid from the rest of the peptide. Certainly, peptides with amino acids other than Leu at the C-terminus can be translocated. So, it is not yet clear at which point the preference for Leu at the C-terminus of the peptide arises.

(6) (Lines 172-178, 243-279, 442-457)

The structural analysis explains some residue combinations, such as Arg at P2 with Glu at Pc-2 or Trp at Pc. However, the structural interpretation is not fully integrated with the large-scale peptide library and immunopeptidomics results. Representative high- and low-frequency combinations should be discussed structurally.

Six crystal structures show that BF2*21:02 remodels the binding to accommodate a variety of anchor residues (Koch et al 2008 Immunity, Chappel et al 2015 eLIFE). These crystal structures are representative of sequences found by the immunopeptidomics from very frequent (H-E at roughly 15% 8-12mers) to moderately frequent (E-L at roughly 6% 8-12mers) to infrequent (N-F, A-D and E-D at roughly 1.5%, 1.6% and 0.7% 8-12mers) based on Fig. 18. All but one of the structures has Leu at the C-terminus, with the last one having Val which is found but not frequently by immunopeptidomics.

Similar numbers are found by LC-MS/MS of double-substitution libraries of the two original peptide sequences in Fig. 10 with H-E found frequently (8.1% in P390, 3.8% in P498) and the others infrequently (0.1, 0.9, 1.0, 0.3% in P390, 0, 1.4, 1.0, 0.3% in P498), as calculated from the numbers in the Supplementary data spreadsheet. As discussed in the manuscript, for single-substitution peptide libraries of the two original peptides, Ile/Leu at the C-terminus was very frequent but at the same or slightly less level as Phe, with Met less frequent and Val even less so (Fig. 7).

In addition, there are two more structures along with models explicitly testing some substitutions (Fig. 5). Attempting more current modelling approaches, we found AlphaFold 3 was unable to correctly predict most of the conformations that are found in the crystal structures of BF2*21:01, so we don’t feel confident in using them to predict unknown structures of this kind.

(7) The inference of co-variation between P2 and Pc-2, as well as the modulatory effects of P3 and Pc-3, should be better explained. At present, some conclusions appear to be based mainly on residue-frequency patterns, and the logical connection between these observations and the proposed binding principles is not always clear. Statistical analyses, such as mutual information, chi-square tests or permutation tests, and representative structural explanations would strengthen this conclusion.

We endeavored to do our best to explain the data, our interpretations and our reasoning, so we apologise if we have not managed to be as clear as might be desired. We have included as close to raw data as possible for the LC-MS/MS and MALDI-TOF (Fig. 10) and for the immunopeptidomics (Fig. 14 and 18) in the Supplementary Data spreadsheet, exactly so that competent practitioners can carry out further analyses (including the sophisticated statistical tests mentioned).

Reviewer #2 (Public review):

Summary:

The study presents an in-depth analysis of the peptide repertoire bound by a promiscuous chicken MHC molecule using mass spectrometry, x-ray crystallography and modelling. While the MHC can bind a very diverse set of peptides, the authors have found some new rules that govern peptide binding to this MHC that could help to build a predictive model to study the repertoire of pathogen-derived peptides.

Strengths:

The study uses a range of well performed experiment across multiple techniques and provides an in-depth analysis of the peptide repertoire, including peptide sequences, length, preferred residues, stability and MHC presentation.

Weaknesses:

The data overall support the analysis and conclusion well. The only caveat is linked to Figure 4, which does not describe the stability of the peptide-MHC complex, but instead shows refold yield, and the two are not always linked.

We are grateful for the clear understanding of the strengths of the work. With regards to Fig. 4, we agree with the reviewer that there are differences in refold yield but that measure may not be correlated with stability of the peptide-MHC complex. However, we were basing our interpretation of stability on the position and quality of the monomer peak, as illustrated by the trace in Fig. 2, in which a sharp peak at the monomer position represents a stable complex (as seen for the 10 and 11mer peptides) and later peaks represent unstable complexes falling apart during the chromatography (as seen for the 7, 8 and 9mer peptides).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Minor Issues: Editorial and Data Presentation Modifications

(1) Lines 53-62, 155-170, 303-314: The terms Pc, Pc-2 and Pc-3 should be clearly defined early in the manuscript and figure legends.

The Abstract introduces the abbreviations as “peptide positions P₂ and P_c-2” followed by P_C, which are standard usage and seem clear. The first usage in the text is “anchor residues at three positions, with co-variation between the anchor residues at P₂ and P_c-2” which again seems clear, particularly in the context of the text and the figure. However, a parenthetical description has been added to read “…anchor residues at three positions, with co-variation between the anchor residues at P₂ and P_c-2 (position 2 and the position two before the C-terminus) …”. Given these usages, it seems unlikely that the reader will fail to understand P_C and P_C-3.

(2) Lines 255-279: The term "peptide backbone" should be defined as the fixed sequence context outside the randomized positions, if this is what the authors mean. Suggest clarifying the meaning of "peptide backbone".

The phrase reads “double-substitution libraries based on four peptide backbones”, which in context of the figures seems clear. However, a parenthetical description has been added: “The examination of double-substitution libraries analysed by MALDI-TOF was expanded to other backbones (that is, other sequences in which two positions were randomised): …”.

(3) Several figures are complex. The authors should add brief take-home messages to figure legends.

Every figure legend starts with a (sometimes quite long) take-home message. It is not clear what more should be added.

(4) A concise summary table of the proposed binding rules, including preferred peptide length, P2, Pc-2 and Pc preferences, and the effects of P3/Pc-3, would be useful for readers.

A concise summary table of binding rules would be very helpful, but the rules are complex, both qualitative and quantitative. For example, immunopeptidomics shows that 10mers are preferred, but that fails to capture the quantitation. The co-variation of P₂ and P_c-2, which is the strongest and best characterized correlation, nevertheless is complex since the occupancy of P₂ by different amino acids (presumably independently of P_c-2) varies considerably. At our current level of understanding, it is hard to imagine a table that is both concise and precise. With time and more data, perhaps code for quantitative prediction might be constructed (dare one suggest machine learning…), which is the hope of presenting all the available data in one place.

(5) The Results section contains a large amount of peptide-library, structural and immunopeptidomics data. The authors should improve the logical flow and add clearer transition sentences to explain how each dataset supports the proposed simplifying principles.

The reviewer is of course correct that any written text can be improved (although each critic may have a different idea about which part should be fixed), but we have done our best with the material and time available. We could respond productively to a more detailed critique.

(6) Some statements in the Abstract and Discussion should be softened, especially those related to in vivo peptide preferences, BF2*21:01 promiscuity and peptide prediction, given the limited biological replication and uncertainty in peptide assignment.

The statements in the both the Abstract and Discussion are very general, reflecting what we believe to be careful interpretations based on the data. We could respond productively to concerns about specific claims.

Reviewer #2 (Recommendations for the authors):

Overall, the data presented in this study are interesting; however, it is complex, and some results could be merged and simplified, as well as the figures. The data provide an in-depth analysis, using mass spectrometry, of the interplay between the different positions of the peptide and the residues favourable to bind within the antigen-binding cleft.

(1) From the abstract, the concept of "promiscuous generalists and fastidious specialists" is not explored after or defined within the results.

The Abstract introduces the concept of promiscuous generalists and fastidious specialists to provide the basis for exploring the peptide-binding specificity of the most promiscuous class I known, BF2*21:01. This overall concept is described in enormous detail in several publications cited in the current manuscript, but it is not particularly germane to the analyses.

(2) From the abstract "These simplifying principles may eventually allow predictions of pathogen peptides", I'm not sure how "simplifying" the principles are with the data, if anything, it does show a rather complex interplay between the different residues of the peptide that enable the MHC to bind a large and diverse number of peptides.

Compared to any combination of anchor residues being permitted at equal frequency, there are clear preferences which the experiments identify. Instead of an enormous range of possible peptide lengths, roughly 50% of peptides are 10mers. Of course, the structural reasons behind these results are certainly complex and likely must be understood in detail in order to attempt peptide predictions. 

(3) Line 48. "less well-expressed". Less than what? Do you mean the level of expression was lower? And if yes, are there values of fold change for comparison?

The sentence in the Abstract reads “Chicken BF2 alleles … are less well-expressed on the cell surface … while certain human HLA-B alleles … are well-expressed …”. Read as a complete sentence, the meaning is clear. This difference for chicken BF2 alleles has been quantified as reported in several publications cited in the current manuscript, ranging from 3-5 fold for peripheral blood lymphocytes to ten-fold for erythrocytes (Kaufman et al 1995 Immunol Rev, Chappel et al 2015 eLIFE), with similar numbers for a few HLA-B alleles on human peripheral blood lymphocytes and monocytes (Chappell et al 2015 eLIFE).

(4) Line 149. "with individual peptides" which peptides are we referring to here?

This introductory sentence to a paragraph outlines the general method used for the experiments in this section of the Results, “refolding in vitro … with individual peptides.” Which “individual peptides” are described in the following paragraphs, with the next section of the Results using “refolding in vitro … with peptide libraries”.

(5) Line 170. If 9 mers and below are not stable, which is not really quantified or shown with the data on Figure 4, why is refolding material observed for peptides with different lengths of 9 aa and below on Figure 4? A lower yield of refolded material can have a different origin, and there is no association between stability and refold yield. The notion of stability here probably needs to be changed, as it does not apply to the data.

As described in our response to a similar concern above, we are not basing our interpretation of stability on the quantity of refolded material, but on the position and quality of the monomer peak, as described clearly in the legend to Fig. 4: “The original 10mer (REVDEQLLSV) and 11mer (GHAEEYGAETL) peptides refold with BF2*21:01 to give stable monomers as do 11mer and 10mer derivative peptides, but 9mer, 8mer or 7mer peptides give heavy chain only peaks” and “The peptides 11mer GHAEEYAETL (top panel), 10mer REVDEQLLSV (middle panel), 11mer GHAEAAAAETL and 10mer GHAEAAAETL (bottom panel) gave sharp monomer peaks, while the 9mer GHAEAAETL, 8mer GHAEAETL and 7mer GHAEETL gave a delayed broad peak indicative of unstable binding or heavy chain.” This concept is illustrated by the trace in Fig. 2 (discussed in the text at the beginning of this section of the Results), in which a sharp peak at the monomer position represents a stable complex, and later peaks represent unstable complexes falling apart during the chromatography or free heavy chains.

(6) Line 175. As the 3BEV structure had a P2-His, is a comparable structure expected?

This sentence reads “Structures with amino acid substitutions in the 11mer peptide GHAEEYGAETL bind with Asp at P_c-2 and either His or Arg at P₂ (5AD0 and 5ADZ), comparable to the original structure (3BEV) (Fig. 5A).” Minor changes in positions and orientations of individual amino acid sidechains are expected and are clear from the crystal structures presented in Fig. 5A, but are overall comparable to the original peptide in 3BEV, which has a His at P₂ and a Glu at P_c-2.

(7) Line 175 "modelling the substituted". How was the modelling done?

The sentence reads “Modelling the substituted peptide with Arg at P₂ and Glu at P_c-2 shows a steric clash that can explain why this peptide did not refold with BF2*21:01 (Fig. 5A).” The legend to Fig. 5A states that “modelling done as detailed in Materials and Methods”, but apparently that section was omitted. A section has been added now to the Materials and Methods which states “Beginning with known crystal structures, modelling was carried out using PyMol with the protein mutagenesis Wizard, the rotamer toggle, show bumps and show surfaces.”

(8) Line 176 "shows a steric clash" with what? Figure 5 is too small to see, and there is no label on the residue to follow where the steric clash is coming from.

As stated in the legend to Fig. 5, “Structures were determined for GHAEEYGAETL (3BEV), GHAEEYGADTL (5AD0) and GRAEEYGADTL (5ACZ), which all refolded successful to give stable monomers, while GRAEEYGAETL did not (see Fig. 3), all models of which showed steric clashes (one depicted, red arrow).” In the model shown, the clash is between R9 of the BF2*21:01 with the Glu at peptide position 9. Parenthetically, this depiction of the key MHC residues for the co-variation has been used repeatedly, starting with Chappell et al 2015 eLIFE. The picture can be zoomed to make it large enough to see.

(9) Line 247 "many combinations". It is not clear here if combinations are referring to a set of double-substitutions or different peptides?

Each peptide in the library has a different double-substitution, so the meaning is the same either way. The point of Fig. 10 is to compare the identification of peptides from LC-MS/MS (in which each peptide is identified exactly) with the identification of sets of peptides from MALDI-TOF (in which the order of the double substitution is not clear, as well as the exact amino acid in the cases of I/L and Q/K). As the figure shows, the numbers are generally very similar, but this sentence describes the percentage of cases for which only one method or the other identified a peptide.

(10) Lines 252-253. The conclusion of the MS data that the LC-MS/NS is more accurate and sensitive than MALDI-TOF is not very surprising. What was the rationale for using both?

Our examination of the binding properties of BF2*21:01 for peptides and peptide libraries developed over a long time-span, so in the beginning we looked at single peptides with size exclusion chromatography peaks as the measure, then single- and later double-substitution libraries, first by MALDI-TOF and later by LC-MS/MS. Each set of experiments built on the previous work, so that together they tell the story. For example, after we optimized the use of double-substitution libraries, we were worried about the effects of temperature, so we tested that by MALDI-TOF. While repeating the temperature experiment once we optimized the LC-MS/MS approach might have yielded some additional data, there were other questions to answer.

(11) Line 272-273 "support the idea that P3 is an important position within the peptide (Figures 8-10) despite not contacting the MHC molecule" The structure of 3BEV clearly shows interaction between the P3-Ala and the Tyr156 of the MHC. Residues that are fully or partially buried in the MHC cleft almost all contact the MHC molecule. Maybe I've missed something, but I think this statement is inaccurate.

We agree with the reviewer that nearly every peptide residue contacts the MHC molecule (but of course some much more than others). The statement is now changed in the text to read “support the idea that P₃ is an important position within the peptide (Figures 8-10) despite not being an anchor residue."

(12) Line 294. Figure 14 clearly shows that the number of 8 and 9-mer peptides eluted is at the same level as the 11mer and above, so how does the data fit with the statement that 9mer and shorter peptides are not stable with the MHC?

Fig. 4 shows that 7, 8 and 9mer derivatives of the original 11mer failed to refold to give a single peak of stable monomers, while Fig. 6 shows that the 10mer derivative of the original 11mer was more thermostable than both the 9mer derivative and the original 11mer. The reason why the 9mer yielded so little monomer in Fig. 4 while giving enough to test by thermostability in Fig. 6 is no longer remembered. A key point is that these results are peptide sequence-specific, so it is not impossible to imagine stable binding of an appropriate 8mer (or perhaps even a 7mer). Another uncertainty, mentioned in the Results and Discussion, is that BF1*21:01 molecules bind primarily 8mers, and the contribution of peptides from BF1*21:01 is not known with certainty.

(13) Line 316. What was the rationale for choosing peptides > 12aa to see if there is some overhang or bulge? As even 11-12mer can exhibit such features.

We were just looking for any obvious patterns, but we didn’t find any.

(14) The section starting at line 366 would have benefited from some structure prediction or modelling to illustrate the findings.

We would have been delighted to model peptides, but we have used AlphaFold3 to compare the models to our crystal structures for seven chicken class I alleles (including BF2*21:01) with one or more peptides. The models sometimes fit the experimental data but they often didn’t, often by a wide margin, and with BF2*21:01 the worst (presumably because the system is not trained on MHC molecules which utilise charge transfer). Therefore, we do not feel confident in using any such modelling approaches except in the most defined situations (such as illustrated in Fig. 5).

(15) Typo - Alleles should be italic, and in vitro as well.

Alleles of genes are in italics, but alleles of proteins are not. To write in vitro in italics is customary, which we have corrected.

(16) Figures

(a) Some of the figures could be merged together.

Of course, any presentation can be improved, but which figures we should merge (some already being three pages in length) is not clear. We could productively respond to more detailed suggestions.

(b) Figure 1. I can't see the different colours mentioned in the figure legend

Our apologies if the colours are not clear enough, but they are present only as an aid (as elsewhere in the manuscript), with red D and E, blue H, K and R, green N, Q, S and T, and all other amino acids black.

(c) Figure 12. Is this figure only with 11mer peptides?

Figure 12 shows the percentage of peptides with particular amino acids at P₂ and P_c-2 for three 11-mer double-substitution peptide libraries, the sequences of which are written on the graphs and described in the figure legends.

(d) Table 1. The name of the protein should be added to the table.

OK.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This study by Vitar et al. probes the molecular identity and functional specialization of pH-sensing channels in cerebrospinal fluid-contacting neurons (CSFcNs). Combining patch-clamp electrophysiology, laser-based local acidification, immunohistochemistry, and confocal imaging, the authors propose that PKD2L1 channels localized to the apical protrusion (ApPr) function as the predominant dual-mode pH sensor in these cells.

The work establishes a compelling spatial-physiological link between channel localization and chemosensory behavior. The integration of optical and electrical approaches is technically strong, and the separation of phasic and sustained response modes offers a useful conceptual advance for understanding how CSF composition is monitored.

Several aspects of data interpretation, however, require clarification or reanalysis-most notably the single-channel analyses (event counts, Po metrics, and mixed parameters), the statistical treatment, and the interpretation of purported "OFF currents." Additional issues include PKD2L1-TRPP3 nomenclature consistency, kinetic comparison with ASICs, and the physiological relevance of the extreme acidification paradigm. Addressing these points will substantially improve reproducibility and mechanistic depth.

Overall, this is a scientifically important and technically sophisticated study that advances our understanding of CSF sensing, provided that the analytical and interpretative weaknesses are satisfactorily corrected.

(1) The authors should re-analyze electrophysiological data, focusing on macroscopic currents rather than statistically unreliable Po calculations. Remove or revise the Po analysis, which currently conflates current amplitude and open probability.

We agree with the reviewer that the Po analysis has strong limitations, particularly in experiments where the recording times are short, like when extracellular pH is changed either by photolysis (Figure 4D) or puff applications (Figure 3Aa). In order to circumvent that problem and not to rely only on Po estimations, we used alternative methods as well, including the analysis of the current membrane charge that we have used extensively during the manuscript (Figures 3A and 4D, for example) or the analysis of the event latencies (Figure 4G). Nevertheless, single-channel recordings clearly contain information that is not included in the macroscopic current analysis. We intend to stress in the revised version that the elementary current amplitude is conserved by manipulations such as pH changes, leaving the total number of channels (N) and the channel open probability (Po) as possible culprits for the current changes. Since these changes are rapid and reversible, it is likely that N stays constant and that Po changes. In order to address the reviewer’s concern, we propose the following changes/reanalysis: i) to report in each condition the minimum N (maximum observed openings; for example, in Figure 3Aa the minimum N goes from 4 in control conditions to 1 during the puff of the pH 6.4 solution). This method (to estimate N by counting the maximum number of open channels), while imperfect, provides a tentative estimate of Po; ii) following the previous point, we propose to reword the text (and images) and use the expression “apparent Po” instead of “Po”; iii) to report the fraction of time that the channels remain open. Also, we acknowledge that some traces are confusing (Figure 3Aa, top) as they seem to show macroscopic currents. We will modify those figures by plotting the amplitude histograms (as in Figure 1Bb) in order to show unambiguously that current recordings from CSFcNs only show single-channel activities.

(2) PKD2L1-TRPP3 nomenclature should be clarified and all figure labels, legends, and text should use consistent terminology throughout.

We agree with the reviewer that the nomenclature concerning polycystin members is confusing. In this manuscript we have followed the nomenclature that has been proposed in a recent, comprehensive review on polycystin channels by Palomero, Larmore and DeCaen (Palomero et al. 2023), where the authors refer to the channels by their gene name. In this review, the authors indicate that PKD2L1 channels correspond to TRPP2 (formerly TRPP3, their table 1). In another, recent review on TRP channels, however, the authors refer to the PKD2L1 channel as TRPP3 (Zhang et al. 2023). In order to avoid any confusion we will remove from the text any reference to the TRPP nomenclature and stick to the PKD2L1 name.

(3) The authors should reinterpret the so-called OFF currents as pH-dependent recovery or relaxation phenomena, not as distinct current species. Remove the term "OFF response" from the manuscript.

We concur with the reviewer that the term “OFF response” is not very helpful from the biophysical perspective and conveys the idea that it is another current. We will remove the term “OFF response” or “OFF current” in the revised manuscript and replace it by the term “photolysis-evoked PKD2L1 current”. Also, we will condense two sections (“The proton-induced current is an off-current” and “The off-current is mediated by the activation of PKD2L1 channels”) into a single new section (“The photolysis-induced current is mediated by PKD2L1 channels”), as separating the description of the photolysis-evoked PKD2L1 current compromises its description. Finally, we will rewrite the discussion to better describe this current.

(4) Evidence for physiological relevance should be provided, including data from milder acidification (pH 6.5-6.8) and, where appropriate, comparisons with ASIC-mediated currents to place PKD2L1 activity in context.

This is partly addressed in Figure 3. The data there indicates that PKD2L1 channels are very sensitive to pH variations around physiological pH. In order to make this conclusion stronger, we will add to the figure the EC50 values drawn from the fittings. In terms of the ASIC-mediated currents, one of our main conclusions is that ASIC channels are not present in the ApPr, as the effects of proton photolysis in the ApPr and are not blocked by ASIC channels blockers. Our results indicate that PKD2L1 channels are the exclusive pH sensitive channels in the ApPr, while ASIC channels are probably the acid-sensitive channels in the soma, although we have not studied the latter in detail. Following this and the editor’s comments, the subsection “the involvement of ASICs” in the Discussion has been modified.

(5) Terminology and data presentation should be unified, adopting consistent use of "predominant" (instead of "exclusive") and "sustained" (instead of "tonic"), and all statistical formats and units should be standardized.

Following the suggestions of the reviewer, an exhaustive work will be performed to unify terminology, data presentation and correct the text following the reviewer’s suggestions.

(6) The Discussion should be expanded to address potential Ca²⁺ -dependent signaling mechanisms downstream of PKD2L1 activation and their possible roles in CSF flow regulation and central chemoreception.

This is indeed a very interesting and currently unresolved point in the physiology of CSFcNs. Published data indicate that calcium flowing into the cell through PKD2L1 channels is a key regulator of apical process physiology: on the one hand, PKD2L1 channels are calcium permeable and at the same time, they are inhibited by intracellular calcium (DeCaen et al. 2016). Also, ultrastructural data indicate that the ApPr is rich in mitochondria and tubulo-vesicular structures resembling the Golgi apparatus (Bjugn et al. 1988; Bruni et Reddy 1987), which are intracellular organelles that contribute to calcium homeostasis. Altogether, this evidence suggests that intraApPr calcium concentration needs to be finely regulated, both in space and in time, in order for the ApPr to fulfil its physiological roles. Based on what has been published in the literature, we can speculate that these calcium signals can be decoded by several systems: i) calcium can act as the second messenger linking the activation of the multimodal PKD2L1 channels to changes in CSFcNs excitability, which in turn regulate spinal neuronal networks controlling locomotor activity; ii) calcium could initiate neurosecretion of different molecules from the ApPr to the central canal (as has been proposed by the Wyart group in the zebrafish in the context of bacterial infections(Prendergast et al. 2023)); iii) calcium could activate the Hedgehog signaling pathways (as has been shown by (Delling et al. 2013)); iv) calcium could modulate CSF flow directly (by modulating ciliary activity) or indirectly (by modulating ependymal cells ciliary activity through paracrine interactions). Resolving these downstream pathways is essential to fully define the role of CSFcNs as integrators of CSF homeostasis. We will expand this issue in the Discussion of the revised ms.

Reviewer #2 (Public review):

Summary:

Cerebrospinal fluid contacting neurons (CSF-cNs) are GABAergic cells surrounding the spinal cord central canal (CC). In mammals, their soma lies sub-ependymally, with a dendritic-like apical extension (AP) terminating as a bulb inside the CC.

How this anatomy-soma and AP in distinct extracellular environments relate to their multimodal CSF-sensing function remains unclear.

The authors confirm that in GATA3:GFP mice, where these cells are labeled, that CSFcNs exhibit prominent spontaneous electrical activity mediated by PKD2L1 (TRPP2) channels, non-selective cation channels with ~200 pS conductance modulated by protons and mechanical forces.

They investigated PKD2L1 pH sensitivity and its effects on CSFcN excitability. They uncovered that PKD2L1 generates both phasic and tonic currents, bidirectionally modulated by pH with high sensitivity near physiological values.

Combining electrophysiology (intact and isolated AP recordings) with elegant laser-photolysis, they show that functional PKD2L1 channels localize specifically to the apical extension (AP).

This spatial segregation, coupled with PKD2L1's biophysical properties (high conductance, pH sensitivity) and the AP's unique features (very high input resistance), renders CSFcN excitability highly sensitive to PKD2L1 modulation. Their findings reveal how the AP's properties are optimised for its sensory role.

Strengths:

This is a very convincing demonstration using elegant and challenging approaches (uncaging, outside out patch of the AP) together to form a complete understanding of how these sensory cells can detect the changes of pH in the CSF so finely.

Weaknesses:

The following do not constitute weaknesses; rather, they are minor requests that this reviewer considers would complete this beautiful study.

(1) It would be nice to quantify further the relation in spontaneous as well as in acidic or basic pH between the effects observed on channel opening and holding current: do they always vary together and in a linear way?

Following the reviewer’s suggestion, we have performed a Spearman’s rank correlation test, which shows a significant correlation between the changes in the apparent open probability and holding current (paired experiments; ctrl vs pH 6.4 pressure applications; p < 0.05, Spearman r = 0.72 and critical value = 0.67). The Pearson correlation coefficient calculated on the same data set = 0.63 and the critical value is 0.632, which indicates that the correlation is not linear. We will add this analysis to the manuscript.

(2) Since CSF-cNs also respond to changes in osmolarity (Orts Dell Immagine 2013) & mechanosensory stimulations in a PKD2L1 dependent manner (Sternberg NC 2018), it would be nice to test the same results whether the same results hold true on the role of PKD2L1 in AP for pressure application of changes in osmolarity.

This is a very important point. As the reviewer mentions, previously published experimental evidence indicates that CSFcNs are also sensitive to osmolarity changes and mechanical stimulation in a PKD2L1-dependent manner. It is therefore reasonable to assume that, as for the pH sensitivity, osmotic and mechanical sensitivity depends on channels segregated to the ApPr. For the mechanosensitivity, the spatial segregation could be tested by “touching” either the ApPr or the soma with a piezo-controlled blunted pipette (see, for example, Hao et al. 2013). However, the sensitivity to osmotic changes is much more difficult to assess, as pressure application does not have enough spatial resolution to discriminate among compartments in such a compact cell such as the CSFcNs. In theory, a highly spatially localized osmotic jump could be reached with photolysis, but a caged compound releasing many osmotic particles simultaneously should be used. In typical photolysis experiments, a localized osmotic jump is produced, but it is very low (in the order of 1 to 2 mOsm).

In mice, like in fish (Sternberg et al, NC 2018), we can observe throughout the figures that a large fraction of the channel activity occurs with partial and very fast openings of the PKD2L1 channel. I recommend the authors analyse the points below:

(a) To what extent do these partial openings of the channel contribute to the changes in holding current and resting potential?

As the reviewer indicates, these partial and very fast openings are a characteristic of PKD2L1 single-channel activity that seems to be present in different species. However, estimating what is the exact contribution of these events to the sustained current would require a detailed model of the channel that it is still lacking. Indeed, the exact mechanism by which CSFcNs show this prominent sustained current is unknown and should definitely being addressed in future works.

(b) In the trace from the outside out AP, it looks like the partial transient openings are gone. Can the authors verify whether these partial openings are only present in somatic recordings?

The outside-out recordings from the ApPr also show some partial openings (please look at the upper trace in Figure 4Db). We will specifically mention this important point in the revised version of the ms.

(3) Previous studies have observed expression of metabotropic Glutamate receptors in CSF-cNs (transcriptome from Prendergast et al CB 2023). The authors only used blockers for ionotropic glutamate receptors in their recordings: could it be that these metabotropic receptors influence the response to uncaging of MNI-Glu when glutamate is co-released with a proton?

We thank the reviewer for pointing out the presence of metabotropic glutamate receptors in CSFcNs. However, our evidence indicates that there is no contribution of metabotropic receptors when uncaging MNIglutamate because: i) the response obtained when uncaging MNI-gLGG (where there is no glutamate release; Figure 5Ab) and ii) the response obtained when uncaging protons from DPNIGABA (a GABA cage that has similar photochemistry than MNI cages which also release a proton when photolysed; data not shown), are the same. Indeed, in both experiments (MNI-gLGG or DPNI-GABA uncaging) a clear photolysis-evoked PKD2L1 current can be observed.

(4) In the outside out patch of the AP, PKD2L1 unitary currents appear rare. Could it be that the disruption in the cilium or underlying actin/myosin cytoskeleton drastically alter the open probability of the channel?

Although we have not quantified it, the reviewer is right that the opening frequency of PKD2L1 channels in the outside-out patches is lower than in the whole-ApPr recordings. We interpreted this difference as a difference in channel number. However, another plausible interpretation is that, as the reviewer suggests, the biophysics of the channels are affected because the protein is taken out from its normal ionic environment and/or loses important interactions with regulatory proteins.

(5) Could the authors use drugs against ASIC to specify which ASIC channels contribute to the pH response in the soma?

As described in the manuscript, we did perform experiments with ASIC channel blockers, although we did not attempt to characterize the specific ASIC channel involved in the somatic response. Based on what has been published in the literature, we used both psalmotoxin-1 (which blocks ASIC1 channels) and APETx2 (which blocks ASIC3 channels). The presence of ASIC1 channels in mice CSFcNs has been shown by (Orts-Del’Immagine et al. 2012; Orts-Del’Immagine et al. 2016), while the presence of ASIC3 in the lamprey CSFcNs has been shown by (Jalalvand et al. 2016). When we puff an acidic solution aiming at the soma, we can record an inward current that is blocked by psalmotoxin-1, although there is always a small component remaining (as originally shown by Orts-Del’Immagine in the aforementioned articles); however, we have not attempted to block this small component that remains after psalmotoxin-1 bath application.

(6) This is out of the scope of this study, but we did observe in fish a very rarely-opening channel in the PKD2L1KO mutant. I wonder if the authors have similar observations in the conditions where PKD2L1 is mainly in the closed state.

We have never seen such kind of openings in our recordings (when the channel is closed or in the presence of dibucaine).

Bjugn, R, H K Haugland, et P R Flood. 1988. “Ultrastructure of the mouse spinal cord ependyma.” Journal of Anatomy 160 (octobre): 117‑25.

Bruni, J. E., et K. Reddy. 1987. “Ependyma of the Central Canal of the Rat Spinal Cord: A Light and Transmission Electron Microscopic Study”. Journal of Anatomy 152 (juin): 55‑70.

DeCaen, Paul G., Xiaowen Liu, Sunday Abiria, et David E. Clapham. 2016. “Atypical Calcium Regulation of the PKD2-L1 Polycystin Ion Channel”. eLife 5 (juin): e13413. https://doi.org/10.7554/eLife.13413.

Delling, Markus, Paul G. DeCaen, Julia F. Doerner, Sebastien Febvay, et David E. Clapham. 2013. “Primary cilia are specialized calcium signalling organelles”. Nature 504 (7479): 311‑14. https://doi.org/10.1038/nature12833.

Hao, Jizhe, Jérôme Ruel, Bertrand Coste, Yann Roudaut, Marcel Crest, et Patrick Delmas. 2013. “Piezo-Electrically Driven Mechanical Stimulation of Sensory Neurons”. In Ion Channels, édité par Nikita Gamper, vol. 998. Methods in Molecular Biology. Humana Press. https://doi.org/10.1007/978-1-62703-351-0_12.

Jalalvand, Elham, Brita Robertson, Peter Wallén, et Sten Grillner. 2016. “Ciliated Neurons Lining the Central Canal Sense Both Fluid Movement and pH through ASIC3”. Nature Communications 7 (janvier): 10002. https://doi.org/10.1038/ncomms10002.

Orts-Del’Immagine, Adeline, Riad Seddik, Fabien Tell, et al. 2016. “A Single Polycystic Kidney Disease 2-like 1 Channel Opening Acts as a Spike Generator in Cerebrospinal Fluid Contacting Neurons of Adult Mouse Brainstem”. Neuropharmacology 101 (février): 549‑65. https://doi.org/10.1016/j.neuropharm.2015.07.030.

Orts-Del’immagine, Adeline, Nicolas Wanaverbecq, Catherine Tardivel, Vanessa Tillement, Michel Dallaporta, et Jérôme Trouslard. 2012. “Properties of Subependymal Cerebrospinal Fluid Contacting Neurones in the Dorsal Vagal Complex of the Mouse Brainstem”. The Journal of Physiology 590 (16): 3719‑41. https://doi.org/10.1113/jphysiol.2012.227959.

Palomero, Orhi Esarte, Megan Larmore, et Paul G. DeCaen. 2023. “Polycystin Channel Complexes”. Annual Review of Physiology 85 (Volume 85, 2023): 425‑48. https://doi.org/10.1146/annurev-physiol-031522-084334.

Prendergast, Andrew E., Kin Ki Jim, Hugo Marnas, et al. 2023. “CSF-Contacting Neurons Respond to Streptococcus Pneumoniae and Promote Host Survival during Central Nervous System Infection”. Current Biology 33 (5): 940-956.e10. https://doi.org/10.1016/j.cub.2023.01.039.

Zhang, Miao, Yueming Ma, Xianglu Ye, Ning Zhang, Lei Pan, et Bing Wang. 2023. “TRP (Transient Receptor Potential) Ion Channel Family: Structures, Biological Functions and Therapeutic Interventions for Diseases”. Signal Transduction and Targeted Therapy 8 (1): 261. https://doi.org/10.1038/s41392-023-01464-x.

Recommendations for the authors:

Reviewing Editor Comments:

Both reviewers were very impressed with your work and definitely feel it is a scientifically important and technically sophisticated study that advances our understanding of CSF sensing. They, however, request some re-analysis of the data and discussion with minimum new experiments, if any. I think, if feasible, this will improve the quality of the study and would look forward to receiving a revised version.

Reviewer #1 (Recommendations for the authors):

(1) Figure 1 - Molecular identity and localization of PKD2L1

Major

Nomenclature clarity.

Please clarify the distinction between PKD2L1 and TRPP3. Several parts of the text and figure labels appear to conflate these names. PKD2L1 corresponds to the TRPP3 subfamily member and should not be interchanged with PKD2/TRPP2. Please confirm and update the nomenclature consistently throughout the manuscript (text, figure labels, and captions).

We have addressed this issue in response to reviewer 1. There seems to be some confusion in the literature concerning the nomenclature of PKD2L1 channels as in some recent publications the PKD2L1 channels are still named as TRPP3. However, the nomenclature of PKD2L1 channels or TRPP2, was updated in 2016 (Wu, Sweet and Clapham, Pharmacological Reviews, 2010). As indicated in response to reviewer 1, we have removed from the text any reference to the TRPP nomenclature and stuck to the PKD2L1 name.

Physiological meaning of apical restriction.

Expand the discussion of why apical-restricted localization matters. Specifically, address how segregation to the ApPr could support directional sensing of CSF flow and/or detection of localized pH gradients.

Following the reviewers and editor’s comments, we have revised the discussion in order to take this and other comments into account.

Open-state annotation (O3).

Please include the O3 state in panels Ba and Bb; the figure clearly shows an additional open level consistent with O3.

The editor is right in that there is another state that presumably corresponds to O3. Following the editor’s recommendation, we now indicate this 3rd level and add a short sentence explaining this in figure 1 legend.

Minor

Indicate the ROI definition and background-subtraction method used for fluorescence quantification (ApPr vs soma).

Not applicable for this figure.

Ensure the same intensity scale (lookup table and range) is used across panels to enable direct comparison.

Done.

(2) Figure 2 - Electrophysiological characterization of ApPr and somatic recordings Major

Definition of "PKD2L1-dependent current."

Define this term precisely at its first appearance. Specify whether it denotes currents inhibited by dibucaine, abolished in PKD2L1-knockout preparations, or both.

Done

Statistical power of single-channel analysis.

The number of observed openings (< 1000 events) is too low to estimate open probability (Po) reliably. Please re-analyze the data using macroscopic current traces rather than Po-based kinetics.

Confounded Po analysis.

The current Po analysis mixes current amplitude and Po in the same calculation, conflating independent variables. Re-evaluate or remove this analysis.

Unknown channel count.

Because the number of channels in each patch is unknown, Po and "closed probability" values cannot be interpreted meaningfully. Focus instead on the averaged macroscopic current density.

General analytical validity.

The single-channel analyses in Figure 2 are not interpretable under these experimental conditions. Closed-time distributions and Po-based metrics (e.g., "Po1," "P2") depend critically on channel number and event sampling. Moreover, the manuscript applies essentially the same Po methodology across conditions (Po1 vs P2), which adds no mechanistic resolution and risks circular interpretation.

Actionable recommendation:

Remove Po- and closed-time-based analyses from Figure 2 and from the manuscript as a whole. Reanalyze the data using metrics that remain valid when the channel number is unknown:

Macroscopic current analysis (leak-subtracted current density, I-V relationships, activation time constants).

Single-channel conductance only (amplitude histograms and unitary slope conductance), without attempting Po or dwell-time inference.

Report filtering bandwidth and sampling rate, and restrict statistical treatment to these robust parameters.

Following the reviewers (see above) and editors’ recommendations, we have reanalyzed the data in order to avoid the analysis based on Po and Pc. We have instead calculated from the recordings other 2 parameters, n_max (the maximum number of channels that open simultaneously during a 500 ms time window) and the total open time of a single channel during the same 500 ms time window. The main text, figures and corresponding figure legends, and the Materials and Methods section have been changed accordingly. Notably, the Po and Pc analysis were removed from Figures 3, 4 and Supplementary Figure 3, and replaced by the above-mentioned parameters. Also, the fact that the recordings are not long enough to calculate Po is now specifically mentioned in the Materials and Methods section, lines 785 to 790. In addition, the analysis in Figure 3Ce has been redone so that the activity of the channel as a function of pH is now plotted as the normalized apparent Po (relative to the apparent Po value at pH 7.4).

Minor

State whether input-resistance values (1.8-4.4 GΩ) were leak-subtracted and series-resistance-compensated.

As already mentioned in the methodology section (line 693), series resistance was not compensated for during the experiments. We have now added a sentence in the methodology section indicating that in the voltage range that was chosen for the analysis of the input resistance, no voltage-dependent conductance was activated (lines 809 to 812).

Ensure unit consistency: use Po or normalized Po rather than frequency (Hz) throughout.

(3) Figure 3 - pH-evoked currents and kinetics

Major

Invalid Po analysis (Fig. 3Ca-Ce).

The Po- and Pc-based single-channel analyses in panels 3Ca-3Ce should be deleted. As noted earlier, the event count is insufficient, and the number of active channels in each patch is unknown. Under these conditions, Po and Pc values have no quantitative meaning and could mislead readers. These panels do not contribute additional mechanistic insight beyond the macroscopic current data and therefore, should be removed. If retained for illustrative purposes, they must be explicitly labeled as representative traces without any statistical quantification.

As we mentioned above, we removed the Po and Pc analysis from the manuscript.

Minor

Present regression equations and r² values for the linear fits shown in Fig. 3D.

Done (lines 947951).

Confirm that all axes include units and identical scaling between conditions for direct comparison.

Done.

(4) Figure 4 - Laser photolysis and local stimulation experiments

Major

Laser timing annotation.

Clearly mark laser-pulse timing (e.g., arrow or shaded region) on all current traces to facilitate interpretation.

We thank the editor for pointing out the inconsistencies in terms of the laser pulse timing. To indicate the laser pulses, we have now added an arrowhead in cases where a single sweep is shown (for example, Figure 3D), and an arrowhead and a dotted magenta vertical line in cases where multiple sweeps are shown (for example, Figure 3C).

pH calibration within the laser spot.

Provide quantitative calibration of pH changes induced by laser photolysis, including information on spot size, local diffusion, and estimated pH recovery kinetics.

This is an important point and we thank the editor for mentioning it. We have now completed the subsection untitled “photolysis” where we provide information on the lateral and axial dimensions of the photolysis laser spot used in this work (lines 734 to 737). We have also rewritten part of Figure 5A legend to highlight the fact that the experiments presented there (photolysis on top of the ApPr and next to it) are compatible with a high spatial resolution of proton release (lines 1023 to 1026).

On the other hand, we have attempted to perform pH calibrations in the setup using the pH-sensitive dye pyranine (or HPTS: 8-Hydroxypyrene-1,3,6-trisulfonic acid). HPTS is a very useful tool for pH calibrations in the physiological range: its pKa value is close to 7.2, and it can be used as a ratiometric dye (its fluorescence is pH-independent at 405–410 nm and pH-dependent at 450 nm). Unfortunately, when trying to perform a calibration under the conditions of a real experiment,

where photolysis occurs in a tiny volume (approximately 1 µm³ in a total bath volume of more than 1 ml), we encountered the following problem, which made it impossible to obtain any useful data: the 405 nm uncaging pulse bleaches the dye, and any useful information is lost. Also, our imaging system is not fast enough to follow the pH change. As it is discussed in the Materials and Methods section, subsection “Estimation of the pH drop induced by photolysis” (line 814), the fast protonation of bicarbonate indicates that the pH change induced by the photolysis recovers in the submillisecond time range.

Repeated stimulation effects.

Discuss whether repeated photolysis induces adaptation or desensitization of PKD2L1 currents, and indicate whether current amplitude decreases across successive trials.

This issue is now specifically mentioned in the Materials and Methods section, lines 739 to 741.

Invalid interpretation of the "OFF response."

The interpretation of the so-called "OFF response" in Figure 4C is not supported by the presented data. There is no evidence for a bona fide OFF current, and the literature cited does not demonstrate such a phenomenon for PKD2L1 alone. Rather, previous studies implicate PKD1L3-dependent mechanisms in similar biphasic responses. Please reconsider the cited references and remove claims of an OFF current attributed to PKD2L1.

Done.

Actionable recommendations:

Do not use the term "OFF response" throughout the manuscript. Recast these transients as pH dependent recovery or relaxation of current following cessation of acidification.

Done. We have performed extensive rewriting and reorganization of the Results and Discussion in order to take into account both the reviewer’s and editor’s comments. Please also take a look at comment #3 of Reviewer 1 and point 11 below.

Include continuous-illumination controls (sustained local acidification) to test whether a steady state current is maintained. This will clarify whether the post-stimulus transient reflects recovery kinetics rather than a distinct current species.

We thank the editor for suggesting this experiment. However, continuous laser illumination is a difficult manipulation and does not necessarily lead to an acidification of the illuminated volume. Indeed, with continuous illumination the cage is lost from the illumination spot and needs to be replaced by diffusion from the non-illuminated volume, leading to non-homogeneous concentrations. Also, the chances of inducing photo damage are higher. We thus designed a similar experiment where instead of performing continuous illumination we photolysed with short and high frequency trains in order to produce a long-lasting acidification. The results of these experiments have been added to the manuscript as part of the results section and in Figure 5H. Similarly to what is seen with single illuminations, the photolysis trains induce a current that appears almost exclusively at the end of the train, implying that the current is indeed a PKD2L1-dependent recovery current.

Align the current time course with measured or estimated local pH (or calibrated proxy) to demonstrate causal coupling and avoid implying a separate conductance.

We have added the calculated pH change to the inset of Figure 4C as an example.

Revise the schematic/model figure and textual description accordingly, restricting the framework to phasic vs sustained activation modes without invoking a separate OFF current for PKD2L1.

Done.

Minor

Include scale bars, sample numbers (n), and laser parameters (duration, power) in all panels.

In order not to make the figure and the panels very heavy in the original version, we tried to limit the number of scale bars. We have now performed some modifications, added the missing scale bars, and changed the figure legend in order to take into account the editor’s comments. We have also corrected a few values that were wrongly reported.

Standardize p-value formatting (e.g., p = 6 × 10 ⁶) throughout the figure and legend.

Done.

(5) Figure 5 - Single-channel recordings

Major

Mixed parameters (current amplitude and Po).

The current analysis improperly mixes single-channel current amplitude and Po within the same figure, conflating distinct parameters. These quantities must be analyzed and presented separately, or the Po data should be removed entirely if not independently supported.

Insufficient event count.

Given the very limited number of observed openings, Po-based statistics are not meaningful. Please report only representative single-channel traces and corresponding amplitude histograms without attempting quantitative Po estimation.

Minor

Convert frequency (Hz) values to Po for consistency with earlier analyses, or remove frequency metrics altogether if Po analysis is omitted.

Figure 5 does not include Po or event frequency analysis, so we think there must be a misquotation of the figure. However, the Po issue has already been addressed before and alternative analysis have been proposed.

(6) Introduction

The introductory paragraph mentions the "five senses" as a framing concept. However, this statement lacks scientific grounding in the context of CSF-contacting neurons and chemosensory physiology. The traditional "five senses" classification is not an evidence-based neurophysiological framework and may be misleading to readers. I recommend removing or rephrasing this part, focusing instead on molecular and cellular mechanisms of sensory transduction (e.g., chemical, mechanical, and pH sensing) rather than on classical sensory categories.

Following the editor’s recommendation, we have removed this part.

The manuscript refers to PKD2L1 using the term TRPP2 in some parts of the introduction. This is incorrect, as PKD2L1 corresponds to TRPP3, not TRPP2. Please correct this nomenclature and ensure consistent use of "PKD2L1 (TRPP3)" throughout the entire manuscript to avoid confusion with the distinct PKD2/TRPP2 protein, which belongs to a different subfamily with separate physiological roles.

We thank the editor for pointing this out. As we mentioned in the responses to the “public reviews”, the literature is confusing, so we decided to remove from the manuscript any mention to TRPP channels.

(7) Discussion

The current Discussion reads largely as a descriptive summary of results and lacks conceptual depth. It does not effectively integrate the biophysical properties of PKD2L1 with its physiological role as a neuronal pH sensor, nor does it develop a broader interpretation relevant to CSF homeostasis or chemoreception.

Following the reviewers and editor’s recommendations, we have now added a new section in the Discussion untitled “PKD2L1 downstream signaling mechanisms”.

(8) Insufficient biophysical analysis

The discussion of channel gating and pH dependence is superficial and does not explore the energetic or structural mechanisms underlying proton sensitivity. The authors should analyze their data in the context of known PKD/TRPP family biophysics-for example, protonation sites, subunit composition, or gating kinetics-and explain how these confer bidirectional (acidic vs alkaline) sensitivity within physiological ranges.

In this work, we studied the pH sensitivity of PKD2L1 channels in the context of CSFcN sensory physiology. From a pure biophysical perspective, the pH sensitivity of PKD2L1 channels has been studied by multiple groups; however, it is still unknown how the gating of the channel responds to pH changes, although it can be proposed that some polar residues in the protein regulate the state of the pore. Likewise, the mechanism of the “off-response” is also unknown. To the best of our knowledge, there is only one article in which the authors have attempted to relate pH, PKD2L1 channel structure, and function. In this work (Su et al., Nature Communications 2018), the authors compare PKD2L1 channels with another pH-sensitive member of the TRP family, TRPML3, whose structures at pH 7.4 and 4.8 are known (Zhou et al., Nature Structural and Molecular Biology, 2017). We have rewritten some sentences of the Discussion in order to be more specific about the pH dependence of PKD2L1 channels and its proposed mechanisms.

(9) Weak physiological context

The manuscript does not adequately address how PKD2L1 functions as a true physiological pH sensor. The discussion should connect channel activity to realistic CSF pH fluctuations (6.8-7.6) and to relevant physiological or pathophysiological conditions (e.g., respiratory acidosis, neurogenic regulation of CSF composition). Without this, the relevance of large, artificial acidification (pH 3-3.5) remains unclear.

We have added a new section in the Discussion where we speculate on how PKD2L1 channels may be activated in physiological and pathophysiological conditions. However, we would like to insist here that the main goal of the photolysis experiments (which induce short and large acidifications) was to assess the spatial segregation of PKD2L1 channels. We now mention this point specifically and also speculate on the conditions that could eventually give rise to the “recovery” current.

(10) Over-interpretation of unsupported points

The paragraph describing voltage propagation from the ApPr to the soma/axon is speculative and unsupported by any data in the manuscript. Please delete this section entirely, including the citation to Orts-Del'immagine et al., unless new electrophysiological evidence is added.

We think this point (the propagation of signals originating from the ApPr to the soma) is important in the context of our work, so we have decided to make new experiments in order measure directly the degree of coupling between the 2 compartments. To do that we made simultaneous, current-clamp and voltage-clamp recordings from the ApPr and the soma. In these conditions we were able to measure experimentally and for the first time both the coupling coefficient and coupling conductance, which confirm that the propagation of voltage signals from the ApPr to the soma is extremely efficient. These new results are now described in a new subsection and in a new Figure 6.

(11) Clarify the role of "OFF currents."

The Discussion repeatedly refers to an "OFF response," but this phenomenon is not experimentally demonstrated for PKD2L1 alone. It likely represents pH-dependent recovery rather than an independent current. All discussion of "OFF currents" should be removed or reformulated accordingly.

Following the editor and reviewer’s comments, we have deleted the term “off response” and “off currents” from the ms and have replaced them with the term “recovery current”. We have also changed the discussion accordingly.

(12) Integration with ASICs and compartmental sensing

While the manuscript briefly mentions ASIC involvement, it does not articulate how PKD2L1- and ASIC-mediated signals might complement each other in different compartments (ApPr vs soma). The authors should discuss the potential division of labor between these sensors and how such compartmentalization enhances pH detection in CSFcNs.

Following the editor’s comments, we have rewritten the part of the subsection ‘the involvement of ASICs’ in the Discussion.

(12) Broadened physiological perspective

The Discussion should close by considering Ca²⁺ -dependent downstream pathways activated by ⁺ PKD2L1 and their implications for CSF flow regulation, neurosecretion, and central chemoreception. These translational aspects would substantially improve the impact and readability of the manuscript.

Done

Overall, the Discussion must evolve from a descriptive narrative to a mechanistically and physiologically integrative synthesis, highlighting why PKD2L1 is not merely present in the ApPr but is a key molecular transducer linking ionic microenvironment to neuronal excitability.

As it has been detailed above, we have performed several changes in the Discussion that follow the reviewer’s and editor’s recommendations.

This comment sticks out to me a lot because I feel like a large amount of people like to think of the internet as the first time that humans had contact in such a broad way, and it is very interesting to see that that may not be as true as we have all assumed. Humans seem to be more interconnected than we believed originally, and lots of ideas come from interacting with one another.

Multiple problems are presented here. The first and more obvious being the fact that women were overlooked and given little opportunity to speak at the meeting. I find this especially frustrating as often women are the most victimized and targeted during times of war. Acts of rape and violence from both foreign imperialist/colonizers and countrymen are not uncommon. While western women may not be the best representatives to voice such concerns, I do think acknowledging the realities of the patriarchy are vital in such discussions. The secondary problem and slightly more egregious in regards to the goal of such a meeting is the unwillingness to teach and educate, and have no clear structure. Such groups do not have the luxury of not educating, having no structure, and letting few speak. To speak to a large meeting, with no baseline of where the majority of the individuals are in regards to understanding such rhetoric and theory is foolish and egotistical.

this is a pretty interesting topic to me because to be fully honest, none of us truly know who we are. You might have a really strong understanding of your personal beliefs, the things you like and dislike, maybe strong self awareness of how you act, but at the very root of it all, it’s hard to define exactly who we are. Subsequently, it’s even harder for another person to define who they think you are. Even if you do have strong self awareness, if somehow you could play a recording of the internal thoughts of everyone you’ve ever talked to in relation to what they thought about you, you’d probably be really surprised by what you heard. That’s simply because of the fact that no one’s ideologies are identical and no one has lived exactly the same life, and everyone’s opinions are going to change based on the life they’ve lived. So when you internalized something that someone else thought about you, that thought could’ve been polar opposite to what someone else thought about you, and therefore we are left in an infinite paradox of what is true about ourselves and who exactly we are.

Introduction

The above screenshot (figure 1) was what was generated when we asked ChatGPT, the generative AI system that has been the subject of a thousand hot takes about how it’s disrupting academia-as-we-know-it, to describe itself for an academic librarian audience. Perhaps it’s learning a bit too much from the public relations documents that were a part of the vast amounts of data it was trained on, when it describes itself as “highly relevant,” “invaluable,” and “accurate.” It did not, however, bring up the caveat that greets you when you open up ChatGPT itself: that it “may occasionally generate incorrect information,” that it “may occasionally produce harmful instructions or biased content,” or that it has “limited knowledge of the world and events after 2021.”1 In addition, it doesn’t bring up the reddest of academic red flags—that ChatGPT provides an easy way for students to cheat and plagiarize. The Atlantic has claimed that because of ChatGPT and other AI, “the undergraduate essay [which] has been at the center of humanistic pedagogy for generations

. . . is about to be disrupted from the ground up.”2 A writer at Times Higher Education has suggested that allowing AI to replace a student’s creative voice means “abandoning our responsibilities as educators.”3 For as many handwringing accounts of how generative AI will destroy academia, there seem to be twice as many researchers, teachers, technologists, and pundits embracing what AI (and specifically ChatGPT) can do for teaching and learning. They suggest using it for overcoming writer’s block, generating outlines, creating summaries, generating prompts for discussion, asking for definitions, or generating flawed examples for critique.4 One compelling argument by Christopher Grobe in the Chronicle of Higher Education suggests that what generative AI can help us with is to “provide new starting points for some of the processes we routinely use to think.”5 We agree with Grobe’s argument that ChatGPT can give us a good starting point from which to work. The text generated by ChatGPT in the screenshot at the start of this article is an overly optimistic and idealized view of itself. We hope that in this article we can add the nuance that it lacks. Academic librarians serve their students and faculty to help them navigate the research process. Therefore, when a new technological tool blazes through higher education, as ChatGPT has over the last few months, it becomes increasingly important that librarians are aware of the tool and its uses so that they can serve their students and faculty. After decades of the ACRL Information Literacy Competency Standards for Higher Education, the ACRL Framework for Information Literacy for Higher Education was established with a much more flexible route for integration into curricula. The Framework provides librarians and disciplinary faculty with a customizable way to provide information literacy instruction that meets the needs of students and enables them to become participants in the information that they are producing (not just consuming). Because of the Framework’s flexible nature, librarians can incorporate new technology, like ChatGPT, more easily into their instruction. We have found that the idea of ChatGPT (and generative AI more broadly) can be connected to many of the knowledge practices and dispositions from the six frames of the ACRL Framework. In some places, the Framework enables us to embrace ChatGPT as an exciting new tool that adds value to information literacy instruction. In other places, the Framework’s discussions of evaluating authority and examining bias shines light on the inherent flaws of ChatGPT. In the next section, we will review each of the frames and discuss how ChatGPT fits into each of those Frames.

Research as Inquiry

One of the knowledge practices for the Research as Inquiry frame states that “learners who are developing their information literate abilities deal with complex research by breaking complex questions into simple ones, limiting the scope of investigations.”11 We have found that students will often come to research consultations or library instruction sessions with broad or vague research questions that they often do not know how to simplify or narrow down to research writing sufficiently scoped to a level that they can tackle in five to eight pages. While they might be interested in, let’s say, “the problem of poverty” or “the abortion debate,” they cannot digest the enormous amount of research in multiple academic

disciplines that have attempted to address these types of questions. This is where we believe ChatGPT can help students (and even seasoned researchers) in generating ways to break complex problems down. ChatGPT can help refine research questions, determine search terms, come up with synonyms and related terms or phrases for searching, help decide which databases to search, generate textual concept maps, and even help generate citations. For example, here was the response it gave when we asked it “What search terms should we use for our hypothetical research question, ‘why aren’t college athletes paid?’”

ChatGPT can also create textual concept maps to help think through various aspects of a research topic. This can be useful for students who need to narrow or refine their topic. Simply asking the AI to help narrow a research topic can be useful as it will give you a variety of ways to explore a topic. For example, we asked it to help us narrow our search on why college athletes aren’t paid, and it gave us detailed options in an easy-to-read format:

You can see clearly how ChatGPT can help students push past that inquiry threshold. Often, they don’t even know where to start in their search for information, or how to probe the nuances or facets of a large complex question for a scope they can grasp. Instead of typing their entire research question into Google or a database (as we have all seen students do) and having to sift through a mountain of results, they can type it into ChatGPT and ask “How do I start searching? Where could I go from here? What’s manageable?” As students are growing in their information literacy abilities, ChatGPT can help scaffold their skills enabling them to accomplish this task more confidently in the future. One caveat that always bears repeating: ChatGPT has biases. It is trained on a large dataset of material from the internet. It may not produce underrepresented or less well-researched aspects of a topic. Because of this, it is important for students to explore topics holistically, with ChatGPT as one tool in their toolbelt.

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

Learn more at Review Commons

Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

The manuscript presents a comparative genomic analysis of chemosensory systems across the order Vibrionales. By combining phylogenetic analyses, genomic context, MCP repertoires, and structural comparisons, the authors investigate the diversity and evolution of chemosensory systems within Vibrionales. The study addresses an interesting question and assembles a substantial genomic dataset. The manuscript is generally well illustrated and contains several potentially useful observations regarding the distribution and organization of chemosensory systems across Vibrionales genomes. However, there are a number of conceptual, methodological, and presentation-related issues that should be addressed before the evolutionary conclusions can be fully supported.

The claim that F8 represents a novel chemosensory system appears to be incorrect Lines 407-424, as well as several other places throughout the manuscript, describe F8 as a "previously uncharacterized lineage" and a "newly identified" system. However, F8 chemosensory systems were previously described by Wuichet and Zhulin and have been part of the established chemosensory system classification framework for more than a decade. Furthermore, F8 systems are already annotated as such in MiST. For example, the genome GCF_003390675.1 (Vibrio anguillarum), which is included in this study, contains CheA, CheR, and CheB proteins assigned to an F8 system in MiST.

Consequently, describing F8 as a novel, newly identified, or newly designated system appears inappropriate. This issue requires substantial revision throughout the manuscript. The authors should clearly distinguish between the previously established F8 chemosensory class and any novel observations reported here. If the novelty lies in the distribution of F8 systems within Vibrionales, their genomic organization, their evolutionary history, or some other aspect, this should be stated explicitly.

__Response: __We thank the reviewer for appreciating our work and further commenting on the points to improve this study. As correctly mentioned by you, F8 CSS has been discovered by Wuichet and Zhulin and already annotated in the MiST database. Since this study focuses on experimentally studied CSS clusters within Vibrio organisms, where F6, F7, and F9 have already been studied very well; however, the F8 is not studied experimentally at least in Vibrio cholerae in any literature. We have revised the statement about F8 CSS cluster being novel throughout the manuscript. We agree that MiST database reports different Che proteins, such as CheA, CheR, and CheB, assigned to F8 class, but the information about the entire F8 gene cluster in those Vibrio species has not been provided. Following this, we have identified this entire F8 gene cluster in our study and discussed it as an ‘experimentally unexplored CSS’ in the manuscript.

The conclusions regarding horizontal gene transfer and vertical inheritance are not sufficiently supported. Lines 429-445 contain evolutionary interpretations that appear internally inconsistent. The manuscript interprets the sporadic distribution of F7 as evidence of vertical inheritance coupled with lineage-specific adaptation, whereas several lines later the similarly patchy distribution of F8 is interpreted as evidence of horizontal gene transfer. Similar distribution patterns should not be used to support contrasting evolutionary scenarios without additional supporting evidence.

More broadly, patchy phylogenetic distributions alone are generally insufficient evidence for horizontal gene transfer. Alternative explanations, including differential gene loss, genome reduction, incomplete sampling, or rapid sequence divergence, should also be considered. Furthermore, the conclusions regarding vertical inheritance and HGT imply reconstruction of deep evolutionary history across broad bacterial groups. Based on the methods presented, these inferences appear to rely primarily on CheA phylogenies and analyses of homologous sequences. While informative, these analyses may not be sufficient to confidently infer ancestral origins. The authors should either provide additional phylogenetic evidence supporting these conclusions or moderate the language throughout the manuscript. In their current form, the proposed evolutionary scenarios would be more appropriately presented as hypotheses rather than demonstrated conclusions.

__Response: __We thank the reviewer for this insightful comment. We agree that the evolutionary interpretations presented in the original manuscript need additional supporting evidence. Since our inferences regarding vertical inheritance and horizontal gene transfer were primarily based on phylogenetic distribution patterns and CheA-based phylogenetic analyses. In response, we have carefully revised the relevant sections of the manuscript and moderated the language throughout. The previously presented statements as a conclusion have been reformulated as hypotheses or possible evolutionary scenarios. It must be noted that comparative analysis of protein architecture of F9 CSS, along with phylogeny, revealed a high degree of similarity between Vibrionales F9 protein architecture and their Alphaproteobacterial counterparts, putatively suggesting the HGT event-based acquisition of these CSS within order Vibrionales.

References are frequently missing, incomplete, or potentially inappropriate. One major concern is the quality and completeness of referencing throughout the manuscript. Multiple statements either lack references altogether or appear to cite sources that do not directly support the associated claims. For example, lines 76-78 cite Ulrich et al. (2005) in support of the statement that two-component systems constitute a dominant signaling paradigm in prokaryotes, whereas the cited article is entitled "One-component systems dominate signal transduction in prokaryotes." The text and/or citation should therefore be reconsidered. Similarly, the statement in lines 100-101 that 17 classes of flagellar chemosensory systems have been designated should be accompanied by an appropriate reference. In addition, numerous ecological, physiological, and evolutionary statements throughout the Introduction and Results sections either lack citations or would benefit from more precise supporting references. I recommend that the authors carefully review all references and ensure that each citation directly supports the corresponding statement.

__Response: __We thank the reviewer for this comment. We have added the correct reference at the place of Ulrich et al 2005. Along with this we have further checked the references throughout the manuscript and corrected them wherever it is necessary.

The manuscript would benefit from substantial restructuring and shortening The manuscript is considerably longer than necessary, and several sections appear only loosely connected to the central biological question. In particular, the Introduction contains extensive discussions of Vibrio ecology, virulence, motility, host interactions, and general signal transduction. While these topics are relevant, the overall narrative currently reads more like a broad review article than an introduction to comparative genomics study. I recommend substantially shortening and restructuring the Introduction so that the central biological question and the specific objectives of the study become more apparent to the reader.

Similarly, the section entitled "Multipartite genome and extensive RNA gene repertoire reflect niche adaptation in Vibrionales" (lines 302-342) contains several observations regarding genome size, tRNA counts, and rRNA copy numbers. However, it remains unclear how these analyses contribute to the primary conclusions regarding chemosensory system evolution. This section should either be shortened substantially and more explicitly connected to the central theme of the manuscript or moved to supplementary material. The manuscript would also benefit from substantial language editing. Numerous grammatical and stylistic issues are present throughout the text, including awkward phrasing, subject-verb agreement errors, and overly long sentences. A thorough language revision would improve readability and help the reader focus on the scientific content.

__Response: __We thank the reviewer for this comment. We agree that this manuscript is considerably larger and we have shortened several parts in the introduction such as Vibrio ecology, virulence, motility, host interactions and focused more on study objectives. We have also moved the result tilted as “Multipartite genome and extensive RNA gene repertoire reflect niche adaptation in Vibrionales” in the supplementary part. We have carefully revised the entire manuscript to address grammatical errors, improve sentence structure, correct subject–verb agreement issues, and eliminate awkward phrasing. We have also streamlined several lengthy sentences and paragraphs to enhance clarity, readability, and the overall presentation of the scientific content.

Specific comments:

Line 20: The phrase "28 Vibrio clades" requires clarification. It is not clear what these clades represent, how they were defined, or whether "clades" is the most appropriate term. Please define these groups more clearly. Perhaps the term "genera" would be more appropriate.

__Response: __We thank the reviewer for this comment. We agree that the terms clade and genera can be confusing. Jiang et al., 2022 have given this clade classification for Vibrionaceae family members based on phylogenetic analysis of 8 core genes. We have adopted this classification for our study and cited it wherever it is needed. We have explained this in the introduction section.

Lines 23 and 39: F8 is described as a "novel lineage" and a "previously uncharacterized system." As discussed above, F8 systems have already been described and are annotated in MiST. Please revise these statements.

__Response: __We thank the reviewer for this comment. We have revised this sentence throughout the manuscript.

Lines 35-36: The statement could be interpreted as implying that the involvement of chemosensory systems in host colonization is unique to Vibrio. Since chemosensory systems are broadly distributed across bacteria and frequently contribute to host interactions, I suggest rephrasing this sentence to avoid overstatement.

__Response: __We thank the reviewer for this comment. We rephrased this sentence.

Lines 41-42: The conclusion that CheA and MCP proteins represent promising drug targets is not directly supported by the analyses presented in this manuscript. The study does not evaluate essentiality, druggability, inhibition, or therapeutic feasibility. I recommend removing this statement.

__Response: __We thank the reviewer for this comment. We agree that this study does not directly evaluate the essentiality of CheA/MCP proteins as a therapeutic target. Therefore, we removed this part from the manuscript.

Line 66: The sentence describing responses to environmental cues via "chemotaxis, quorum sensing, and response to nutrients" is awkwardly phrased, since chemotaxis itself often represents a response to nutrients. Please revise for clarity.

__Response: __We have revised this sentence.

Lines 69-70: The statement that signal transduction in Vibrio species is "highly precise" and senses chemical gradients "very accurately" require both a reference and a clearer explanation. Relative to what system or organism is this precision being evaluated?

__Response: __We removed this sentence.

Lines 76-78: Please reconsider the citation to Ulrich et al. (2005) and revise the associated statement accordingly.

__Response: __We have corrected this part.

Lines 100-101: Please provide a reference supporting the statement that 17 classes of flagellar chemosensory systems have been designated.

__Response: __We have added reference for this sentence.

Line 106: The manuscript states that our understanding of CSS architecture and function derives primarily from a limited number of model organisms, particularly Escherichia coli. However, later sections highlight the extensive literature on Vibrio cholerae chemotaxis. Since V. cholerae itself is one of the better-characterized organisms in this field, the rationale for emphasizing E. coli alone is unclear.

__Response: __We agree with your point. We have removed the part of chemosensory system of Escherichia coli and focused on Vibrio cholerae.

Lines 278-286: This paragraph appears to contain contradictory statements regarding the number of genera included in the analysis. Please clarify how many genera were included, which were excluded, and the criteria used for inclusion.

__Response: __We have clarified the criteria for inclusion of genera in our study.

Lines 289-291: Please provide a reference supporting the statement regarding the mutualistic association between Aliivibrio fischeri and squid.

__Response: __We thank the reviewer for this comment. We have provided the necessary reference for this statement.

Lines 291 onward: Several ecological and physiological statements in this section require appropriate references.

__Response: __We have provided the necessary references for these statements. Also, we have shortened some parts of it.

Lines 302-342: This section would benefit from substantial shortening or a clearer connection to the central theme of chemosensory system evolution.

__Response: __We have moved this part into the supplementary material, since it is not directly related to the central theme of the manuscript.

Lines 369-371: This statement is difficult to interpret. MCPs are generally much more variable in abundance than core chemotaxis proteins, and conservation of abundance alone does not demonstrate essentiality. Please clarify and revise this conclusion.

__Response: __We agree with the reviewer. We have revised this statement in the manuscript. MCP protein shows more abundance than other che proteins.

Lines 429-445: The contrasting interpretations of F7 and F8 distributions require additional supporting evidence or a more cautious presentation.

__Response: __We thank the reviewer for this insightful observation. We have rephrased the statement in the manuscript.

Lines 538-541: This sentence is difficult to follow and would benefit from reformulation. In addition, CheA domain architectures, including those associated with Vibrionales F6, F7, F8, and F9 systems, have recently been described in detail by Berry et al., 2023. The authors should discuss their observations within the context of this work.

__Response: __We thank the reviewer for this insightful observation. We have reformulated this result part in accordance with the Berry et al., 2023 paper. We have mentioned the possible reasons behind the absence of P2 domain in Che-F6 as well as extra structured insertion between F8 and F9.

Line 545: The phrase "additional insertion domain" is not well defined. If this region corresponds to a recognized domain, it should be identified explicitly. If it represents an insertion or a poorly structured region, more appropriate terminology should be used.

__Response: __We thank the reviewer for this comment. We have used the terminology “an insertion” as it is not a recognizable domain.

Figure 4: It would be helpful to include the identifiers of the proteins used in the structural comparisons.

__Response: __We thank the reviewer for this comment. We have added the identifiers for the CheA proteins.

__

__

__ __

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

This article has to be completely rewritten because it is now very confused and difficult to read, starting with the title: landscape, architecture, and bipartite organization are difficult terms to employ when describing the "chemosensory system" of bacteria. Systems, in my opinion, does not refer to assemblies, and chemosensing in bacteria refers to anything that involves quorum sensing. Nevertheless, not all bacteria use quorum sensing for flagellar motility, and if these Che-As (and MCPs) are found in "non-chemosensory" systems and are mapped in the abstract without much explanation, this should probably be thoroughly further discussed before debating the organization of the genome and the division of "chemosensory" genes.

__Response: __We thank the reviewer for these comments regarding terminology and conceptual framing. We agree that bacterial signalling encompasses a wide range of signaling mechanisms beyond those involved in flagellar motility. In our manuscript, use of chemosensory system refers specifically to CheA/CheW/CheY/MCP-based signalling pathways as defined by Wuichet & Zhulin, 2010. We have revised the introduction to clarify the difference between chemosensory systems and other bacterial sensory systems such as quorum sensing. We also agree that not all CheA-containing pathways are necessarily associated with flagellar motility and because of this, we have used chemosensory array and chemostaxis in different contexts. Accordingly, we have moderated several statements throughout the manuscript and mentioned that some chemosensory pathways may regulate other cellular functions. We also agree that here wording “driven by bipartite genome architecture” should be changed to distribution of chemosensory systems across different replicons. Overall, following your suggestions, we have significantly changed the title, introduction, results and discussion.

There are often few attempts to take into account the "modern" literature to describe the evolution of bacteria and vibrionales and their capacity for quorum sensing, particularly in the introduction and discussion. Such two lengthy, in-depth paragraphs about the biology and diversity of Vibrionales that span more than two pages and only include six references are rather inappropriate for a research article, particularly when the topic is chemosensing and genetics. The description of the Che family, whose abbreviation is never explained, is highly ambiguous and very confusing in comparison to very basic understanding about vibrionales. Despite their significance intracellularly, we typically gain little from reading this section of Ches. Without making a distinction between chemotaxis and quorum sensing, the third paragraph is intended to a lesson about one component systems, two component systems, and chemosensory systems. Which kind of audience do the authors hope to reach? Microbiologists? Examples of these systems that are better characterized can be found throughout the literature.

Bacterial chemosensory systems are then abruptly introduced. "Chemosensory systems are extremely modular (?) and are typically organized as gene clusters within bacterial genomes". Which sensory genes? Which clusters? What families of bacteria? Which references? When it comes to the classification of chemosensory systems, only Gumerov et al. 2021 is cited. However, what role do other groups play in the study of bacterial Ches and their distribution among the vast diversity of bacteria, such as proteobacteria, actinomycetes, and firmicutes? In order to give a more pertinent Introduction, there are fewer acronyms to employ and undoubtedly more efforts to thoroughly analyze the literature.

__Response: __We thank the reviewer for this detailed and constructive comment. We agree that the earlier introduction was giving more space to the general biology and diversity of Vibrionales and did not provide sufficient context on the development, diversity, and evolution of bacterial CSS. We have therefore substantially revised and shortened the introductory sections describing Vibrionales biology and diversity, while expanding and restructuring the section on bacterial signal transduction and chemosensory systems. Specifically, we have

• reduced the number of acronyms and simplified the description of OCSs, TCSs, and CSSs;
• explicitly distinguished chemosensory signaling from quorum sensing, emphasizing that quorum sensing is primarily a population-dependent signaling process, whereas chemosensory systems detect environmental cues and regulate cellular behaviors such as motility;
• defined the Che (stands for Chemosensory) proteins and introduced the major components of the chemosensory machinery before discussing their organization; and
• expanded the discussion of the diversity and evolutionary distribution of bacterial chemosensory systems beyond Vibrionales, incorporating additional literature covering their occurrence and diversification across major bacterial lineages. We have also revised the text describing chemosensory systems as “modular” to clarify that this refers to the combinatorial organization and evolutionary diversification of core signaling proteins, accessory components, and sensory receptors, rather than simply the co-occurrence of che genes within a genomic region. We have further added relevant references to provide a broader and more contemporary overview of bacterial chemosensory system diversity and evolution.

It learns a little bit more about the chemosensory clusters (whose genes?) in V. cholera, but this information is not really helpful for the study's objective, which at the very end of this incredibly long and badly worded introduction is still ambiguous and essentially unknown. The non-chemosensory/chemotactic motile Vibrionale mutants (line 143) were built by which research team? The authors? Every sentence the authors utilize in the introduction, such as "motility and chemotaxis directly or indirectly contribute to the pathogenicity of bacteria, is somewhat disorganized without a citation (lines 152-155). "The complex (?) interaction between chemotaxis and virulence gene expression in pathogenic Vibrio species" is not better to consider. There are no references included, even while discussing the last three decades of V. cholera research. This is not really appropriate for publication. After a lengthy introduction to the many proteins that mediate chemosensing (quorum sensing) in bacteria, the study is restricted to informatics work, see material and methods, and finally limited on CheAs, which is fairly harmful. For correlation analysis, phylogeny, and structure modeling, the authors use previously available information. Therefore, what distinguishes all of these tables and figures from what is currently understood about bacterial genetics and evolution?

Response: We thank the reviewer for this important comment. We agree that the original introduction contained excessive discussion of well-characterized chemosensory systems in Vibrio cholerae. We have therefore shortened this section, clarified the study objectives, and added appropriate references to statements concerning motility, chemotaxis, and virulence.

Regarding the novelty of the study, our objective was not to rediscover individual chemosensory proteins, but to provide a comparative, order-wide analysis of chemosensory system evolution across Vibrionales. Using 116 representative genomes and ~10,000 additional genomes/MAGs, we resolved four distinct CSS lineages (F6-F9), characterized their contrasting genomic distributions and replicon localization, and identified F8 as an experimentally unexplored system. We further provide evolutionary evidence for distinct trajectories of these systems, including probable horizontal acquisition of F9, and reveal a conserved F6 core alongside more dynamic accessory system. We have also revised the introduction to make these objectives, findings, and the significance of the comparative analysis more explicit.

Reviewer #2 (Significance (Required)):

The majority of the figures are too little to make any sense. Additionally, there are some unexpected "surprises". For example, the authors' in silico data on Photobacterium toruni, E. coli, and Vibrio qinghaiensis while Introduction led us to anticipate or pick V. cholera as the primary target (see last part of introduction). Bootstrap analysis and a clear display of the clades are necessary for phylogenetic validation. A well-established protein structure (Che-A? Che-B? Other Ches?) is required as an unambiguous reference in order to validate protein structure modelling.

I would also add that since Vibrionaceae is a family of g-proteobacteria in the order Vibrionales, it is not surprising that they are common traits in the genomes of proteobacteria and vibrionales. However, I'm not sure what the authors mean when they say that patchy and replicon-flexible groups are vertically inherited from g-bacteria. A set of genes (discrete CSS types?) that would be horizontally acquired from alphaproteobacteria are the subject of the same critical point. What is the duration of the convergence of Alphaproteobacteria and Vibrionales? Please refer to Sonnenberg and Haugen (2023) about "bipartite" genome and horizontal transfer.

__Response: __We thank the reviewer for these suggestions. We have improved the readability of a few figures by increasing font size, clarifying clade annotations, and adding bootstrap support values to the phylogenetic trees. We have also revised the introduction to clarify that the study focuses on chemosensory systems across Vibrionales, rather than V. cholerae alone, and have highlighted Photobacterium toruni and Vibrio qinghaiensis because of their unusual CSS distribution across replicons. In order to have a well-established protein structure from AFDB for structures validation, we have used the pLDDT and pTM score for already available and predicted structures, respectively, and we have added this point in our methodology. Finally, we have revised our interpretation of vertical inheritance and horizontal acquisition, moderating the relevant claims. We have further refined the evolutionary interpretation of F6, F7, and F8 by placing their distribution within the broader Gammaproteobacteria context, while F9 is discussed separately based on its close phylogenetic association with Alphaproteobacteria and the evidence supporting its possible horizontal acquisition.

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

This manuscript by Rawool and Sharma is a comprehensive bioinformatics analysis of the chemosensory systems in Vibrionales, their chromosomal locations, likely evolution and acquisition, and differences in CheA architectures. The Abstract and Discussion sections are beautifully written, but the language in the rest of the paper, especially in the Introduction section, is difficult to follow at times (I have many comments below under minor points). An impressive amount of data was acquired and analyzed for this paper, including the identification of F8 systems in Vibrios, and I commend the authors for filling the knowledge gap with such a comprehensive data set. However, the paper overall is extremely long and very detailed, and it took me a very long time to plow through all of it.

The Introduction section, for example, reads like a literature review from a dissertation, but without figures, and could be streamlined without losing impact. Lines 132-154, include many details on environmental sensing and virulence studies, but it reads like a long list of disconnected sentences with findings from different studies, rather than an integrated summary of current knowledge. The Methods section is also very detailed, and although I am not a bioinformatician, the level of detail often seems excessive. In the Results section, data sentences are often followed by discussion or qualification sentences, which makes the Results section even longer. So, while the science in this paper and its interpretation is sound, the paper needs reworking to make it more palatable for most readers. I think it will be difficult for most readers to remain engaged through the entire manuscript the way it is currently presented.

Response: We thank the reviewer for their appreciation of our study. Following their suggestions, we have shortened the introduction part as well as the overall manuscript. In the methods part, we have included the detailed parameters used in our analysis, so that result can be reproducible for others. We agree about the lengthy result part, and we have shortened this part as well.

Minor points:

1. General - sometimes clades are written in capitals, sometimes not, and sometimes they are in italics and other times not. Was this intentional? Shouldn't the formatting be consistent throughout?

__Response: __We thank the reviewer for noting down this inconsistency. There should not be variation in the formatting. We have carefully reviewed the entire manuscript and standardized the formatting of clade names throughout the text, figures, figure legends, and supplementary materials to ensure consistency.

Line 35 - "moving towards nutrients and away from harm" is a very narrow interpretation of chemosensory systems, referring solely to chemotaxis, which only 1 of the 4 chemosensory systems in Vibrio likely supports. The statement here should be more inclusive.

__Response: __We thank the reviewer for this important clarification. We agree that the original statement focused primarily on chemotaxis and did not adequately reflect the broader functional diversity of bacterial chemosensory systems. The sentence has been revised to emphasize that chemosensory systems mediate the detection of environmental cues and can regulate a variety of cellular behaviors, including but not limited to motility.

Line 56 and line 702 - "V. cholerae" not "V. cholera" - a common victim of autocorrect

__Response: __We thank the reviewer for identifying this typographical error. "V. cholera" has been corrected to "V. cholerae" at the indicated locations and throughout the manuscript.

Line 64 - "marine sea"? Marine = of the sea. So, effectively "sea sea" = redundancy.

__Response: __We thank the reviewer for noting this. We have corrected this part in the manuscript.

Lines 67-68 - the English on these lines doesn't make sense to me. Perhaps "...reaching swimming speeds of 40-200 mm/sec, which requires 1-2 orders of magnitude more energy for propulsion than that required for Escherichia coli".

__Response: __We thank the reviewer for noting this point. Since this sentence is not directly related to the chemosensory system, we have removed this line from the manuscript.

Line 69 - Why mention V. alginolyticus here as an example of a Na+-driven flagellar motor when it's relevant for other Vibrios as well? Also, no reference is provided.

__Response: __We thank the reviewer for noting this point. Since this sentence is not directly related to the chemosensory system, we have removed this line from the manuscript.

Lines 79-95 - While introducing the proteins found in a chemosensory pathway, chemotaxis itself is given as the "pathway", whereas it should be indicated that it is an example pathway. Not all chemosensory pathways have CheYs that interact with FliM. And not all chemoreceptors in Vibrios have periplasmic sensing domains - some are cytoplasmic.

__Response: __We agree with the reviewer on this point. We have revised the phrasing in the manuscript.

Lines 91-93 - awkward sentence where the last clause reads like a non-sequitur.

__Response: __We thank the reviewer for this observation. We have revised and streamlined the relevant paragraph to improve its clarity, organization, and overall flow.

Lines 110-113 - The "function" of chemosensory systems are determined by their output, whereas the signals recognized determine their specificity. Please correct.

__Response: __We thank the reviewer for this clarification. We agree that the signals recognized by chemoreceptors determine the specificity of a chemosensory system, whereas its function is defined by the downstream cellular response it regulates. Accordingly, we have revised the text to distinguish between signal specificity and system function.

Line 111 - Aer is not an MCP as it is not a "methyl-accepting" receptor in E. coli. Change "MCP proteins" to "chemoreceptors" to be accurate.

Response: We have changed this part.

Line 115 = 43 MCPs; Line 149 = 45 chemoreceptors; Line 225 = 46 MCPs - there is variation in the total number of MCPS in Vibrios. Perhaps give a number range where appropriate (line 115, V. cholerae in general), and specific numbers where specific strains are mentioned.

__Response: __We thank reviewer for noticing this variation in MCP gene numbers. We have revised this statement.

Line 116 - "forms"

__Response: __We have changed this part.

Line 119 - Change "the" to "a" and what is meant by "double-layered membrane structure" since it isn't in the membrane? Please use a more accurate description.

__Response: __We thank reviewer for this comment. We agreed that it is not a double-layered membrane, rather F9 CSS cluster form a double-layered appearance in the cytoplasm. We have rephrased this in the manuscript.

Line 121 - Replace the comma with a semi-colon before "overall".

__Response: __We have changed this part.

Line 124 - You've already told us that F9 is a cytoplasmic array

__Response: __We have changed this part.

Line 226 - Change "during" to "via"

__Response: __We have changed this part.

1. Line 133 - "which is involved" and "indicating a link"

__Response: __We have changed this part.

Lines 137-139 - If V. cholerae shows a chemotaxis response to these chemicals, then it isn't clear why you would say that they sense the environment "through these CSS clusters" - only 1 cluster (F6) is known to be involved in chemotaxis.

__Response: __We thank reviewer for this comment. We have corrected this statement.

Line 140 - "for epithelial colonization"

__Response: __We have changed this part.

Line 151 - gene names should be in italics

__Response: __We have changed this part throughout the manuscript.

Line 153- "contributes"

__Response: __We have changed this part.

Line 156 - "are associated"

__Response: __We have changed this part.

Line 162 - "Studies" don't perform anything. It is an inappropriate subject. But kudos for using the word "lacuna" so eloquently!

__Response: __We have changed this part.

Line 179 - "from which a pie chart”!

__Response: __We have changed this part.

Line 187 - "using the ggsignif"

__Response: __We have changed this part.

Line 209 - "A total of 154"

__Response: __We have changed this part.

Line 219 - "using parameters the same"

__Response: __We have changed this part.

Line 225 - "the 46 MCP proteins were aligned"

__Response: __We have changed this part.

Line 240 - "was converted"

__Response: __We have changed this part.

Figure 1 - the labels under parts C, D and E are too small

__Response: __We have increased the font size of the labels and revised the figures.

Line 346 - "encodes"

__Response: __We have changed this part.

Line 349 - "with average values"

__Response: __We have changed this part.

Line 352 - defined HK and RR on lines 347-348

__Response: __We have changed this part.

Line 365 - replace "chemotaxis-associated" with "chemosensory-associated". Chemotaxis is not inclusive.

__Response: __We have changed this part.

Line 380 - shouldn't "cheA" be in italics?

__Response: __We have changed this part.

Line 281 - again, "chemosensory proteins" not "chemotaxis proteins"

__Response: __We have changed this part.

Line 382 - "in trends with" makes no sense

__Response: __We have changed this part.

Line 283 - "an average of 33"

__Response: __We have changed this part.

Lines 387-388 - I don't understand the comment in brackets - why was the protein count limited to 40?

__Response: __We thank the reviewer for this comment. We agree that the rationale for the cutoff value was unclear. Therefore, we have revised the analysis and replaced the previously used cutoff of 40 MCP proteins with the average MCP protein count of 34 calculated from the dataset. The corresponding text has been updated in the revised manuscript.

Lines 398-405 - It isn't clear which species have lost flagella, and did they also loose the F6 system? Did they retain the other systems? Lines 427-429 doesn't make it any clearer and I am interested to know.

__Response: __We thank reviewer for this comment. The species from three clades namely Marinum, Rumoiensis, and Halioticoli don’t have any CSS proteins present in it and all these organisms are well-known to be non-motile, suggesting that they don’t have flagellar proteins. These species lost F6 as well as all other F classes.

Another organism, Vibrio qinghaiensis Q67 does not encode F6 system, however it has F7 system.

Line 423 - "HubP protein functions" makes no sense

__Response: __We thank the reviewer for this comment. The text has been revised to clarify that HubP is a polar landmark protein that acts as an anchoring factor for the localization of chemotaxis arrays through its interaction with the ParC/ParP complex. We have given proper reference for this.

Line 470 - why are your reporting 2 F7s and then explaining further on on Line 474 that this is a genome assembly artifact? The information is dislocated and should be streamlined.

__Response: __We thank reviewer for this comment. As per our analysis, two F7 clusters are present in Vibrio qinghaiensis Q67 species. When we checked further, these clusters reside within nearly identical (~99% sequence identity) terminal regions spanning ~20.3 kb at both ends of the replicon. This is artifact during genome assembly process which involves duplicated terminal sequences. We have corrected the order of writing these details in the text.

Line 499 - "with the smaller"

__Response: __We have changed this part.

Lines 536-538 - The F7 system in Vibrios isn't involved in chemotaxis signaling - please correct your language here.

__Response: __We have revised the statement for clarification and added the figure number.

Lines 550-551 - "Structural superpositions analyses similarity...." makes no sense. I don't understand what you are trying to say.

__Response: __We have rephrased this sentence.

Lines 612 and 630 report the same thing - sensing of bile and mucin. Are both instances necessary?

Response: We have removed the redundant sentence.

Figure 6B - "against" not "againts"

__Response: __We have changed this text.

Line 634 - "accounting for 69% of sensory inputs"

__Response: __We have changed this part.

Line 659 - Hiremath et al., 2015b isn't an appropriate reference for the sensory repertoire of PAS domains. Please reference a PAS domain review instead, e.g., Stuffle and Watts, 2021. PMID: 33647528; PMCID: PMC8169565.

__Response: __We thank reviewer for this comment. We agreed that the reference cited was not completely based on PAS domain, but the authors have mentioned about PAS domain in their paper. However, we have also cited paper for PAS domain which you mentioned in the comment.

Line 664 - "ligand" not "legend"?

__Response: __We have changed this part.

Line 740 = "chemosensory" instead of "chemotaxis"

__Response: __We have changed this part.

Line 744 - "between the extra domain..."

__Response: __We have changed this part.

Author response:

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

We believe that the manuscript has been substantially strengthened through the revision process. The main changes are summarized below:

We substantially revised the Introduction and Discussion sections to better position our work relative to previous studies on starvation-dependent thermotaxis plasticity, neuropeptidergic modulation, and AWC function.

We clarified throughout the manuscript the distinction between negative thermotaxis in innocuous thermal ranges and thermonociceptive responses to noxious heat. We now discuss more explicitly that these behaviors involve at least partly distinct molecular, cellular, and circuit-level mechanisms.

We performed new experiments in ins-1 mutants. Unlike what was previously reported for thermotaxis plasticity, ins-1 does not appear required for starvation-dependent thermonociceptive plasticity in our paradigm (new Figure 6—figure supplement 1).

We revised the analysis and terminology used for AWC calcium imaging data. We no longer use the “deterministic/stochastic” terminology and instead describe a starvation-induced shift from predominantly excitatory responses to a mixed distribution of excitatory and inhibitory responses. We also added new quantitative analyses and histogram representations of response distributions, as directly suggested by reviewers, to better illustrate this point.

We performed new genetic interaction experiments using eat-4; flp-6 double mutants. These analyses revealed that glutamatergic and FLP-6 signaling act largely in parallel to mediate heat-evoked reversals after early food deprivation, while prolonged starvation reveals a hierarchical interaction between these pathways.

We revised and clarified the mechanistic model figures accordingly, particularly regarding the proposed ASI → AWC signaling pathway and the role of ASI-derived neuropeptides.

We improved the presentation and statistical rigor throughout the manuscript, including:

- Replacement of heating power values by corresponding temperature increases,

- Clarification of the rationale for using the 1-hour off-food condition as reference,

- Expanded statistical reporting and multiple-comparison procedures,

- Additional methodological details for calcium imaging, rescue validation, and cell ablation approaches,

- Clarification of replotted datasets in figure legends.

We also simplified the manuscript by removing experiments whose interpretation remained ambiguous (notably the nsy-1 and nsy-7 analyses).

Below, we provide a detailed point-by-point response to all reviewer comments.

Public Reviews:

Reviewer #1 (Public review):

This study by Thapliyal and Glauser investigates the neural mechanisms that contribute to the progressive suppression of thermonociceptive behavior that is induced under conditions of starvation. Several previous studies have demonstrated that when starved, C. elegans alters its preferences for a variety of sensory cues, including CO2, temperature, and odors, in order to prioritize food seeking over other behavioral drives. The varied mechanisms that underlie the ability of internal states to alter behavioral responses are not fully understood; however, there is growing evidence for a role of neuropeptidergic signaling as well as the capacity for functionally distinct microcircuits, formed by distinct internal states, to trigger similar behavior outcomes.

Within the physiological range of C. elegans (~15-25{degree sign}C), starvation triggers a profound reduction in temperature-driven thermotaxis behaviors. This reduction involves the recruitment of the amphid sensory neuron pair AWC. The AWC neurons primarily act to sense appetitive chemosensory cues; however, under starvation conditions begin to display temperature responses that previous studies have linked to the reduction in thermotaxis navigation. Here, Thapliyal and Glauser investigate the impact of starvation on thermonociceptive responses, innate escape behaviors that are triggered by exposure to noxious temperatures above 26{degree sign}C or rapid thermal stimuli below 26{degree sign}C. They compare the strength of thermonociceptive behaviors, specifically heat-triggered reversals, in worms experiencing either early food deprivation (1 hour off food) or prolonged starvation (6 hours off food). Their experiments demonstrate a progressive loss of heattriggered reversals that is mediated by AWC and ASI neurons, as well as both glutamatergic and neuropeptidergic signaling.

At the level of neural activity, this study reports that the transition from early food deprivation to prolonged starvation reconfigures the temperature-driven activity of AWC neurons from largely deterministic to stochastic. This finding is interesting in light of previous work that reported the opposite transition (from stochastic to deterministic) in temperature-driven AWC responses when comparing well-fed worms to those kept from food for 3 hours. This study also identifies neural and genetic mechanisms that contribute to differences in thermonociceptive responses at +1 versus +6 hours of starvation; confusingly, these mechanisms are partially distinct from those that contribute to differences in negative thermotaxis behaviors in well-fed and +3 hours of starvation worms (Takeishi et al, 2020). A limitation of this manuscript is that these differences are not particularly acknowledged or addressed, other than the hypothesis that independent mechanisms underlie negative thermotaxis versus thermonociceptive stimuli. However, this suggestion is not experimentally verified.

We thank this reviewer for pointing to the interest of our work. The difference between previous work focusing on negative thermotaxis in the range of innocuous temperatures and our work focusing on thermo-nociceptive response is important and indeed deserves further clarification and a deeper discussion in the manuscript.

Two major empirical evidence for a distinction between negative thermotaxis (as assessed in previous studies) and thermonociceptive plasticity (as assessed in our paradigm) were already included in the initial article version. First, we reported a decrease in average response in AWC neurons due to a shift in the distribution of response polarities from mostly up-response to a mix of ‘up-response’ and ‘downresponse’ after starvation, while previous results showed an increase in response probability of AWCs after starvation (Takeishi et al, 2020). Second, contrary to starvation-evoked thermotaxis adaptation, ASI neurons are required to orchestrate starvation-evoked plasticity in thermonociception. These observations already indicate differences at the circuit and cellular level. For the revision, we conducted further experiments to address the molecular level. We tested ins-1 mutants (see also specific point 3 by reviewer 2, below) and deepened this aspect in the discussion section of the revised manuscript. Previous study found that INS-1 signaling from the intestine is a major mediator of negative thermotaxis plasticity. In contrast, our new data show that INS-1 peptide does not seem critical in regulating starvation-dependent thermonociceptive plasticity (see new Figure 6-supplement 1). Taken together these three lines of empirical evidence support the notion that negative thermotaxis and thermonociceptive starvation-evoked plasticity involves at least partially distinct mechanisms and it seems therefore inappropriate to qualify this notion as purely hypothetical.

Modification in the revised manuscript include extended introduction about the known thermotaxis regulation mechanisms (Introduction section), new Figure 6-supplement 1 about ins-1 and accompanying text in the result section as well as extended discussion about these differences (Discussion section)

Multiple additional aspects of this study make the results difficult to synthesize with existing knowledge, including

(1) Differences in - and insufficient discussion of - the magnitude and kinetics of thermal stimuli;

We have included a better description of the stimuli characteristics in the revised methods section. The discussion section was deepened to better emphasize that different types of thermal stimuli have been used in different studies.

(2) This study's use of "heating power" rather than temperature values when presenting behavioral results;

Thanks for noting this point, which was indeed an unnecessary complication in the result display of the initial manuscript. We have changed ‘power values’ to corresponding ‘temperature increase’ in the revised figures.

(3) The use of +1 hours starvation as a baseline instead of well-fed worms. Indeed, this last point reflects a noticeable experimental result that differs from previous studies, namely that at room temperature, the basal movements of well-fed and starved worms are not different. Such a surprising result warrants further quantification of worm mobility in general and could have prompted a set of experiments directly testing previously published thermal conditions to demonstrate that the new effects reported arise specifically from the use of thermonociceptive stimuli, as hypothesized.

The consideration of on-food and off-food behavioral state is an important point indeed. We found that, at room temp, worms shift from dwelling on food (a state with high spontaneous reversal rate) to global search off-food (a state with low spontaneous reversal, after 1hr starvation) (see Figure 1B). Therefore, unlike the reviewer’s statement, the reported data highlighted key differences in the basal locomotion of worms in fed and 1hr starved conditions. Furthermore, these behavioral states have been characterized very deeply using high-content worm behavioural tracking in our recent publication: Thapliyal et al. 2023 (PMID: 37236963). Our choice of using 1hr as a baseline is primarily driven by the fact that an elevated baseline of spontaneous reversals on food decreased the dynamic range to monitor changes in heat-evoked reversals. 1-hour early food deprivation reduced spontaneous reversals and led to a mild attenuation of heat-evoked responses at low stimulus intensities, while responses to stronger stimuli remained comparable to those of fed animals. Additionally, we observed a clear progressive decrease in heat-evoked reversals with increased duration of food-deprivation, which we further used to dissect the mechanism underlying this plasticity. The choice of the 1hr food deprivation timepoint as a reference is further justified below.

Finally, a previous report (Yeon et al, 2021) demonstrated differences in the impact of chronic versus acute neural silencing on starvation-dependent plasticity in the context of negative thermotaxis. We therefore wonder whether similar developmental compensation impacts the neural circuits that contribute to starvation-dependent plasticity in the thermonociceptive responses.

Indeed, this is an interesting question. Our conclusions are so far based on ablation (with chronic effects). In order to gain insight on this question, future studies could address the impact of chronic vs acute silencing approach in starvation-dependent thermonociceptive responses. We have added an opening on this question in the discussion, as follows:

“Another open question is whether ASI action takes place during development (prior to starvation), or more acutely with active signaling after starvation.”

A weakness of this manuscript is that the introduction is insufficiently scholarly in terms of citations and the description of current knowledge surrounding the impact of internal state on sensory behavior, particularly given previous work on the impact of feeding state on thermosensory behavioral plasticity (Takeshi et al 2020, Yeon et al 2021) and chemosensory valence (Banerjee et al 2023, Rengarajan et al 2019, etc).

To address this weakness, we have revised the introduction section of the manuscript and cited previous relevant research on the impact of internal states on animal behavior, including the papers suggested by the reviewer. We note that 2 out of 4 suggested citations were already present in the initial manuscript (though in the discussion section).

Similarly, the authors' commanding knowledge of the distinction between thermotaxis navigation (especially negative thermotaxis) and thermonociceptive behaviors could be communicated in more depth and clarity to the readers, in order to contextualize this study's new findings within the previous literature.

As mentioned above, we have deepened this aspect in the discussion section of the manuscript (with a dedicated paragraph). It is quite clear that starvationinduced plasticity in negative thermotaxis and thermonociceptive behaviors engage distinct mechanisms (at least in part). These differences include distinct alterations in AWC calcium activity, role of ASI neurons and INS-1 neuropeptide.

Nevertheless, this study represents a solid addition to the growing evidence that C. elegans sensory behaviors are strongly impacted by internal states, and that neuropeptidergic signaling plays a key role in mediating behavioral plasticity. To that end, the authors have provided solid evidence of their claims.

We thank this reviewer for the efforts in evaluating our manuscript, for the positive assessment of our work, and for highlighting some weaknesses which, we believe, have been addressed through the revision.

Reviewer #2 (Public review):

In this work, Thapliyal and Glauser tried to provide a mechanistic understanding by which animals modulate their neural circuit responses to control nociceptive behavior on the basis of the dynamic internal feeding state. It is an important study that adds to the growing body of evidence coming from multiple model systems. They have used elegant genetics, behavioral, and Ca-imaging experiments to demonstrate how the auxiliary thermosensory neuron pair, AWC, and one of the internal state-sensing interneuron pairs, ASI, respond to dynamic internal starvation state to modulate behavioral response to noxious heat. Interestingly, these neuron pairs use distinct molecular mechanisms along with some other unidentified neurons to suppress heat-induced reversal response under short-term and prolonged starvation. The experiments are well performed, supporting most of the claims and providing an important framework for future studies.

I have some queries that, if answered, will certainly enhance the study.

(1) The results suggest that ASI is one of the primary drivers for the starvation-evoked behavioral plasticity, which regulates AWC activity under prolonged starvation. It raises many important questions, including: (a) how starvation modulates ASI response to heat?, and (b) under prolonged starvation, whether ASI also promotes other, non-AWC, glutamatergic inhibitory neurons to suppress heat-induced reversal, and how?

We agree with this reviewer that the mechanisms by which ASI detects and mediates starvation-evoked changes in our model is a very interesting (unsolved) question. However, addressing these questions empirically represents a substantial body of work that would go beyond the scope of the present report. E.g., is temperature-dependent activity in ASI even relevant? At present, we envision that ASI could either work acutely (during heat stimuli) or be modulated over much longer time frames (hours of starvation) as an internal state sensor. Therefore, there will be quite some exploration needed before we figure out the ASI-level regulation more fully (including the critical temporal aspect regarding cell activity, as well as quantitative and qualitative transmission aspects). It will be very interesting in future work to address these questions.

(2) How does ASI regulate AWC activity? In the proposed model (Figure 8) authors suggested an independent, unknown signal, other than INS-32 and NLP-18, from ASI to regulate AWC activity. However, from the results, the existence of another signal is not very clear.

Thanks for raising this point, which reveals a weakness in our graphical representation (in Fig. 8) that was not properly conveying our point. Our current work shows INS-32 and NLP-18 to be important in modulating heat-evoked reversals upon starvation. However, at the moment, we don't know if INS-32, NLP-18, both, and/or other neuropeptides from ASI modulate AWC activity patterns. The calcium imaging experiments in single, double and potentially triple mutants would answer these questions but are not within our current reach, given the time needed to carry out these experiments. However, we acknowledge this point and have changed the figure and its legend to state that the arrow connecting ASI to AWC activity pattern could potentially reflect the action of these neuropeptides.

(3) Previously, Takeishi et. al. showed that ins-1 dynamically modulates AWC-AIAmediated thermotaxis behavior based on the feeding state of the animal. It raises questions whether ins-1 also contributes to noxious heat-induced reversal behavior.

We thank the reviewer for this question. We have now quantified the phenotype of ins-1 mutant in our paradigm. Our data shows that INS-1 neuropeptide is not critical in mediating starvation-evoked thermonociceptive plasticity, unlike plasticity in thermotaxis behavior (See Figure 6- Supplement 1). Together with the differential activity patterns in AWC and the differential need for ASI neurons, these new data further consolidate the notion that starvation-evoked thermotaxis adaptation and noxious-heat avoidance engage separable molecular, cellular and circuit-level modulatory mechanisms. A specific discussion paragraph was added too.

(4) Experiments with AWC fate conversion mutants (nsy-1 and nsy-7) were very good ideas; however, the results obtained were confusing. flp-6 mutant data suggest AWCoff would be essential for heat-induced reversal, especially at the low intensity stimulus level. However, the nsy-1 mutant-forming two AWCon neurons showed complete rescue at the low heat level, which is quite opposite. Similarly, although less prominent, eat-4 rescue experiments suggested both nsy-1 and nsy-7 should behave normally at high heat conditions, which was not the result observed.

We appreciate this comment and the legit attempt to infer what we should expect from a worm with two AWCon or two AWCoff, respectively. From previous studies so far, it's not quite clear if cellular properties of newly formed AWCs in nsy-1 and nsy-7 mutants, including response to sensory cues, formed synapses and their partners, expression of neuromodulator and gap junctions, synaptic output are similar or different. We think further studies are required to first establish if FLP-6 and glutamate signaling (expression, release and action) from altered AWCs in nsy-1 and nsy-7 mutants are the same or different. Therefore, direct comparison between cell fate conversion mutants with flp-6 and glutamate would rely on too many assumptions at this stage. Considering this comment, the limited additional value of the data with nsy1 and nsy-7 mutants (in the absence of additional analyses) and the confusion it could trigger, we have decided to remove these non-essential data of the manuscript.

Reviewer #3 (Public review):

Summary:

Thapliyal and Glauser show that hunger alters how C. elegans responds to noxious thermal stimuli. Using targeted neural ablation, mutant analysis, and live-cell functional imaging, the authors demonstrate that hunger changes the properties of AWC sensory neurons, which sense noxious heat. The authors further show that the effects of hunger on nociception require ASI neurons, which are known to respond to hunger and mediate the effects of food deprivation on behavior. Finally, the study uses mutant analysis to implicate glutamate and specific neuropeptides in thermal nociception and in the modulation of nociceptors by hungerresponsive neurons.

Strengths:

The study clearly shows a strong effect of hunger on nociception and documents a striking effect of hunger on the intrinsic properties of AWC sensory neurons, which respond to noxious heat. The study also clearly and compellingly demonstrates that ablation of hunger-responsive ASI neurons blocks the effects of hunger on nociceptive AWCs. These data, which constitute the kernel of the manuscript, are striking and exciting.

Weaknesses:

The study has some weaknesses that the authors should address.

(1) Ablation of AWC neurons alters the basal sensitivity to noxious heat stimuli. This should be clearly noted in the description of the result and warrants some discussion.

We thank this reviewer for raising this legitimate point. We have clarified this aspect in the results section of the revised manuscript, reading as follows:

“Removal of AWC nearly abolished heat-evoked reversal behavior across all stimulus intensities and timepoints (Figure 2B and E). While one should keep in mind that potential indirect developmental effects might take place in neuro-ablation lines, this observation suggests that AWC plays an essential role in mediating the thermonociceptive response under both early food deprivation and prolonged starvation. Notably, in AWC-ablated animals, the residual response level was unaffected by starvation, suggesting that AWC might also be required for the expression of starvation-dependent plasticity.”

The contrast with known function of the best-characterized sensory neurons mediating thermal nociception (AFD and FLP) is discussed as follows:

“...Therefore, noxious heat-evoked activity in AWC varies widely according to context, which is in line with previous literature [18, 20, 41]. Interestingly, the role of AWC is distinct from that of AFD and FLP neurons, which are canonically linked to thermosensation and nociception [5, 14, 42, 43], but contribute only modestly to heat-evoked behavior in our assay conditions with between 1 and 6 hrs of food deprivation.”

(2) Throughout the study, it seems that data are replotted in multiple figure panels. The authors should clearly indicate in the figure legends when this occurs. Also, the authors should ensure that statistical tests requiring multiple comparisons are correctly implemented and reflect the number of times experimental data are compared to a single set of control data.

Thanks for raising this important point. We have clarified this aspect in the revised figure legends of the manuscript, and in the method section. In some instances, we reconducted some analyses to be perfectly rigorous in multiple comparison accounting. This did not lead to significantly different conclusions. The one exception was that the small effect of eat-4 mutation on spontaneous reversal went below significance threshold. We therefore removed this aspect of the result reporting and of the corresponding interpretation scheme, which became slightly simpler (Figure 3). Globally, this makes the story more focused.

(3) How ASIs modulate AWCs remains unclear. The authors find that loss of INS-6, an insulin-like peptide provided by ASIs, partially recapitulates the effect of ASI ablation. This observation is not further developed, and instead, the authors characterize other secreted factors that seem to mediate sensitization of animals to noxious heat stimuli. While it is interesting that there are multiple opposing inputs into the nociceptor circuit, the essential connection between ASIs and AWCs that underlies the foundational observations in Figures 1 and 2 is not sufficiently characterized.

Whereas we agree that how ASI modulates AWCs is only partially solved by our study, we should emphasize that our work identified two ASI-expressed neuropeptides that function to decrease reversal response after starvation: INS-32 and NLP-18. We initially set a lower priority on INS-6 because the reversal response level in starved mutants appeared lower than that in nlp-18 and ins-32. It is important to note that ins-32 and nlp-18 are not ‘generally potentiated’ mutants, but display reversal upregulation selectively following starvation, which placed them as strong candidates to selectively mediate ASI regulation. This said, it is also true that these two mutants (and ins-6 too) display reduced responsiveness at the early food deprivation time point. Therefore, none of the neuropeptide mutants was strictly identical to ASI ablated line, suggesting that the peptides might also work via non-ASI cells at the early food deprivation timepoint.

Following this reviewer’s comment, we have attempted to complement our story with the idea of using a similar approach and rescue ins-6 with its endogenous promoter or ASI-specific promoter. Unfortunately, we failed to obtain rescue effects, and therefore these data (with a negative result) remain inconclusive (as we cannot guarantee that the rescue constructs were functional). We decided to keep these data aside in the revised manuscript. Globally, our point made graphically in Figure 7F remains valid. We have complemented the figure legend to mention that INS-6 could also potentially work from ASI, but it is not depicted as no ASI-specific data are available. In summary, our data suggests that the connection between ASI and AWC(s) might be established by the integrated action of multiple peptides and their receptors. Further calcium imaging experiments in single, double and potentially triple mutant(s) of peptides and receptors would be required go deeper in this question, which could be performed in future work.

“...Additional neuropeptides (such as INS-6) may also be involved, but in the absence of direct evidence for their origin from ASI, they were not included in this scheme.”

(4) The assertion that 'starvation reshapes AWC responses from deterministic to stochastic' is not clearly supported by the data. AWC neurons seem capable of showing different responses to thermal stimuli, and the probabilities associated with these responses change after fasting. The different kinds of responses are seen under basal and fasted conditions.

We thank this reviewer for the comment. There is an activity response shift that is quite solidly described, including with new quantitative analyses of distributions (histograms in new Fig. 4CD and new Fig. 5C-D, accompanied by Kruskal-Wallis tests). Yet, we totally agree that the wording choice was inappropriate. We have furthermore changed our terminology to avoid using the terms “stochastic” or “deterministic” that were indeed a cause of confusion. We now use the terms “stimulus-locked responses” and describe the shift as “shift from mostly excitatory responses to a mix of both excitatory and inhibitory responses”. We have also included detailed methodology for characterization of traces and statistical analysis in the revised method section of the manuscript, together with the new analyses on peak polarity distribution.

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers agree that the study is clearly presented and makes good use of behavioral, genetic, and imaging approaches to link starvation state with changes in AWC and ASI function. To strengthen the manuscript and ensure clarity for readers, we ask you to address the following points in revision:

(1) Positioning and citations.

Clarify how your findings relate to Takeishi 2020, where the opposite trend in AWC activity was reported, and make a clear distinction between thermonociception and thermotaxis. The introduction should also include additional citations in two specific areas: prior work on AWC and noxious thermal stimuli, and studies demonstrating starvation-dependent behavioral changes via altered neuropeptide release (e.g., Banerjee 2023; Rengarajan 2019).

We have clarified this aspect with extension of the work cited in the introduction and extensive rewriting of the discussion sections.

Our data shows that mechanisms underlying starvation dependent changes in thermonociception and thermotaxis show differences at the molecular, cellular and circuit levels. First, we see a decrease in average response in AWC neurons due to shift from mostly excitatory to a mix of excitatory and inhibitory responses in response to noxious heat after starvation, while previous study found an increase in response probability of AWCs after starvation (Takeishi et al, 2020). Second, contrary to thermotaxis behavior ASI neurons are required to orchestrate starvation evoked plasticity in thermonociception. And, finally, previous study found that INS-1 signaling from the intestine regulates thermotaxis behavioral plasticity while INS-1 peptide does not seem critical in regulating starvation-dependent thermonociceptive plasticity (new data in Figure 6 supplement 1).

We have revised the introduction section of the manuscript and cited previous relevant research on AWC and noxious thermal stimuli and studies demonstrating starvationdependent behavioral changes via altered neuropeptide release including the papers suggested by reviewers. The extended discussion section reads as follows:

“Starvation regulates thermonociceptive and negative thermotaxis plasticity via at least partly different mechanisms

Previous studies showed that AWC plays an important role in starvationdependent plasticity in the negative thermotaxis behavior in an innocuous thermal range between 15 and 25°C [26, 33]. Negative thermotaxis involves the detection of thermal changes created by animal movement in spatial thermogradient (0.5°C/cm), the magnitude of the expected thermal changes approximating 0.01°C/s [26]. The starvation impact on negative thermotaxis was shown to (i) involve an up-regulation of AWC cell activity, (ii) rely on INS1 neuropeptide produced in the intestine and (iii) to occur independently of ASI neurons. In contrast, our study used thermo-nociceptive stimuli, with faster raising thermal slopes (~0.5-2°C/s, hence 50-200 times faster than those occurring for thermotaxis) and covering noxious temperatures (up to 28°C). Our results indicate that the regulation of thermo-nociceptive response by starvation (i) is linked to a shift in the distribution of AWC activity response polarities from mostly excitatory to a mix of excitatory and inhibitory response, (ii) relies on ASI and specific neuropeptide produced in ASI, and (iii) works independently of INS-1 neuropeptide. Therefore, our study complements our understanding of the modulation of temperature-dependent behavior in C. elegans with previously undocumented mechanisms at the circuit, cellular and molecular levels.”

(2) ASI → AWC mechanism.

Because ASI is central to your conclusions, please expand on how ASI is thought to act on AWC and/or other neurons. If an additional ASI signal is proposed beyond INS-32/NLP-18, mark this as speculative unless further rationale can be provided, and adjust the model figure accordingly.

We have revised Figure 8 and its legend to clarify what is still hypothetical in the way ASI could affect AWC activity patterns and reversals. Note that the figure was also modified to integrate the conclusions made from epistasis analysis of eat-4 and flp-6.

(3) AWC response description.

The data support a shift in response distributions rather than a categorical switch from "deterministic to stochastic." Please adjust the language accordingly and provide a clear description of how traces were classified as "up, variable, or down," ideally with a quantification of the distributional shift.

We agree that the term “stochastic” can convey different things, and because it was used for something different for AWC in the past, we should have avoided it. We have revised the nomenclature. What we observe can indeed be better described as a shift in the response polarity distribution. The article was revised accordingly. We also included the quantitative analysis and histogram representation, suggested in one of the specific comments, and added detailed methodology on the categorization of traces.

When ASI is intact, we see a shift from mostly excitatory responses to an ~equal mix of excitatory and inhibitory responses (new Figure 4C-D). This effect is lost when ASI is ablated (new Figure 5C-D).

(4) Presentation and statistics.

In figure legends, indicate where datasets are replotted across panels and confirm that multiple-comparison corrections take account of repeated comparisons to the same controls.

We have included these details in the revised figure legends, and a statement in the method section.

(5) Methods clarity.

Provide justification for using 1-h off-food as the baseline, with quantification of baseline mobility/reversal rates. Expand the calcium-imaging methods to describe the processing pipeline (ΔR calculation, baseline period, drift correction), and add a brief rationale if the approach deviates from common normalization procedures. Clarify how cell ablations were performed and verified for specificity, and how cell-specific rescues were confirmed. Please also acknowledge the potential for developmental compensation with chronic ablation.

The justification of using 1hr off-food as baseline was made more prominent in the revised manuscript.

Revised result section:

“Starvation downregulates thermonociceptive responses in C. elegans

To assess how the feeding state modulates thermonociceptive behavior in C. elegans, we compared responses across different durations of food deprivation (Figure 1A). Synchronized first-day adult animals were stimulated with a series of 4-s infrared pulses of increasing heating power (100, 200, 300, 400 W), causing temperature increase of +2°C, +4°C +6°C and 8°C at the surface of the plate (Figure 1A). Fed animals on food produced robust heat-evoked reversal response to heat, but they also displayed a very elevated baseline of spontaneous reversals (~38%). A 1-hour off-food condition reduced spontaneous reversals (from ~38% to ~10%) and led to an attenuation of heat-evoked responses at low stimulus intensities, while responses to stronger stimuli remained comparable to those of fed animals. More prolonged food deprivation led to a striking progressive reduction in thermonociceptive responses at every heating level, with responses after 6 hours of starvation approaching baseline spontaneous reversal rates (Figure 1B and C). This suggests a robust inhibition of nociceptive behavior caused by prolonged starvation. To determine whether this attenuation was due to the absence of nutrients or chemosensory cues, we conducted similar starvation experiments in the presence of food odor, with OP50 bacteria present on the petri dish lid (Figure 1D). The reduction in thermonociceptive response persisted, indicating that the effect is driven by the internal starvation state rather than external olfactory input.

Although fed animals showed high sensitivity to noxious heat, they also displayed an elevated baseline of spontaneous reversals, which limited their utility as a control group by strongly reducing the dynamic range of heat-evoked reversal quantification and by complicating the quantitative comparison with food-deprivation conditions with much-reduced reversal baseline (Figure 1B). In addition, technical limitations in our calcium imaging setup would have prevented the intended follow-up analyses in fed animals. Based on these observations and technical considerations, we focused subsequent analyses, aiming at dissecting the circuit and molecular underpinnings of starvation-dependent plasticity, to the comparison of two off-food conditions with similar spontaneous reversal baseline: the early food deprivation condition (1-hour off-food, with high responsiveness to noxious heat) and the prolonged starvation (6-hour off-food with almost abolished noxious heat responsiveness).”

In addition, the method section was modified as follows:

- Calcium imaging details were added regarding ΔR calculation, baseline period, drift correction.

- We now explicitly refer to the original respective articles describing the neuroablation lines.

- We clarify that cell-specific transgene expression for rescue was confirmed using SL2::mCherry co-marker

In the result section, we now explicitly address potential developmental compensation in genetic ablation backgrounds in the result section as follows: “…one should keep in mind that potential indirect developmental effects might take place in neuro-ablation lines”.

Reviewer #1 (Recommendations for the authors):

(1) The data availability statement is missing from the reviewed manuscript and should be included.

Thanks, we have included the data availability statement in the revised manuscript.

(2) We request additional information on how n's were determined for individual experiments, as well as the inclusion of post-hoc power measurements for all quantification.

n were determined in agreement with previous studies using similar measures. No a priori power analyses were performed. A posteriori power analyses are not informative beyond the reported effect sizes and p-values (now reported in File S2). We clarified this in the statistical subsection of the method section.

(3) In many cases, the specific statistical tests used are not clear or justified; more details should be provided, including the non-post-hoc test used. Are all tests one-way ANOVAs? For comparisons across genotype and starvation duration, two-way ANOVAs would likely be more appropriate. Also, the authors switch between Bonferroni post-hoc tests and Holm-Bonferroni post-hoc tests. What determined the use of one versus another?

We have now clarified the statistical analyses used and provided full details in File S2. We have now more systematically applied two-way ANOVAs across all relevant analyses (with detailed parameters reported in File S2). When particularly relevant (e.g epistasis analysis between eat-4 and flp-6 mutations) the results of the two-way ANOVAs, is also explicitly stated in the result section.

We also note that all multiple-comparison corrections were performed using the Bonferroni method. Previous mentions of Holm-Bonferroni correction were inaccuracies, and we apologize for this confusion; these mentions have now been corrected throughout the manuscript.

(4) The use of heating power instead of the temperature experienced by the worms is an unwelcome abstraction. We strongly recommend revisiting that choice.

We do agree. We have revised the figures to label the axis with temperature increase.

(5) For calcium imaging, how are the traces categorized into "calcium up", "calcium down", or "no change"? Were those determined blindly - i.e., by individuals unaware of the experimental condition? Did the response direction need to be consistent across different temperatures? Did the change from baseline need to hit a specific threshold, consistent with previous studies in the field (i.e., +/- 3xSD for a minimum amount of time)? We encourage the authors to include these details in their methods section.

We have complemented the method section to clarify the criteria for the qualitative classification of traces. More importantly, new quantitative peak polarities comparisons were added (see specific points below and above, about histograms).

(6) For the experiments showing that exposure to food odor does not prevent response reduction, we suggest that feeding worms heat-killed bacteria would be a helpful control for the importance of bacterial nutritional status. In addition, showing that the impact of starvation was reversible with re-feeding would have been a useful experiment in line with standard experimental design in the starvation field.

Thanks, indeed with our current work we cannot pinpoint the role of additional sensory cues (except food odor) to be mediating starvation-evoked plasticity. Together with refeeding, these are all extremely interesting questions that we aim to answer and potentially link with ASI and AWC activity in our future work.

(7) For the various AWC rescue experiments, we found it curious that there wasn't an AWCon+off rescue, only each neuron individually.

Previous studies have identified similar or opposite responses of both AWCs for distinct sensory cues. Though our calcium imaging experiments point to both AWC on and off having similar response patterns to heat, we cannot rule out the possibility that their output (ability of control reversals) is distinct possibly due to recruited neuromodulators. Therefore, in the present work, we examined where these cell types act via the same or distinct combinations of neuromodulators to control reversals.

Reviewer #2 (Recommendations for the authors):

Experiments suggested:

(1) The authors should look into the Ca-dynamics in ASI.

How does the spontaneous and heat-evoked activity of ASI differ in fed, early food-deprivation and prolong starvation and its link to releases of neuromodulators, modified AWC activity to alter output of thermal nociception are very interesting questions. However, these questions are extremely exploratory (see argumentation above in response to the public review) and addressing them goes beyond the scope of our current manuscript.

(2) The authors should check AWC activity in ins-32 and nlp-18 mutant animals.

In this study, we focused on the roles of INS-32 and NLP-18 released from ASI in modulating heat-evoked reversals, as these mutants exhibit relatively strong behavioral phenotypes. However, these effects remain less pronounced than those observed following ASI ablation. In addition, we cannot exclude the contribution of additional signaling molecules, including INS-6 and other neuropeptides.

A comprehensive analysis of AWC activity in this context would require calcium imaging across multiple genetic backgrounds, including single, double, and potentially higher order peptide and receptor mutants, combined with cell-specific rescue experiments. While we appreciate the suggestion, such an approach would represent a substantial extension of the present work and will be important to pursue in future studies to further elucidate the underlying mechanisms.

(3) Short-term food deprivation completely eliminated heat heat-induced reversal response to 100W stimulus, while the response to 400W stimulus remained unaffected. This suggests fed, short-term starvation, and prolonged starvation are three distinct states, and authors should also test the response of AWC and ASI ablated animals in the fed conditions.

We agree that analyzing thermal nociception in fed states, in addition to short-term and prolonged food deprivation states is an important and interesting question, as these 3 conditions likely represent 3 distinct internal states that may recruit different neural pathways.

Several reasons led us to set the fed condition aside for this study, and we realize we insufficiently explain them in the initial manuscript. There are 2 main reasons.

(1) It is of paramount importance to consider the ‘baseline’ reversal rate (spontaneous reversals not triggered by heat, but visible in our dataset as the first point in the ‘dose-response’ curve). In Fed animals spontaneous reversal rate is very high (~38%) compared to the 1hr and 6hr food-deprivation conditions (>10%). This has two consequences: first a decreased dynamic range for quantify heat-evoked reversal, and, second, the difficulty in judging quantitative differences in heat-evoked reversals with such major differences in baseline reversals.

(2) Experimentally, assessing calcium responses in truly fed animals presents technical challenges. With our current setup, animals must be removed from food for at least ~5 minutes prior to recording (followed by ~5 minutes of imaging), which effectively corresponds to a “freshly starved” condition rather than a fully fed state. While previous studies have used serotonin to mimic aspects of the fed state, such manipulations can be difficult to interpret in this context.

A systematic comparison including fully fed animals, as well as AWC- and ASI-ablated conditions across these states, would be a valuable direction for future work, in particular once the methodological barriers associated with point 2, have been overcome.

We have clarified these choices in the result section as follows:

“Starvation downregulates thermonociceptive responses in C. elegans

To assess how the feeding state modulates thermonociceptive behavior in C. elegans, we compared responses across different durations of food deprivation (Figure 1A). Synchronized first-day adult animals were stimulated with a series of 4-s infrared pulses of increasing heating power (100, 200, 300, 400 W), causing temperature increase of +2°C, +4°C +6°C and 8°C at the surface of the plate (Figure 1A). Fed animals on food produced robust heat-evoked reversal response to heat, but they also displayed a very elevated baseline of spontaneous reversals (~38%). A 1-hour off-food condition reduced spontaneous reversals (from ~38% to ~10%) and led to an attenuation of heat-evoked responses at low stimulus intensities, while responses to stronger stimuli remained comparable to those of fed animals. More prolonged food deprivation led to a striking progressive reduction in thermonociceptive responses at every heating level, with responses after 6 hours of starvation approaching baseline spontaneous reversal rates (Figure 1B and C). This suggests a robust inhibition of nociceptive behavior caused by prolonged starvation. To determine whether this attenuation was due to the absence of nutrients or chemosensory cues, we conducted similar starvation experiments in the presence of food odor, with OP50 bacteria present on the petri dish lid (Figure 1D). The reduction in thermonociceptive response persisted, indicating that the effect is driven by the internal starvation state rather than external olfactory input.

Although fed animals showed high sensitivity to noxious heat, they also displayed an elevated baseline of spontaneous reversals, which limited their utility as a control group by strongly reducing the dynamic range of heat-evoked reversal quantification and by complicating the quantitative comparison with food-deprivation conditions with muchreduced reversal baseline (Figure 1B). In addition, technical limitations in our calcium imaging setup would have prevented the intended follow-up analyses in fed animals. Based on these observations and technical considerations, we focused subsequent analyses, aiming at dissecting the circuit and molecular underpinnings of starvationdependent plasticity, to the comparison of two off-food conditions with similar spontaneous reversal baseline: the early food deprivation condition (1-hour off-food, with high responsiveness to noxious heat) and the prolonged starvation (6-hour off-food with almost abolished noxious heat responsiveness).”

(4) The authors should test the effect of ins-1 in noxious heat-mediated dynamic reversal behavior.

We thank the reviewer for this valuable suggestion. We have now tested the phenotype of ins-1 mutants in our paradigm. Our data shows that INS-1 neuropeptide is not critical in mediating starvation-evoked thermonociceptive plasticity unlike plasticity in thermotaxis behavior (New Figure 6 Sup1). This molecular aspect adds to our initially presented evidence at the cell activity and circuit levels, that noxiousevoked reversal and thermotaxis behaviors are regulated in a clearly separable manner.

(5) Whether Glutamate and flp-6 work in parallel or in the same pathway to regulate reversals?

We thank the reviewer for this question. We tested eat-4; flp-6 double mutants and found:

(1) After short-term food deprivation (1hr), flp-6 and eat-4 separately contribute to heat-evoked reversal at high & low heat and they act in parallel pathways to explain ~90% of animal responsiveness (new version of Fig 3)

Corresponding new text:

“Next, we focused on eat-4 and flp-6 mutants, showing the strongest phenotype. We addressed whether glutamate and FLP-6 signaling act dependently of each other in controlling heat-evoked reversal, by testing eat-4; flp-6 double mutants. The residual response seen in each single mutant (Figure 3 A and B) was almost entirely abolished in the double mutant (Figure 3C). A two-way ANOVA for the highest heat stimuli with eat-4 and flp-6 genotypes as factors (two levels each: mutant or wild type) showed significant main effects of eat-4 (F_(1,67) =48.70, p<.001, η²p=0.421) and flp-6 (F_(1,67) =58.50, p<.001, ηp=0.466), respectively, but no interaction effects (F_(1,67) =0.093, p=.761, η²p=0.001). The significant cumulative effect of the two mutations indicates that the two signaling pathways act mostly independently of each other to mediate heat-evoked reversals.”

(2) After prolong starvation (6hr), flp-6 mutation has a dominant impact on plasticity and eat-4 mutation cannot cause loss of plasticity, pointing to a hierarchy in this context (new version of Fig. 6, including revised hierarchy in the model in panel G, and also revised model in Fig.

8).

Corresponding revised text:

“Second, we tested whether starvation-dependent plasticity was preserved in eat-4 and flp6 mutant backgrounds, which we had suggested to represent the main AWC transmitters controlling heat-evoked reversals under the early food deprivation condition (Figure 3). Even if the heat-evoked response upon early food-deprivation was reduced relative to wild type in flp-6 mutants, a significant further decline was seen after prolonged starvation (Figure 6B). These results indicate that starvation-dependent plasticity can operate independently of FLP-6. In contrast, eat-4 mutants displayed markedly elevated heat-evoked responses after prolonged starvation, even exceeding the response level seen in the early food deprivation condition for low heat stimuli (Figure 6C). This potentiated response in eat-4 mutants was entirely dependent of an intact FLP-6 signaling, since reversal responses in eat-4; flp-6 mutants were entirely abolished, like in flp-6 single mutant (Figure 6C-E, a two-way ANOVA indicating a significant interaction effect between the two mutations: F_(1,70) =0.093, p<.001, η²p=0.247). Moreover, the potentiated response in eat-4 single mutant could not be rescued by expressing eat-4 rescue transgene selectively in either AWC^OFF or AWC^ON neurons (Figure 6F). Interestingly, AWC^OFF-specific rescue produced a further potentiation of heat-evoked reversal response to high heat stimuli (Figure 6F, 6 and 8°C thermal increases), aggravating the phenotype of eat-4 mutants. These results are consistent with a model in which glutamatergic signaling regulates heat-evoked reversals in starved animals via two bidirectional drives (Figure 6G). On the one hand, glutamatergic signaling—originating from AWC^OFF—up-regulates reversals in response to high heat stimuli, thus contributing to prevent starvation-induced thermonociceptive plasticity. On the other hand, glutamatergic signaling—originating from neurons other than AWC— down-regulates reversals over a broad range of heat intensities, thus promoting starvation-induced thermonociceptive plasticity. The latter glutamatergic signaling inhibitory effect seems to be more dominant and to depend on intact FLP-6 signaling.”

(6) The authors should perform flp-6 and eat-4 mutant/rescue experiments in the nsy-1 and nsy-7 background to clarify the results.

Our results indicate that glutamate release via EAT-4 from both AWC^ON and AWC^OFF, as well as FLP-6 from AWC^OFF, contributes to heat-evoked reversals regulation. The experiments suggested by the reviewer would, in principle, provide further insight into the interaction between AWC subtype identity and the respective roles of glutamatergic and peptidergic signaling.

However, as discussed in more details above in the public review, the extent and nature of AWC^ON/OFF remodeling in nsy-1 and nsy-7 mutant backgrounds remain incompletely understood. This introduces significant uncertainty in interpreting results obtained from combining these mutations with eat-4 and flp-6 manipulations. As a result, such experiments would be difficult to interpret in a definitive manner at this stage.

We therefore consider this an important direction for future work, once the roles of nsy1 and nsy-7 in AWC subtype specification and function are more clearly established. As our preliminary results with nsy-1 and nsy-7 mutants added more confusion than clarity, we have chosen to set them aside (former Fig. 3-figure supplement 2 has been removed).

Minor comments:

(1) What is food odor? The experiment should be clearly mentioned.

Thanks for spotting this unintended omission. Food odor experiments were performed by adding OP50 bacteria on the inward side of the petri dish lid instead of the NGM surface. We have added this description in the method section of the revised manuscript.

(2) Panel 3C is coming before 3B. This should be rearranged.

Thanks for pointing this out. Panel arrangement was entirely reorganized in revise Fig. 3, with the addition of eat-4 x flp-6 genetic interaction analysis.

(3) In Figure 6, if the panels are arranged horizontally, it would be easier to follow.

Thanks for pointing this out. Panel arrangement was entirely reorganized in revise Fig. 6, with the addition of eat-4 flp-6 genetic interaction analysis.

Reviewer #3 (Recommendations for the authors):

(1) The authors should consider moving measurements of AFD-ablated animals into the main Figure 1. AFD is a well-known thermosensor, and it is worth showing that responses to noxious thermal stimuli persist in animals lacking AFD.

Thank you for this suggestion. We have moved measurements of AFDablated animals to the main figure (revised Fig. 2).

(2) AFD ablation does affect responses to noxious heat. The authors could consider ablating/silencing AFDs and AWCs simultaneously to determine whether these two neurontypes account for the behavior.

We agree that investigating the combinatorial contributions of thermosensory neurons, including AFD and AWC, to thermal nociception is an important and interesting question. In principle, simultaneous ablation or silencing of these neuron types could indeed reveal unexpected interactions.

In our experimental paradigm, however, we observe only a minimal contribution of AFD neurons to heat-evoked reversals, whereas ablation of AWC nearly abolishes the response. Based on these observations, we chose to focus the present study on AWC, which appears to play a more prominent role in this behavior.

A more detailed dissection of the potential interactions between AFD and AWC, including combinatorial manipulations, would be a valuable direction for future work. In particular, the possibility that AFD exerts a modulatory influence remains an interesting hypothesis to explore.

(3) Given that EAT-4/VGLUT and FLP-6 neuropeptides each contribute to nociception, the authors should consider testing an eat-4; flp-6 double mutant to determine whether this combination of neurochemical signals accounts for AWC signaling to downstream circuits.

We thank the reviewer for this suggestion, which is similar to point 5 of Reviewer 2 (above).

We tested eat-4; flp-6 double mutants and found:

(1) After short-term food deprivation (1hr), flp-6 and eat-4 separately contribute to heat evoked reversal at high & low heat and they act in parallel pathways to explain ~90% of animal responsiveness (new version of Fig 3)

Corresponding new text:

“Next, we focused on eat-4 and flp-6 mutants, showing the strongest phenotype. We addressed whether glutamate and FLP-6 signaling act dependently of each other in controlling heat-evoked reversal, by testing eat-4;flp-6 double mutants. The residual response seen in each single mutant (Figure 3 A and B) was almost entirely abolished in the double mutant (Figure 3C). A two-way ANOVA for the highest heat stimuli with eat-4 and flp-6 genotypes as factors (two levels each: mutant or wild type) showed significant main effects of eat-4 (F_(1,67) =48.70, p<.001, η²p=0.421) and flp-6 (F_(1,67) =58.50, p<.001, η²p=0.466), respectively, but no interaction effects (F_(1,67) =0.093, p=.761, η²p=0.001). The significant cumulative effect of the two mutations indicates that the two signaling pathways act mostly independently of each other to mediate heat-evoked reversals.”

(2) After prolong starvation (6hr), flp-6 mutation has a dominant impact on plasticity and eat-4 mutation cannot cause loss of plasticity, pointing to a hierarchy in this context (new version of Fig. 6, including revised hierarchy in the model in panel G, and also revised model in Fig. 8).

Corresponding revised text:

“Second, we tested whether starvation-dependent plasticity was preserved in eat-4 and flp6 mutant backgrounds, which we had suggested to represent the main AWC transmitters controlling heat-evoked reversals under the early food deprivation condition (Figure 3). Even if the heat-evoked response upon early food deprivation was reduced relative to wild type in flp-6 mutants, a significant further decline was seen after prolonged starvation (Figure 6B). These results indicate that starvation-dependent plasticity can operate independently of FLP-6. In contrast, eat-4 mutants displayed markedly elevated heat-evoked responses after prolonged starvation, even exceeding the response level seen in the early food deprivation condition for low heat stimuli (Figure 6C). This potentiated response in eat-4 mutants was entirely dependent of an intact FLP-6 signaling, since reversal responses in eat-4; flp-6 mutants were entirely abolished, like in flp-6 single mutant (Figure 6C-E, a two-way ANOVA indicating a significant interaction effect between the two mutations: F_(1,70) =0.093, p<.001, η²p=0.247). Moreover, the potentiated response in eat-4 single mutant could not be rescued by expressing eat-4 rescue transgene selectively in either AWC^OFF or AWC^ON neurons (Figure 6F). Interestingly, AWC^OFF-specific rescue produced a further potentiation of heat-evoked reversal response to high heat stimuli (Figure 6F, 6 and 8°C thermal increases), aggravating the phenotype of eat-4 mutants. These results are consistent with a model in which glutamatergic signaling regulates heat-evoked reversals in starved animals via two bidirectional drives (Figure 6G). On the one hand, glutamatergic signaling—originating from AWC^OFF—up-regulates reversals in response to high heat stimuli, thus contributing to prevent starvation-induced thermonociceptive plasticity. On the other hand, glutamatergic signaling—originating from neurons other than AWC— down-regulates reversals over a broad range of heat intensities, thus promoting starvation-induced thermonociceptive plasticity. The latter glutamatergic signaling inhibitory effect seems to be more dominant and to depend on intact FLP-6 signaling.”

(4) The authors should consider representing AWC responses to thermal stimuli as histograms to illustrate how fasting increases the probability of some responses and decreases the probability of others.

We thank this reviewer for the suggestion. The proposed histograms nicely convey the concept of “shift in response polarity distribution” that we observed (using the new terminology we now use, instead of using the term “stochastic”). To create such histograms, we computed the magnitude of the peaks on a trial-by-trial basis. When ASI is intact, we see a shift from mostly excitatory responses to an ~equal mix of excitatory and inhibitory responses (new Figure 4C-D). This effect is lost when ASI is ablated (new Figure 5C-D).

(5) It seems important to better understand the ins-6 mutant phenotype and determine whether ASI-to-AWC signaling involves this insulin-like peptide (ILP). The authors should consider using some of the tools available for disrupting ILP signaling to more clearly demonstrate that a specific neurochemical signal mediates modulation of AWCs by ASIs.

Our work identified two ASI-expressed neuropeptides that function to decrease reversal response after starvation: INS-32 and NLP-18. We initially set a lower priority on INS-6 because the reversal response level in starved mutants appeared lower than that in nlp-18 and ins-32. It is important to note that ins-32 and nlp-18 are not ‘generally potentiated’ mutants, but display reversal up-regulation selectively following starvation, which placed them as strong candidates to selectively mediate ASI regulation. This said, it is also true that these two mutants (and ins-6 too) display reduced responsiveness at the early food deprivation time point. Therefore, none of the neuropeptide mutants was strictly identical to ASI, suggesting that the peptides might also work via non-ASI cells at the early food deprivation timepoint (as follow up data indicated at least for nlp-18).

Following this reviewer’s comment (and the similar one in the public review), we have attempted to complement our story with the idea of using a similar approach and rescue ins-6 with its endogenous promoter or ASI-specific promoter. Unfortunately, we failed to obtain rescue effects, and therefore these data remain inconclusive (as we cannot guarantee that the rescue constructs were functional). We decided to keep these data aside in the revised manuscript. Globally, our point made graphically in Figure 7F remains valid. We have complemented the figure legend to mention that INS6 could also potentially work from ASI, but it is not depicted as no ASI-specific data are available. In summary, our data suggests that the connection between ASI and AWC(s) might be established by the integrated action of multiple peptides and their receptors. Further calcium imaging experiments in single, double and potentially triple mutant(s) of peptides and receptors would be required to go deeper in this question, which could be performed in future work.

Author response:

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

We thank the three reviewers for their encouraging and constructive comments. We have addressed them by increasing clarity of the writing and adding details to the methods section that were previously missing or not stated clearly enough. We have included additional experimental data. Specifically, we tested how the osmotic effect of lactulose depends on lactulose dosage and colonization state, added data on cecum sizes of mice with different microbiomes, and tested how lactulose treatment in the active phase affects feeding behavior.

Public Reviews:

Reviewer #1 (Public Review):

Greter et al. provide an interesting and creative use of lactulose as a "microbial metabolism" inducer, combined with tracking of H2 and other fermentation end products. The topic is timely and will likely be of broad interest to researchers studying nutrition, circadian rhythm, and gut microbiota. However, a couple of moderate to major concerns were noted that may impact the interpretation of the current data:

(1) Much of the data relies on housing gnotobiotic mice in metabolic cages, but I couldn't find any details of methods to assess contamination during multiple days of housing outside of gnotobiotic isolators/cages. Given the complexity of the metabolic cage system used, sterility would likely be incredibly challenging to achieve. More details needed to be included about how potential contamination of the mice was assessed, ideally with 16S rRNA gene sequencing data of the endpoint samples and/or qPCR for total colonization levels relative to the more targeted data shown.

We thank the reviewer for pointing out that we have not made the experimental setup clear in the text. One of the unique features of our metabolic cage setup is that the mice do not need to be housed outside gnotobiotic isolators, but that the whole system is placed inside an isolator. We have developed and published this system recently (Hoces et al, PLOS Biol 2022), including extensive testing for sterility/gnotobiosis. We have now adapted the main text to increase clarity on this issue (lines 76ff).

Given that 16S sequencing of germ-free mice will typically produce false-positive reads, we used Blautia pseudococcoides as an indicator strain for contamination. This strain is present in our SPF mouse colony, forms spores that are highly resilient to decontamination measures, and has been the most likely contaminant in our gnotobiotic system. We have checked for presence of this strain in the cecum content of all our animals at the end of each experiment, and only included experiments which had a B. pseudococcoides signal below threshold level. We have now added this information to the methods section (lines 389ff).

(2) The language could be softened to provide a more nuanced discussion of the results. While lactulose does seem to induce microbial metabolism it also could have direct effects on the host due to its osmotic activity or other off-target effects. Thus, it seems more precise to just refer to lactulose specifically in the figure titles and relevant text.

We have adapted all figure legends to not contain interpretations, but rather state what was done in the experiments shown in the figures. We have also adapted the text in multiple places to soften the language and avoid overinterpretation of our experimental results.

Additionally, the degree to which lactulose "disrupts the diurnal rhythm" isn't clear from the data shown, especially given that the markers of circadian rhythm rapidly recover from the perturbation. It is probably more precise to instead state that lactulose transiently induces fermentation during the light phase or something to that effect.

We tried to make the argument that what we call disruption of the diurnal rhythm is acute, meaning that it is not disrupting the rhythm "chronically" (i.e., for longer), but that it recovers rapidly from this transient disruption. Given the confusion this wording is causing we are introducing this conceptually in the new version of the manuscript (lines 56ff).

The discussion could also be expanded to address what methods are available or could be developed to build upon the concepts here; for example, the use of genetic inducers of metabolism which may avoid the more complex responses to lactulose.

We also appreciate the mention of concepts from our study that can be built on in future studies, and we added a paragraph on potential further research. (lines 301ff).

Despite these concerns, this was still an intriguing and valuable addition to the growing literature on the interface of the microbiome and circadian fields.

We thank the reviewer for all their encouraging and constructive remarks!

Reviewer #2 (Public Review):

Summary:

The authors aimed to investigate how microbial metabolites, such as hydrogen and short-chain fatty acids (SCFAs), influence feeding behavior and circadian gene expression in mice. Specifically, they sought to understand these effects in different microbial environments, including a reduced community model (EAM), germ-free mice, and SPF mice. The study was designed to explore the broader relationship between the gut microbiome and host circadian rhythms, an area that is not well understood. Through their experiments, the authors hoped to elucidate how microbial metabolism could impact circadian clock genes and feeding patterns, potentially revealing new mechanisms of gut microbiome-host interactions.

Strengths: 

The manuscript presents a well-executed investigation into the complex relationship between microbial metabolites and circadian rhythms, with a particular focus on feeding behavior and gene expression in different mouse models. One of the major strengths of the work lies in its innovative use of a reduced community model (EAM) to isolate and examine the effects of specific microbial metabolites, which provides valuable insights into how these metabolites might influence host behavior and circadian regulation. The study also contributes to the broader understanding of the gut microbiome's role in circadian biology, an area that remains poorly understood. The experiments are thoughtfully designed, with a clear rationale that ties together the gut microbiome, metabolic products, and host physiological responses. The authors successfully highlight an intriguing paradox: the significant influence of microbial metabolites in the EAM model versus the lack of effect in germ-free and SPF mice, which adds depth to the ongoing exploration of microbial-host interactions. Despite some methodological concerns, the manuscript offers compelling data and opens up new avenues for research in the field of microbiome and circadian biology.

We thank the reviewer for their encouraging remarks, specifically on the surprising findings that microbial metabolism seems to affect circadian clock gene expression and behavior differently in EAM and SPF mice.

Weaknesses:

The manuscript, while providing valuable insights, has several methodological weaknesses that impact the overall strength of the findings. First, the process for stool collection lacks clarity, raising concerns about potential biases, such as the risk of coprophagia, which could affect the dry-to-wet weight ratio analysis and compromise the validity of these measurements.

We thank the reviewer for pointing out that our description of the specific methods used for collecting feces were presented in a somewhat confusing manner. In short, dry and wet faecal weights were determined based on fecal pellets that were freshly produced and directly collected from restrained mice. To determine total fecal output over time, we collected all fecal pellets produced in a 5-hour window in a cage, determined their dry weight, and then used the water content determined for fresh faeces to calculate wet weight. Using this method, we cannot account for potential differences in coprophagia between the groups. However, this is not likely to affect the dry-to-wet ratio of faecal output in our results. We have now adapted the section in the methods to increase clarity (lines 440ff), and changed the quantity shown in Figure S2C and E to "water content", which is a more intuitive measure for the same thing.

Additionally, the use of the term "circadian" in some contexts appears inaccurate, as "diurnal" might be more appropriate, especially given the uncertainty regarding whether the observed microbiome fluctuations are truly circadian.

Similarly to our answer to reviewer 1 above, we appreciate this remark about imprecise language and have addressed this issue in the text and the figure legends. Indeed, we do not think the fluctuations in microbiota activity are truly circadian, but likely a result of the entrainment through the host's food intake.

Another significant issue is the unexpected absence of an osmotic effect of lactulose in EAM mice, which contradicts the known properties of lactulose as an osmotic laxative. This finding requires further verification, including the use of a positive control, to ensure it is not artifactual.

This is a good point. We have used this lactulose dosage specifically to induce microbial metabolism without causing osmotic diarrhoea and went to some lengths do demonstrate this (FigureS2C-E). In response to this comment (and one by reviewer 3 below about transit time), we have now performed additional experiments using higher lactulose dosage (new FigureS3). Our results indicate that the effect of lactulose on water content and transit time depends on microbiota complexity, with no change in fecal water content in 3MM mice even when treated with higher lactulose doses, and a stronger change in SPF mice. We now address this in the main text (lines 127ff).

The presentation of qRT-PCR data as log2-fold changes, with a mean denominator, could introduce bias by artificially reducing variability, potentially leading to spurious findings or increased risk of Type I error. This approach may explain the unexpected activation of both the positive and negative limbs of the circadian clock.

While we agree that our description of the qPCR method used for measuring circadian clock gene expression was lacking detail, we do not see how our analysis would lead to an increased risk of Type 1 error.

Briefly, we use the standard ΔΔCt method to analyze our RT-PCR results. We first normalize gene expression values for each gene of interest to an internal housekeeping gene. Then, we use these normalized values to compare gene expression values in treatment vs control groups (or to the control group at time point 0 in the case of Figure 3C). We then use a log2 transformation to convert the logarithmic RT-PCR values to fold changes. We apologize for the confusing labeling in the figures, where we called the values "log2(fold changes)", which we have now changed to "log2(ΔΔCt) of expression" in Figures 3B, C and S4.

The simultaneous activation of both limbs of the circadian clock is indeed a surprising result and somewhat complicates interpreting the effect of lactulose treatment on clock gene expression. We take it as evidence that it generally interferes with clock gene expression, while a clearer understanding of the effects would require further research.

Moreover, the lack of detailed information on the primers and housekeeping genes used in the experiments is concerning, particularly given the importance of using non-circadian housekeeping genes for accurate normalization.

It seems like the resource table describing these important experimental details was omitted in the original submission. We have now included it in the revised version (Table S1).

The methods for measuring metabolic hormones, such as GLP-1 and GIP, are also not adequately described. If DPP-IV/protease inhibitor tubes were not used, the data could be unreliable due to the rapid degradation of these hormones by circulating proteases.

We thank the reviewer for pointing out this omission. We have now added details of how we measured the metabolic hormones to the methods section, including the fact that we have added a DPP-IV inhibitor to the tubes at sampling (lines 469ff).

Finally, the manuscript does not address the collection of hormone levels during both fasting and fed phases, a critical aspect for interpreting the metabolic impact of microbial metabolites.

While we agree that it would be interesting to measure hormone levels also in the fed phase, a more thorough examination of hormone levels over the diurnal cycle, as suggested by reviewer 3, would be relevant for a full-scale follow-up. Given our data, we of course cannot exclude that there may be time-point-specific differences and therefore have softened the language around this conclusion to state that hormone levels are not acutely changed after a lactulose intervention at the time-points examined. (lines 318ff).

These methodological concerns collectively weaken the robustness of the study's results and warrant careful reconsideration and clarification by the authors.

Because of these weaknesses, the authors have partially achieved their aims by providing novel insights into the relationship between microbial metabolites and host circadian rhythms. The data do suggest that microbial metabolites can significantly influence feeding behavior and circadian gene expression in specific contexts. However, the unexpected absence of an osmotic effect of lactulose, the potential biases introduced by the log2-fold change normalization in qRT-PCR data, and the lack of clarity in critical methodological details weaken the overall conclusions. While the study provides valuable contributions to understanding the gut microbiome's role in circadian biology, the methodological weaknesses prevent a full endorsement of the authors' conclusions. Addressing these issues would be necessary to strengthen the support for their findings and fully achieve the study's aims.

We thank the reviewer again for their careful and critical reading of our work, and for their constructive input. In the revised version of our manuscript, we address the reviewer's concerns by providing more methodological detail and additional experimental data.

Despite the methodological concerns raised, this work has the potential to make a significant impact on the field of circadian biology and microbiome research. The study's exploration of the interaction between microbial metabolites and host circadian rhythms in different microbial environments opens new avenues for understanding the complex interplay between the gut microbiome and host physiology. This research contributes to the growing body of evidence that microbial metabolites play a crucial role in regulating host behaviors and physiological processes, including feeding and circadian gene expression.

We thank the reviewer for their encouraging remarks!

Reviewer #3 (Public Review):

Summary:

In the manuscript by Greter, et al., entitled "Acute targeted induction of gut-microbial metabolism affects host clock genes and nocturnal feeding" the authors are attempting to demonstrate that an acute exposure to a non-nutritive disaccharide (lactulose) promotes microbial metabolism that feeds back onto the host to impact circadian networks. The premise of the study is interesting and the authors have performed several thoughtful experiments to dissect these relationships, providing valuable insights for the field. However, the work presented does not necessarily support some of the conclusions that are drawn. For instance, lactulose is administered during the fasting period to mimic the impact of a feeding bout on the gut microbiota, but it would be important to perform this treatment during the fed state as well to show that the effects on food intake, etc. do not occur.

We thank the reviewer for this important point. In the revised version, we include an experiment where we administer lactulose during the fed state and do not observe a significant change in food intake. We describe this in the text (lines 189ff) and in the new Figure S5C and D.

To truly draw the conclusion that the current outcomes are directly connected to and mediated via an impact on the host circadian clock, it would be ideal to perform these studies in a circadian gene knock-out animal (i.e., Cry1 or Cry2 KO mice, or perhaps Bmal-VilCre tissue-specific KO mice). If the effects are lost in these animals, this would more concretely connect the current findings to the circadian clock gene network.

We agree that these would be interesting experiments to follow up on the question how the observed effects are actuated by host functions. However, they would require a large amount of preparatory work (including rederiving the KO mice to get them germ-free in our gnotobiotic facility), we argue that they are beyond the scope of this study.

Despite these reservations, the work is promising.

We thank the reviewer for their encouraging assessment.

Strengths:

Attempting to disentangle nutrient acquisition from microbial fermentation and its impact on diurnal dynamics of gut microbes on host circadian rhythms is an important step for providing insights into these host-microbe interactions.

The authors utilize a novel approach in leveraging lactulose coupled with germ-free animals and metabolic cages fitted with detectors that can measure microbial byproducts of fermentation, particularly hydrogen, in real-time.

The authors consider several interesting aspects of lactulose delivery, including how it shifts osmotic balance as well as provides calculations that attempt to explain the caloric contribution of fermentation to the animal in the context of reduced food intake. This provides interesting fundamental insights into the role of microbial outputs on host metabolism.

Thank you!

Weaknesses:

While the authors have done a large amount of work to examine the osmotic vs. metabolic influence of lactulose delivery, the authors have not accounted for the enlarged cecum and increased cecal surface area in germ-free mice. The authors could consider an additional control of cecectomy in germ-free mice.

We thank the reviewer for pointing out the potential effect of the anatomical differences of germ-free and conventionally colonized mice. We agree that when comparing germ-free mice to SPF mice, the enlarged cecum area in germ-free animals could lead to differences in water release or uptake. However, this difference is smaller in gnotobiotic mice colonized with our minimal microbiota, even though their ceca are still slightly smaller than those of germ-free mice (new Figure S2F). While we agree that including control of cecectomy in germ-free mice could be interesting, we do not have the option of doing surgery on germ-free mice given our current experimental setup. We have now added information on cecum weight, a good proxy for cecum size, in the new Figure S2F done.

The authors have examined GI hormones as one possible mechanism for how food intake is altered by microbial fermentation of lactulose. However, the authors measure PYY and GLP-1 only at a single time point, stating that there are no differences between groups. Given the goal of the studies is to tie these findings back into circadian rhythms, it would be important to show if the diurnal patterns of these GI hormones are altered.

We fully agree that a deeper investigation of the diurnal fluctuations of hormone levels would be an interesting next step in studying whether perturbations in food intake can disturb these rhythms. Doing this for the whole rhythm would really require a full second study.

In response to the reviewer's comments, we have changed the statements made around these data to point out just that hormone level fluctuations could not be detected during specific time points after lactulose treatment and therefore do not seem to explain the imminent behavioral changes (lines 318ff).

Considerations of other factors, such as conjugated vs. deconjugated bile acids, microbial bile salt hydrolase activity, and bile acid resorption, might be an important consideration for how lactulose elicits more influence on ileal circadian clock genes relative to cecum and colon.

We absolutely agree that investigation of microbial bile acid modification and their metabolism by the host would be an interesting topic for a follow-up study.

Measurements of GI transit time (both whole gut and regional) would be an important for consideration for how lactulose might be impacting the ileum vs. cecum vs. colon.

This is also an interesting point. While we did not add an experiment in which we specifically measure transit time to the revised version, we now measure total faecal output in a 5 h time period after PBS or lactulose treatment (Figure S3C). Faecal output is known to be a good proxy for transit time, and we see no significant difference between lactulose treatment (even with a two-fold higher dose than used before, new Figure S3) and PBS treatment.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Line 126 - see the point in the public review, this data argues against disrupting the rhythm.

See our response above

(2) Line 156 - the metric used for water content is confusing. Why not just subtract dry weight from wet weight to get water content? The ratio is much harder to think about for me. Perhaps more importantly, this data is very confusing given that colonization seems to impact the activity of lactulose, which complicates the interpretation. Could be an interesting area for future study that you might highlight more in the discussion.

We thank the reviewer for pointing out that our presentation of water content could be clearer. We have changed the dry/wet ratio we have used in the previous version to the "water fraction" (new Figure S2C, E; new Figure S3A,B), i.e., the per cent of weight of the wet sample that is made up by water. We would argue that this is a measurement that is easier to interpret than the difference suggested by the reviewer, because it is independent of the absolute sample weight.

We also agree that it is surprising that colonization state changes the osmotic state of the gut environment and have now added text discussing that (lines 127ff).

(3) Line 188 - the lack of expression changes in the distal gut (cecum/colon) potentially conflicts with the model, warranting additional discussion/qualifications. Is lactulose getting metabolized in the small intestine? Alternatively, does lactulose have a direct effect on the host? The current text seems to imply that lactulose is fermented in the colon, the fermentation products are absorbed, and then they only impact the ileum through circulation, which doesn't seem physiologically possible.

It is possible that lactulose affects small intestinal tissue directly, but we show that the effect depends on microbial activity. Microbial activity is much larger in the large intestine than in the small intestine, which is why we hypothesize that it acts through systemic signals rather than locally. These systemic signals might be fermentation products impacting the ileum through circulation. We would argue that this is not implausible, given that there are well-documented systemic effects of fermentation products in circulation (e.g., den Besten et al, 2013). It is, however, also possible that, e.g., metabolism of fermentation products in the liver triggers a secondary signal that acts systemically.

(4) Line 241 - need to weaken this sub-heading. The experimental design shows that fermentation products impact feeding behavior, but this does not necessarily imply that fermentation products are responsible for the lactulose effect.

Done.

(5) Line 256 - The lack of an effect in SPF mice is surprising and potentially conflicts with the model proposed. Given this and other confusing results (gene expression site specificity, osmolarity effects, etc) it seems prudent to be more cautious as to the potential mechanisms through which lactulose supplementation impacts host gene expression and feeding behavior, which would likely require a lot more experiments to provide a definitive answer.

While the lack of an effect in SPF mice is surprising, we would argue that this is rather points towards the need for a better understanding of host-microbiota-diet interactions than a conflict with our interpretation. We do agree with the reviewer that more work is necessary for providing definitive proof of the underlying mechanisms of the observed effects and have adapted the language throughout the text.

(6) Line 260 - A lot of text is devoted to the potential caloric effects of the fermentation products and the lactulose itself. Was this in response to a prior reviewer? Either way, it seems too speculative to me and I would recommend trimming it down and moving it to the discussion.

We have rewritten this section to make it more concise and increase readability (lines 224ff).

(7) Line 305 - Not fasting, just lower caloric intake, as shown by Figure 1c.

We have changed the text to reflect that.

(8) Line 371 - Too definitive given the current data. Need to qualify the interpretation here.

We have adapted the text and qualified the interpretation.

(9) Figure 2 - Need to revise the title, no data showing that the rhythm is disrupted.

Done.

(10) Figure 3b - Clarify what timepoint is shown in the legend.

Done.

(11) Figure 3c - label when the treatment started. Consider changing to 2-way ANOVA which is probably more appropriate than t-tests.

We have added information on treatment start to the figure legend and have changed the statistical analysis to a two-way ANOVA (time, treatment).

(12) Figure 4c - move to supplement as this negative data isn't sufficient to rule out an impact on the hypothalamus or liver. Even when only considering transcript levels it's possible that the timepoint is just not ideal.

We agree that this data only represents a snapshot of gene expression at one timepoint after treatment and does not rule out involvement of hypothalamus or liver in this process. We have now moved the previous Figure 4C to the supplementary information (new Figure S6A).

(13) Figure 5 - defined the "fermentation products" and their concentrations in the legend. Consider moving panels d, and e to the supplement - negative results with unclear interpretation. Clarify in the legend how many calories/g were assumed for the fermentation products and provide a scientific rationale for this decision. Modify the title to be more cautious - as discussed above.

We thank the reviewer for pointing out that this was not clear. We have now added the formulation of the fermentation products to the figure legend and moved panels D and E to the supplement. We have also combined the former Figures 4AB and 5ABC into the new Figure 4.

(14) Figure S1 - The patterns in panel a are really intriguing and could be discussed more. For example, what do you think is driving the rapid oscillations in E. rectale?

We agree that the patterns are potentially interesting, but the fact that the patterns we observe do not replicate well between the two light-dark cycles we monitor suggest a large contribution of experimental noise. We therefore refrain from interpreting too much into this dataset.

(15) Figure S2 - Could changing the metric for water content be more easily interpretable? Modify the title to better match the data shown.

We thank the reviewer for pointing that out. We have now changed the metric in Figure S2 (and the new Figure S3) to % water in feces/cecum content, which is easier to interpret.

(16) Figure S3 - need to specify the multiple testing correction used.

Done.

(17) Figure S4 title - replace "inducing microbial metabolism" with "lactulose".

Done.

(18) Figure S5 title - modify to weaken the causal claim.

We have adapted all figure titles to conform to this comment.

Reviewer #2 (Recommendations For The Authors):

Greter and colleagues present an insightful manuscript investigating the effects of microbial metabolites, such as hydrogen and SCFAs, on feeding behavior and circadian gene expression at a single time point. Notably, they observed that these metabolites exert a significant influence on behavior in a reduced community model (EAM). However, this effect was not evident in germ-free or SPF mice, highlighting an intriguing paradox. The manuscript is well-written, with experiments that are thoughtfully designed and clearly rationalized. The study contributes valuable data to the poorly understood relationship between the gut microbiome and host circadian rhythms. While I find the manuscript compelling, I believe that providing additional experimental and analytical details would enhance clarity and rigor.

Major Comments:

(1) Additional clarity is needed regarding the stool collection process. Were the samples collected as fresh specimens, or was there a possibility of coprophagia before collection? Clarification on this point is important, as it could impact the results, particularly the dry-to-wet weight ratio analysis. Ensuring the collection process did not introduce this bias is crucial for the validity of these measurements.

Thank you for pointing out that this was not stated clearly. Wherever we assessed water content in faeces, we used fresh samples that were directly collected from a live animal and immediately frozen in a closed container or analyzed. When we assessed total faecal output, we collected the total bedding from a cage, sorted out the faecal pellets, and only measured dry weight. Total wet weight output was then assessed by using the water content of fresh faeces of animals with the same microbiota and the same treatment as a correction factor. We have now made this clear in the methods section (lines 435ff).

In cases where we performed total output measurements by collecting bedding, there was the possibility for coprophagia. We did not control for this but assumed that coprophagia will have a small effect that is likely similar between groups and should thus not affect the comparison.

(2) Caution is advised in the use of the term 'circadian,' which is sometimes used when 'diurnal' might be more appropriate. For example, the title of the first results section could be revised to 'Host Feeding [or Diurnal] Rhythms Influence Microbial Metabolic Fluctuations.' Additionally, line 357 should likely use 'diurnal' instead of 'circadian.' It's important to note that 'circadian' implies that cyclical fluctuations would persist without environmental cues (e.g., feeding). Since it's not clear whether most microbiome compositional or functional fluctuations are truly circadian, 'diurnal' is likely the more accurate term.

We thank the reviewer for pointing out our imprecise use of the term circadian. We have now adapted this throughout the manuscript.

(3) The lack of an osmotic effect of lactulose in EAM mice is quite surprising, given that lactulose is known to be an osmotic laxative. Was this finding specific to EAM mice, or was a similar lack of osmotic effect observed in SPF mice? A positive control is necessary to verify that this unexpected result is not artifactual. If there is no osmotic laxative effect in SPF mice, an explanation is needed as to why this medication is not functioning as expected in these mice.

This is a good point. While we initially thought that the lack of an osmotic effect was due to the specific lactulose dose we were using, we also did not observe an osmotic effect (measured by the water content of fresh faecal pellets produced after treatment) when we used twice the amount of lactulose in EAM mice (new Figure S3). However, in SPF mice, we did see an increase in faecal water content after treatment. This intriguing result suggests that the effect of lactulose as an osmotic laxative depends on the presence of a complex microbiota. We now show this data in the new Figure S3A and discuss it in the text (lines 127ff).

(4) The authors state that 'To account for faulty measurements due to disruptive events and for measurement noise, some datapoints were excluded from the raw datasets.' It would be important for the authors to confirm that this data exclusion was unbiased, meaning it did not disproportionately affect one group over another, and that any exclusions affected groups randomly.

This is a good point, and we analyzed this for the experiments we show in Figs 4A/S5A, 4B/S5E, 4C, and S5F, and discuss this in the methods part (lines 493ff). The resulting statistics is not fully conclusive: using a Chi-square test to check whether the probability of excluding values differs between experiments, we get significant differences (p=3.9 x 10^-18). We would, however, argue that this is not surprising, as different experiments sometimes different in the number of times we needed to do maintenance work on the isolators, which could lead to actuation of the scales measuring feed values, and thus faulty measurements.

We face the same problem within experiments: we found a significant difference in the probability to exclude values between treatment and control in the experiment shown in Figs 4A/S5A (p=1.7 x 10^-6), but no significant differences in the experiments in Figs 4B/S5E and S5F (p=0.71, and p=0.10, respectively). While it is hard to strictly exclude an influence of our data exclusion strategy, these findings speak against a systematic effect of treatment.

(5) The authors should provide details on the primers and housekeeping genes used in their experiments. It's crucial that the housekeeping gene is not circadian and is stable at all time points (PMID 17878933).

In the previous submission, the main resources table was omitted by accident. We have now added it (Table S1), including details on the primers and reagents used for all experimental work.

(6) The presentation of qRT-PCR data as log2-fold change is confusing. It's unclear what the numerator and denominator represent for this ratio or why such normalization was deemed necessary. Ideally, transcripts should be normalized to a housekeeping gene (as noted in a previous comment), not to a baseline measure of other same genes acquired from other mice. Log2-fold change is typically appropriate when comparing two measures from the same mice; however, in this study, the mice were euthanized, and the denominator is a mean of genes measured from other samples. This approach could introduce bias and might explain why both the positive and negative limbs appear to be activated by the microbial metabolites. It would be more rigorous to present these values as absolute gene expression levels.

We thank the reviewer for pointing out that this was not described clearly in the previous version of our manuscript. We have now adapted the methods part to explain that all data showing RT-PCR data is normalized to a housekeeping gene. Only after that, we compare the gene expression levels of the treatment group to the control group (or to gene expression of the control group at timepoint 0 in the case of Figure 3C).

(7) The use of log-ratios, with a mean as the denominator, could artificially reduce the variability in the data, potentially leading to spurious findings or an increased risk of Type I error.

As pointed out above, we have used internal normalization to a housekeeping gene before comparing the resulting values of the treatment and control groups. This method (commonly known as ΔΔC_t method) is a standard way of comparing gene expression values obtained by RT-PCR. The use of a log2 transformation is commonly used to convert the logarithmic data resulting from the RT-PCR measurement to a linear fold-change measurement. We do not see that this data analysis strategy should lead to an increased risk for producing false positives. We now explain this better in the methods section of the manuscript (lines 541ff), and have adapted the labels in Figures 3B, C and S4 to avoid confusion.

(8) It is unusual that both the positive and negative limbs of the circadian clock are overexpressed following lactulose administration. The authors should provide data confirming that these genes are in counter phase to each other at baseline. This clarification would help readers better understand the effects of the experimental interventions. As it stands, this critical part of the results is quite confusing.

We agree that this result does not allow a clear interpretation of the effect of lactulose on the diurnal rhythm of the host. While we agree that this would be interesting to understand in detail, we are merely taking this as a first indication that actuation of microbial metabolism during the inactive phase of the diurnal rhythm can lead to changes in clock genes. This claim is supported by our data.

(9) Could the effects of the microbial metabolites be mediated by AMPK, a known nutrient sensor that can influence the post-translational modification of Cry proteins? It would be beneficial for the authors to explore whether these metabolites have a more direct, previously unknown mechanism of affecting the circadian clock, or if their effects are mediated through known signaling pathways such as AMPK.

We agree that this would be a valuable path to continue investigating the effect of microbial metabolism on clock gene activity.

(10) The methods section does not specify how the metabolic hormones (e.g., GLP-1, GIP, leptin, ghrelin) were measured in the experiments. It is important for the authors to confirm that DPP-IV/protease inhibitor tubes were used for hormone measurement, as these proteins can be rapidly degraded by circulating proteases. Without the use of appropriate tubes, this data cannot be reliably interpreted. Additionally, it would have been ideal to collect these hormone levels during both the fasting and fed phases, but it appears this was not done. This represents a significant limitation of the study and should be addressed in the discussion.

We thank the reviewer for pointing out this omission, we have now added a description of our protocol to measure metabolic hormones to the methods section (lines 469ff).

(11) If the samples were appropriately collected in DPP-IV/protease inhibitor tubes, the authors should consider measuring active GLP-1, as this would likely provide a more accurate assessment of GLP-1 activity.

We agree that this would be a valuable next step, in addition to testing the effect of changes in microbial metabolism on the time traces of hormone levels.

Minor Comments:

(12) Line 350 appears to have an incomplete sentence, as it seems part of the first sentence in the paragraph has been inadvertently deleted. This should be reviewed and corrected for clarity.

Done.

Reviewer #3 (Recommendations For The Authors):

Major comments:

(1) Could the authors provide a deeper description about what they are referring to in the following statement? "...higher order interactions and microbial metabolism are variable..." it is difficult to interpret as written. Do the authors mean cross-feeding interactions?

We have changed this sentence to clarify the meaning.

(2) Could the authors explicitly state their hypothesis in the introduction and provide a brief, but deeper explanation of the intervention prior to the results section?

This is a good point, we have adapted the text accordingly (lines 53ff).

(3) Could the authors include a bit more information regarding the diet provided to the mice? If grain-based chow, please provide insights into the fiber source, etc.

While we agree that it would be interesting to know what part of the mouse diet is available to the microbes, this is hard for the standard mouse chow that we (and most others doing experiments with mice) feed the experimental animals. We have now added more detailed information on the specific type of chow the mice were fed (lines 347f). We would argue that, because the control and treatment groups were always fed the same chow, the effect of the fiber source and other specifics are controlled for, even if we do not know them.

(4) In figure 1A - cells/g does not seem to be the correct unit - # of copies/g feces perhaps?

Cells/g is the appropriate unit, but it seems like we have not explained the way we arrive at this unit in sufficient detail. In short, we use a qPCR run on a known standard curve of bacterial counts (known cells/g values) to estimate these numbers from qPCR results from faeces. We have now explained this better in the methods section (lines 385f).

(5) Figure 1B/C and Figure S1B/C are confusing - the legend states these measurements were taken over two days, however, the plot shows a single 12:12 LD period. Was the data averaged? It might be best to show each day separately (i.e., over a 48-hour period) rather than in one 24-hour plot. Then, the authors could also show the averages in the light period vs. the dark period in a separate, complementary graph.

We thank the reviewer for pointing this out. The previous figures were indeed averaged over the two days of measurement and projected onto one 24h period for plotting. We have now changed Figures 1B,C and S1B,C to show the full 48h time windows.

(6) Line 109 - The reviewer concurs that lactulose is a non-nutritive, synthetic disaccharide, however, in theory, lactulose may have a high heat increment, which could cause the animal to undergo metabolic responses to defend core body temperature (which also exhibits diurnal rhythmicity). Have the authors considered core body temperature rhythms, their connection to microbial metabolism, and the core circadian clock gene network in their model?

This is an interesting thought. We have not measured body temperature in our experiments. As the heat increment from food is typically associated with metabolic activity, and lactulose is not metabolized, we do not expect its heat increment to be high, at least in GF mice. In mice with a microbiota, we agree that metabolic heat will be produced upon lactulose metabolism by the microbes, which could be a contributor the observed effect.

(7) Figure 2A and corresponding text in lines 121 - 123 - indicate at what time the bar and whisker plots were taken (assuming at ZT8, but please be explicit in the figure and corresponding text). Could the authors also include statistics for these waveforms?

Done.

(8) In Figure 2B, the authors state that microbial metabolism had been restored to normal levels by ZT15, however, did this persist into the next light phase? It would be ideal if the authors could present these data in a similar manner to that shown in Figure S2A for SPF mice. Further, what are the statistical considerations here to describe changes in phase, amplitude, periodicity, etc.

This is a good point. Unfortunately, we do not have H2 measurements for EAM and GF mice over comparable time periods as shown for SPF mice in Figure S2A. However, the food intake data shown in Figure S5BCD is a indicates that the food intake normalized in the second dark phase after treatment.

(9) In lines 147 - 149 and in Figure S2B figure legend - assuming these measurements are from individual bacteria? Could this be stated clearly in the text or legend? Also, what are the statistical considerations? Were there significant differences in SCFA production between bacteria?

We thank the reviewer for pointing out that this was unclear. We have now adapted the legend to explain the way these data were collected and added a statistical analysis.

(10) The authors have done a large amount of work to examine the osmotic vs. metabolic influence of lactulose delivery - however, have the authors accounted for the enlarged cecum and increased cecal surface area in germ-free mice? Would an additional control be cecectomy in germ-free mice to be more in-line w/ SPF animals? Further, could the authors tie in these findings more explicitly and state how they pertain to the overall goal of the study? Is this simply to draw the conclusion that microbial biomass is increased w/ lactulose?

We wanted to make sure that the effect we see with lactulose is due to microbial metabolism and not due to the induction of osmotic diarrhoea or other host-dependent effects, and we have added a statement to that effect (lines 127ff). We have not corrected for the change in cecum size between GF and EAM mice, as EAM size (and many other gnotobiotic mouse models) also have enlarged ceca relative to conventionally colonized mice, but have added a dataset showing how cecum size of EAM and GF mice compare and discuss this in the text (new Figure S2F, lines 135ff).

(11) Is Figure 3A necessary?

It might not be strictly necessary, but it can help with understanding the relation of the genes tested in B and C, and we would therefore like to keep it in.

(12) Line 155 - 157 - the authors make the statement that dry/wet feces weight ratio is decreased in GF mice, but this does not appear to be statistically significant. Please adjust to state numerical differences were observed or provide statistics.

We have changed the statement in the text.

(13) Could Figure S3A be moved to the main Figure 3 as this may provide a more logical flow? qRT-PCR data is expressed as - log2 (fold expression), but relative to what? Could the authors provide further info about the control?

The former Figure S3A (new S4A) and Figure 3B show the same data in slightly different ways. We therefore opted to keep only one of those illustrations in a main figure. The fold changes are always relative to the average of the PBS control group, which we now state explicitly in the figure legend.

(14) The authors state that the qRT-PCR data shows that microbial metabolism of lactulose impacts peripheral circadian gene expression, but this conclusion seems simplified. Lactulose treatment only impacted the ileum circadian gene expression. Additional peripheral tissues (liver, adipose tissue, etc.) could be moved to this figure, i.e., move Figure 4C data. Why do the authors think the ileum was most impacted beyond GI hormones as discussed later in the manuscript? Could changes in bile acid deconjugation (i.e., BSH activity?) and/or bile acid resorption by the host in the distal ileum due to lactulose delivery be involved? Or is it simply due to differences in GI transit time (which was not measured in the current study)? Further, lactulose had minimal impact in SPF ileum, and in fact, shifted Cry1 in the opposite direction relative to EAM mice. Could the authors provide more insight into these disparate observations (line 196 - 200)?

We agree that the statement "lactulose impacts peripheral gene expression" is oversimplified, and we have now adapted the text to avoid the impression that this is our conclusion. No tested tissues other than the ileum showed significant differences in gene expression at the time point tested, which does not rule out that other tissues would react to the treatment at that time point, or the tested tissues would do so at the tested time point. As we don't have a good enough understanding of what mechanism causes the gene expression changes in the ileum, we refrain from speculating in the text, even though we agree that this is an intriguing question.

(15) Could the authors provide more insight into the statistical approaches used to assess amplitude, peak, nadir, etc. in Figure 3C? Was the co-sinor waveform tested?

This is a good question. Even though this was a highly work-intensive experiment using many animals, we would argue that the noise level is too high and the coverage of the time analyzed too sparse to infer meaningful statistics on the fluctuations of gene expression over time. In the new version, we have changed our statistical analysis of this dataset to a two-way ANOVA (treatment, time) to better analyze this dataset.

(16) The food intake decrease and interpretation following treatment (Figure 4A and S4A) is curious - all animals were gavaged and in EAM mice, many animals, regardless of PBS or lactulose are trending down in food intake rate/total intake. It seems to be more of an impact of gavage and not of treatment, which the authors somewhat acknowledge in Lines 228 - 230.

We agree that gavage is a possible factor in future food intake of experimental animals, which is precisely why we used the PBS gavage as a control. Even though the difference is not large, we see a significant change in food intake when lactulose is given, but not when PBS is given (Figure 4A, S4A).

(17) Could the authors provide a deeper rationale for their line of thinking for lines 234 - 240? What is the evidence that systemic effects are likely to occur 3 hours after lactulose delivery? Further, as stated in comment 13, could brain and liver data be moved to Figure 3/Figure S3 as an additional example of peripheral tissue clocks?

We have added an explanation for the rationale we use to justify the 8h time point (it is 3h after the peak of H2 production, as shown in Fig2AB, which happens 5h after lactulose delivery). While we agree that the brain and liver data would also fit into the Figure 3, we have now moved all negative data to the supplementary information (in response to a comment by reviewer 1, and in a general effort to clean up the data in the manuscript).

(18) The authors measure PYY and GLP-1 at a single time point and state there are no differences, yet, the goal of the studies is to tie this back to circadian networks. Would it be possible to measure these GI hormones over a 24-hour period to show that the diurnal patterns are altered?

We fully agree that measuring the metabolic hormones over time would be very interesting. It is possible but would represent a major effort using many animals and a large amount of work. We would therefore argue that it is beyond the scope of this revision, but a good starting point for a follow-up study.

(19) The authors state that the administration of fermentation products acutely altered circadian food intake, but the studies do not support that this change is connected to the circadian network. Suggest softening the interpretation of the findings.

We have changed the language there to soften the interpretation.

Minor comments:

(1) The authors should consider when it is appropriate to refer to rhythms as diurnal vs. circadian, as each has a distinct meaning. Diurnal follows entrainment cues while circadian is endogenously driven (i.e., line 39, line 58).

We thank the reviewer for pointing out this important difference, we have adapted this in the whole text accordingly.

(2) Circadian rhythm should be plural throughout the manuscript (circadian rhythms).

Thank you, we have changed that where we refer to host circadian rhythms generally.

(3) Lines 54 - 63. Fermentation should be capitalized when used at the beginning of a sentence.

Done.

(4) Line 289 - This should be Figure 5D and 5E.

Done.

(5) Line 290 - heart should be cardiac.

Done.

Author response:

eLife Assessment

This paper introduces a valuable optical method for simultaneous in vivo multiphoton imaging of the mouse brain combined with DMD-based one-photon patterned photostimulation in different axial planes. The evidence for effective optical separation of excitation and imaging is convincing, although the in vivo data in the olfactory bulb suggest potential confounding factors arising if stimulation not only affects cell bodies but also neuronal processes. The work will be of broad interest to neurobiologists working in circuit and systems neuroscience, as well as to specialists in optical microscopy.

We thank the reviewers for their constructive feedback. We are planning to address their concerns as detailed below. Specifically, in the revised manuscript, we will streamline and consolidate the text to include:

(1) An in-depth discussion of the awake recording results in the main text.

(2) Further discussion of light scattering, photo-stimulation specificity of targeting individual glomeruli and resolution.

(3) A summary (including also a table) of the operating regime and comparisons with alternative techniques for patterned photo-stimulation and imaging of the ensuing responses. We will highlight the advantages and constraints of the current implementation of ADePT. In particular, here we explored a small set of spatiotemporal parameters to understand the limits of our technique and provide a proof of principle of the strategy. These parameters can be varied further depending on the exact research question.

(4) Implementation considerations and technical guidelines for calibration and long-term stability of the rig for ADePT (i.e. ‘a how-to guide’).

(5) A bill of materials and estimated hardware costs.

Furthermore, we will provide additional controls and rephrase some of the statements in the text as suggested (e.g. replace ‘accessible’ with ‘simple’, etc.). We will correct the unfortunate grammatical errors, improve clarity of text, and update the references accordingly.

Public Reviews:

Reviewer #1 (Public review):

In this methods paper, the authors introduce a novel and innovative imaging approach for simultaneous in vivo multiphoton imaging of the mouse brain combined with DMD-based one-photon patterned photo-stimulation in different axial planes. This is a highly exciting technique that enables the axial decoupling of optical imaging of deep neural circuits from surface photo-stimulation of spatially precise (tens of micrometres) brain spots. This method builds on previous developments from the same laboratory, combining DMD-based patterned photo-stimulation with in vivo electrophysiological recordings. To my knowledge, this is the first instance in which patterned photo-stimulation has been combined and axially decoupled from two-photon (2P) imaging.

Beginning with a thorough characterisation of the optical resolution of the photo-stimulation system, the authors applied this method to the olfactory bulb (OB) network, in which sensory inputs are topographically organised at the surface of the OB and thus ideally suited to demonstrate the relevance of this approach. They first showed that this technique can be used to rapidly reveal connectivity patterns of OB output neurons and to identify sister mitral cells. In addition, they manipulated a specific glomerular inhibitory population and demonstrated that these neurons provide spatially heterogeneous long-range inhibition of OB output neurons, with differential effects on mitral and tufted cells (a result previously observed in a paper from the same lab: Banerjee et al., 2015, Neuron). Altogether, the data demonstrate that this technique is well-suited for high-throughput functional mapping of neural circuit properties. The results are compelling and illustrate both the significant advance represented by this method and its feasibility.

We thank the Reviewer for their constructive input.

Despite my initial enthusiasm, there are several concerns in the present study that must be addressed in order to rule out confounding observations and to resolve remaining uncertainties regarding photo-stimulation resolution. These include the following:

(1) Spatial resolution: Although the authors provide convincing data on spatial resolution in vitro, several observations throughout the paper suggest that the effective photo-stimulation precision may be lower than initially reported. For instance, in Figure 2, the authors observe repeated responses in neighbouring glomeruli (e.g., glomeruli #3 & #5, #4 & #6). To what extent could light scattering along the X/Y/Z-axis above the targeted glomerulus recruit en passage axons, resulting in the inadvertent activation of multiple glomeruli?

Indeed, we cannot rule out this possibility. Fibers of passage are a potential concern. This is why we systematically sample different light intensities and assess their impact on specificity of dendritic mitral and tufted cell responses within the glomerular layer (same axial-plane optical stimulation and imaging experiments, Fig. 2). We identify a range of intensities that on average result mostly in activation of the targeted glomeruli. Within the range of intensities used for identifying sister cells, >90% of responses were on the diagonal (targeted glomeruli) and ~5% pixels that cleared the signal significance criterion used were in off-target glomeruli, as stated in the text and quantified in Fig. 2f. In the revised manuscript, we will further clarify and expand on these points.

A further observation concerns the presence of "inhibited" sister mitral cells (Figure 3). The authors claim this is reminiscent of the differential spike-timing reported between sister cells (Dwawale et al., 2010, Nat Neuro). However, observing both excitatory and inhibitory responses following stimulation of glutamatergic inputs is an altogether different matter, particularly given that sister mitral cells are reciprocally connected via gap junctions. This observation requires further clarification and raises serious questions about the effective resolution of the stimulation. Could the inhibited cell simply correspond to a non-sister mitral cell receiving disynaptic feed-forward inhibition?

This is indeed what we think it is happening (i.e. disynaptic feed-forward inhibition as the Reviewer points out). We observe inhibition in some of the mitral cells in the field of imaging when we stimulate not their parent glomerulus, but other glomeruli in the neighbourhood. As the Reviewer points out, sister cells are connected via gap junctions, but they also receive inhibitory chemical synaptic inputs via their secondary (and primary dendrites) from other (not-their-parent) glomeruli mediated by numerous types of interneurons including the DAT+/GABAergic (a.k.a. superficial short axon cells) and granule cells. Our data is consistent with differential inhibitory input from other glomeruli on sister cells getting input from the same parent glomerulus. As it appears that we failed to present this point clearly in the initial submission, we will further expand along these lines in the revised manuscript. Briefly:

First, we identify a photo-stimulation regime that results mostly in the activation of a given targeted glomerulus (and not of other glomeruli in the field of stimulation). To this end, we photo-stimulate and image ensuing neuronal responses in the same axial optical plane. We strobe (alternate) between monitoring dendritic mitral and tufted cell (enhanced) GCaMP responses within the targeted glomerulus and other glomeruli in the field of imaging, while varying systematically the light intensity (Figs. 2,3a; Suppl. Fig. 4b, Suppl. Fig, 5b-d;h-j). We use as criterion for specificity a condition when >95% of significantly responding pixels (above a statistically defined signal response threshold) lie within the anatomical boundaries of the targeted glomerulus. For each glomerulus (or pixel within a glomerulus) we compared the average light response across trials with the baseline reference distribution in the absence of light stimulation. If this value crossed the 99th percentile of the baseline distribution, the glomerulus/pixel within glomerulus was classified as responsive to the photo-stimulation.

Second, using the minimal light intensity regime experimentally identified as ‘specific’ for targeting individual glomeruli in the field of photo-stimulation (< 5% significant activation of off-target pixels), we decouple photo-stimulation in the glomerular layer from monitoring responses of mitral and tufted cells in the deeper layers of the olfactory bulb (100-250 µm axial displacement). This approach enables us to map cohorts of sister (daughter) cells associated with any specific target glomerulus in the field of view (1,2,3…n) by monitoring excitatory (enhanced) responses of mitral and tufted cell bodies. A cohort of sister cells associated with glomerulus x_i (daughters of glomerulus x_i) is defined by those cells which show statistically significant excitatory responses (4 SD - standard deviations - above their baseline fluctuations) specifically in response to photo-stimulation of glomerulus x_i.

Third, in the process, as we photo-stimulate different glomeruli in the field of stimulation, we also observe at times suppressed (inhibitory) responses in a subset of the mitral and tufted cells (exceeding 3 SD in the negative direction their baseline fluctuations). These suppressed responses occur in response to photo-stimulating not the parent glomerulus of a given cell, but other glomeruli in the field. These experiments revealed that within a cohort of sister cells (daughters of glomerulus x_i), only a subset of cells are suppressed by activation of glomerulus x_j, and, in a few example cases, different cells are suppressed by activation of different glomeruli (e.g. x_j vs. x_k), presumably through disynaptic feed-forward inhibition (Fig. 3b iii; 3d; Suppl. Figs. 5f,g; l,m). These preliminary observations suggest that sister cells receive differential inhibitory inputs from glomeruli in the neighborhood. In the revised manuscript, we will expand to further clarify these points.

To verify sister cell identity, the authors could confirm that the predicted sister cells share a similar odour receptive field compared to randomly selected mitral cell pairs. In their previous study employing analogous DMD-based photo-stimulation (Dhawale et al., 2010, Nat. Neurosci.), sister mitral cells did not exhibit such opposite response profiles (firing rate correlation of ∼0.7 between sister cells). Could the authors verify that a comparable activity correlation is also observed among the sister cells identified using ADePT in the present study? In Figure S6, the authors show recordings and stimulation of the same neurons co-expressing GCaMP and ChR2. Applying this experimental design to the mitral/tufted cell population (using a Tbet-Cre mouse transduced in the OB with both GCaMP and Chrimson virus) would constitute a valuable control to clarify the nature of these "inhibited" sister cells.

We thank the Reviewer for the suggestion. We consider that the experiments shown here are proof-of-principle in nature, highlighting the potential of ADePT for mapping functional neural circuit connectivity. In our opinion, further investigating the logic of similarities and differences in the odor responses of sister mitral cells and the nature of inhibitory glomerular interactions forms the focus of future studies. We also note that firing rate correlations can be notoriously difficult to compare and interpret across experimental regimes (spikes vs. calcium imaging).

An additional concern relates to the 21 out of 162 mitral cells that were activated by two distinct glomeruli - a finding that is incompatible with the established OB wiring diagram and that further challenges the claimed stimulation resolution.

Indeed, this reflects some degree of non-specific activation of the targeted glomeruli as discussed above. In the revised manuscript, we will further highlight this issue.

A critical control experiment is also absent: in a Thy1-GCaMP6 mouse lacking any light-sensitive opsin, do the authors observe any unintended side effects of photo-stimulation?

In the revised manuscript, we will include an additional control as suggested by the reviewer. Within the range of intensities used, we did not observe significant modulation of GCaMP6s activity in mitral and tufted cells in mice lacking light-sensitive opsins.

Regarding sister cells (Figure 3), tufted cells are not analysed alongside mitral cells in this dataset, whereas this is elegantly performed in Figure 5 using the DAT+ model. Could the authors also demonstrate how the technique can reveal the complete family portrait of sister mitral and tufted cells?

We thank the Reviewer for the suggestion. We think that the differences between mitral and tufted cells are indeed very interesting to investigate, but in our opinion form the subject of future studies.

(2) The authors have explored only a limited set of photo-stimulation parameters, primarily varying light intensity. They should present additional tests, such as varying the spot size (which appears to be arbitrarily fixed at 30-50 µm) and the z plane of stimulation. The level of activation can vary considerably: for example, in Figure 3a(iii), identical stimulations elicit responses of markedly different amplitudes (see glom#3 and #4). In Figure 2, 5 out of 15 glomeruli failed to respond - could the choice of z-plane account for this variability? The stimulation duration (50-150 ms) also appears somewhat arbitrary: can the authors demonstrate that the technique is compatible with finer temporal patterns (e.g., 10 Hz stimulation for 500 ms using 20 ms light pulses)? What are the spatiotemporal and axial scanning limits of this approach, and can two or three glomeruli be targeted simultaneously with temporally patterned stimulation?

Indeed, here we explored a limited set of spatiotemporal parameters to understand the limits of our technique and provide proof of principle. These can be varied depending on the exact question. In the revised manuscript, we will clearly state what the constraints of the current implementation are and provide context for further optimizations. Briefly, in the current version, individual as well as multiple glomeruli can be photo-stimulated together and 20 ms per pulse regime in trains of pulses is feasible.

(3) One particularly relevant application of this method would be to guide photo-stimulation based on prior functional measurements - for instance, by generating a photo-stimulation mask specifically targeting odour-responsive glomeruli. In the DAT-Cre × Thy1-GCaMP6 experiment shown in Figure 5e, which glomeruli are activated by a given odour, and how does this odor responsiveness influence the efficiency of DAT+ cell-mediated inhibition?

We thank the Reviewer for the suggestion. We are thinking along exactly the same lines. In particular, we would like to investigate the relationship between the degree of overlap in odor responses of individual glomeruli and the strength and specificity of their inhibitory interactions mediated by DAT+ interneurons. In the revised manuscript, we will further expand on discussing this venue of study. We feel however that this investigation is beyond the scope of this technical report.

Reviewer #2 (Public review):

Summary:

In this manuscript, Koh and colleagues describe ADePT (Axially Decoupled Photo-stimulation and Two-photon Readout), a modular approach for combining patterned one-photon optogenetic stimulation with two-photon calcium imaging in independently controlled axial planes. The method relies on a digital micromirror device together with a motorized holographic diffuser to generate spatially confined stimulation patterns while imaging deeper neuronal populations. As proof-of-principle applications, the authors use the system to map excitatory and inhibitory functional connectivity in the mouse olfactory bulb by stimulating superficial glomerular circuits and recording responses from mitral and tufted cells in deeper layers.

This is a well-executed Tools and Resources manuscript. The technical implementation is described in considerable detail, the optical performance is systematically characterized, and the biological experiments provide convincing demonstrations of the types of circuit questions that can be addressed using the method.

Strengths:

The greatest strength of the manuscript is the comprehensive technical characterization of the optical system. The authors carefully benchmark the spatial resolution, axial confinement, registration accuracy, calibration procedure, and practical operating limits of the setup. I found the extensive optical benchmarking particularly helpful, as it gives readers a realistic sense of the operating regime and practical limitations of the approach.

Another strength is the high level of methodological transparency. The optical design, calibration procedures, stimulation strategies, and analysis pipeline are described in sufficient detail that an experienced laboratory could realistically evaluate whether the system is suitable for its own applications. This level of documentation is particularly appropriate for a Tools and Resources article.

A further strength is the clear positioning of ADePT relative to existing approaches. The authors are transparent about the trade-off between spatial resolution and implementation complexity: ADePT does not provide single-cell photostimulation, but offers flexible axial separation, a large stimulation field, and cellular-resolution two-photon readout in deeper planes without requiring a full holographic stimulation system. This defines a credible and potentially useful experimental niche.

The biological applications convincingly demonstrate the utility of ADePT. The experiments identifying sister mitral/tufted cells through selective glomerular stimulation and the mapping of heterogeneous inhibitory influences from DAT-positive interneurons illustrate the types of functional connectivity questions that become experimentally accessible with this approach. Importantly, the authors generally avoid overstating these biological findings and appropriately present them as proof-of-principle demonstrations of the technology.

We thank the Reviewer for their constructive input.

Weaknesses:

The primary limitation is inherent to the method itself rather than the execution of the study. Because ADePT relies on one-photon patterned illumination, photo-stimulation remains restricted to relatively superficial structures and does not achieve single-cell spatial resolution. The authors appropriately acknowledge these constraints and clearly position the method within this operating regime. Consequently, ADePT occupies a useful niche for interrogating spatially organized functional units such as olfactory glomeruli or cortical barrels, rather than applications requiring single-cell precision or deeper tissue penetration.

We agree. In the revised manuscript, we will further expand on these points, highlighting the limitations and advantages of ADePT compared to other techniques in a table discussing various operating regimes.

Although the manuscript describes the approach as relatively simple and cost-effective, implementation still requires careful optical alignment, registration, calibration, and optimization. This does not diminish the value of the approach, but terms such as modular or accessible may better reflect the practical implementation than simple. Likewise, a brief bill of materials, approximate add-on cost, and indication of which components are essential versus substitutable would help prospective users assess the accessibility of the system.

We agree. We will change the text accordingly and provide the additional information as suggested.

Finally, the manuscript provides an impressive level of technical characterization, but much of the practical guidance for adopting the system is distributed across the Results and Discussion. Bringing together the principal limitations, recommended operating regime, expected calibration workflow, evidence for long-term alignment stability, and the circumstances in which ADePT is preferable to alternative approaches would further strengthen the manuscript as a community resource.

We agree. We will proceed accordingly in the revised manuscript.

Reviewer #3 (Public review):

Summary:

This manuscript asks whether two forms of explicit strategy use in visuomotor adaptation, i.e., algorithmic mental rotation and retrieval of a cached aiming solution, differentially influence implicit recalibration. The question is relevant because much prior work treats explicit strategy as a unitary process, whereas the algorithmic/retrieval distinction is theoretically meaningful and grounded in cognitive theory. Across three experiments, the authors report that algorithmic strategy conditions initially produced broader fitted implicit generalization functions than retrieval conditions, but that this difference was reduced or eliminated when reach variability and sensory prediction errors were more tightly controlled.

Strengths:

The paper is clearly written, theoretically well-motivated, and employs a commendably transparent and progressive experimental logic. The three-experiment structure, in which confounds are systematically identified and addressed, represents a strong model of cumulative experimental design (I will certainly use it in teaching courses on experimental methods):

Experiment 1 establishes an apparent difference in implicit generalization breadth. Experiment 2 attempts to reduce error spillover from Non-Critical targets by increasing angular separation and using delayed endpoint feedback. Experiment 3 uses an error-clamp design to decouple variable reaching from error feedback. This sequence is appropriate for testing whether the initial difference reflects a strategy-dependent change in implicit recalibration or instead follows from the distribution of movement plans and error exposure. The authors also provide reaction-time and performance data that are broadly consistent with the intended distinction between algorithmic and retrieval-like task performance.

Weaknesses:

The evidence does not support the strongest claims made in the manuscript, namely that algorithmic and retrieval strategies generally do not reshape implicit recalibration.

In general, I am skeptical of the authors' interpretation of null results. Several central conclusions depend on non-significant group differences, especially in Experiment 3. Non-significant tests are repeatedly treated as evidence that groups are equivalent or that confounds are absent (e.g., implicit recalibration magnitude (Algorithmic: 11.43 {plus minus} 6.43{degree sign}; Retrieval: 15.49 {plus minus} 8.99{degree sign}; t(38) = −1.65, p = .11), adaptation level before Exclusion probes (F(1,256) = 3.04, p = .08) and Exclusion RT differences (F(1,266) = 3.15, p = .08), whereas a modest model-dependent breadth effect (bootstrap p = .02) is treated as meaningful (for more on the model-dependent breadth effect, see below).

Without confidence intervals, equivalence tests, or Bayesian analyses, I think that the authors' interpretations comprise an inferential gap. A failure to find a significant difference is not equivalent to evidence of equivalence, particularly given that the implicit recalibration signal gets progressively attenuated across experiments (Experiment 1: ~16-17{degree sign}; Experiment 2: ~11-15{degree sign}; Experiment 3: ~7-8{degree sign}). With a substantially diminished signal in Experiment 3, the null result could partly reflect reduced statistical sensitivity rather than true equivalence.

My main technical concern is the analysis of generalization breadth already alluded to. The central claims rely on group-level Gaussian fits to only seven Exclusion probe locations spanning −45{degree sign} to +45{degree sign} around the Critical target. In several cases, the fitted centers and widths are poorly constrained by the sampled range. For example, in Experiment 2 the algorithmic group's fitted center is shifted to approximately 29{degree sign}, meaning that the probe range samples the function asymmetrically relative to its own peak. In Experiment 3, fitted centers are near or outside the sampled range, while estimated widths are very broad. Under these conditions, the width parameter may partly reflect extrapolation or parameter trade-offs between center, amplitude, and width rather than a genuine difference in generalization breadth.

Lastly, I think that the authors' use of an error-clamp paradigm is, from an experimental point of view, quite elegant. By controlling the sensory prediction error independently of reach direction, they can isolate implicit recalibration from the confounds identified in Experiments 1 and 2. However, I see a fundamental problem or question concerning construct validity here: In Experiments 1 and 2, the algorithmic strategy was operationalized as participants computing a counterrotated aiming direction in response to a visible cursor rotation. This is a naturalistic context where mental rotation is both required and meaningfully connected to task success. In Experiment 3, however, there is no visuomotor rotation to compensate for. The error-clamp renders the cursor feedback task-irrelevant. Instead, participants are instructed via text commands (e.g., "move towards 45{degree sign}") to reach invisible locations, rendering the "algorithmic strategy" in this context essentially an instructed spatial navigation toward arbitrary angular locations, not genuine visuomotor mental rotation driven by an error signal.

To put it differently, are we sure that the cognitive process engaged by the algorithmic group in Experiment 3 is the same as the algorithmic mental rotation strategy in Experiments 1 and 2? If not, then the null result in Experiment 3 may not speak to the original question about how algorithmic strategies interact with implicit recalibration after all. Instead, it may reflect the absence of a genuine strategy manipulation.

To their credit, the authors report a compelling RT dissociation that mirrors Experiments 1 and 2: The algorithmic group shows slower RT, which is decreasing over training (0.98s → 0.76s), whereas the retrieval group exhibits faster, stable RT (0.52s → 0.45s). While this pattern is consistent with genuine strategy differences persisting in Experiment 3, it could also reflect the greater spatial precision demands of reaching to invisible targets from text instructions, rather than genuine mental rotation per se. Reaching to an invisible location defined by a verbal angular label is inherently more demanding than reaching to a visible target, regardless of strategy type, and this demand is asymmetrically present in the two groups, since Non-Critical targets are invisible for the algorithmic group but visible for the retrieval group.

Thus, from my point of view, experiment 3 should not be used as definitive evidence that algorithmic and retrieval strategies during standard visuomotor adaptation cannot differentially influence implicit recalibration.

Overall, the manuscript addresses a meaningful question and the multi-experiment structure is useful. The evidence is incomplete for the broad claim that implicit recalibration is insensitive to strategy type. The study would make a clearer contribution if the authors narrowed the claims, strengthened the generalization analyses, and treated null effects with appropriate inferential tools.

Author response:

Reviewer #1 (Public review):

A previous study from the same team (McDougle & Taylor, 2019) demonstrated that explicit strategies during visuomotor adaptation can be dissociated into retrieval-based and algorithmic strategies. However, whether these distinct forms of explicit processing differentially influence implicit recalibration has remained unresolved, with previous studies providing evidence both for relatively independent explicit and implicit processes and for interactions between them. This study addresses this question through a series of experiments that used Critical and Non-Critical targets to induce distinct strategic modes while maintaining comparable adaptation at the Critical target.

Experiment 1 replicated previous findings showing broader implicit generalization under algorithmic strategies. However, this broader generalization could be explained by spillover effects arising from adaptation at the Non-Critical targets. Experiment 2 was designed to reduce such spillover effects by increasing the spatial separation between the Critical and Non-Critical targets. Although broader generalization was still observed in the algorithmic condition, this effect was interpreted as reflecting greater variability in reaching behavior at the Critical target. Finally, Experiment 3 introduced additional controls using an error-clamp paradigm, and the difference in generalization width between the two strategies largely disappeared.

We appreciate the reviewer’s thoughtful and comprehensive summary of our study.  One thing we would like to clarify is that the non-critical targets used in Experiment 1 received the same type of online continuous feedback as the critical target.Therefore the extent of implicit recalibration should be comparable between the critical and non-critical targets in Experiment 1. In contrast, for Experiment 2, we tightened the control for implicit recalibration at the non-critical targets by: 1) delivering delayed endpoint feedback for all non-critical targets while keeping the online continuous feedback for the critical target, which is known to suppress implicit recalibration, and 2) we widened the spatial gap between the critical and non-critical targets, to minimize spillover 2) As a result, the implicit recalibration was diminished at the non-critical targets, contributing to the shrinkage of the generalization curve around the critical target. 

One other issue that we would like to make clear is that Experiment 1 was not a straight replication of a previous study, at least to our knowledge. We believe that the reviewer is referring to our previous study (McDougle and Taylor 2019), which found broader generalization for algorithmic strategies (Experiment 4). However, in that study cursor feedback was always delayed. As such, the observed broader generalization was most likely due to the strategy itself and not implicit recalibration. 

Together, these findings led the authors to conclude that implicit recalibration is relatively insensitive to the type of explicit strategy employed and is primarily shaped by the statistics of the movement plans on which learning occurs.

The experimental design using Critical and Non-Critical targets is particularly interesting and represents a creative approach to manipulating strategy use. Reaction times were generally longer in the algorithmic group, even at the Critical target, suggesting that the manipulation was at least partially successful in biasing participants toward algorithmic versus retrieval-based strategies. The results that the implicit recalibration is independent of the explicit strategy (how you aim) but depends on the aiming point by the explicit strategies (where you aim) are basically reasonable.

We are glad to know that our primary finding and conclusion appears reasonable. While we acknowledge that the finding doesn’t appear to be particularly exciting at face value, it does speak to larger questions regarding the independence of different learning systems and how just statistical or surface-level differences in training can result in relatively large differences in apparent behavior that could be easily misinterpreted as the result of system interactions.

I would like the authors to clarify two points.

First, how reasonable is it to infer the use of distinct explicit strategies primarily from reaction time differences? While longer reaction times in the algorithmic group are consistent with greater computational demands, it remains unclear whether the longer reaction times observed at the Critical target necessarily reflect different strategy implementations at that location. In particular, could the increased cognitive demands associated with the Non-Critical targets in the algorithmic condition have carried over to the Critical target, thereby prolonging reaction times without implying qualitatively different strategies at the Critical target itself?

This is a fair concern, as RT is an indirect marker of strategy use and, by itself, cannot establish that participants used different strategies at the Critical target. Prior work, however, provided guidance for the design of our experimental manipulations. Algorithmic strategies, in which an aiming solution is computed online, are associated with longer RTs, whereas retrieval of a previously cached stimulus–response association produces substantially shorter RTs (McDougle and Taylor, 2019; Velazquez-Vargas and Taylor, 2024). Moreover, caching becomes increasingly difficult as the number of target-specific solutions increases, particularly beyond approximately four targets (Velazquez-Vargas and Taylor, 2024; Bejjanki and Taylor 2026). Our manipulation was designed around these findings: participants in the Algorithmic condition learned the 45° rotation across 10 targets, whereas participants in the Retrieval condition repeatedly encountered the 45° rotation only at the Critical target. As expected with this experimental design, RTs at the Critical target were significantly longer in the Algorithmic condition across all three experiments.

We agree with the reviewer, however, that this RT difference could in principle reflect a more general carryover of cognitive demands from the Non-Critical targets rather than online computation at the Critical target itself. We can address this possibility more directly by asking whether RT at the Critical target exhibits the parametric signature expected of an algorithmic process. A defining feature of mental rotation is that RT scales with the magnitude of the computed aiming solution (Georgopoulos and Massey, 1987; Bhat and Sanes, 1998; McDougle and Taylor, 2019; Velazquez-Vargas and Taylor, 2024). Although rotation magnitude was fixed in the present experiments, participants’ actual reach angles varied naturally from trial to trial. Indeed, McDougle and Taylor (2019) originally demonstrated this relationship using actual reach angle rather than imposed rotation magnitude. We can therefore test whether trial-by-trial RT covaries with reach angle at the Critical target in the Algorithmic condition but not in the Retrieval condition. Such a relationship would be difficult to explain as a nonspecific carryover of cognitive load and would instead provide direct evidence that preparation time at the Critical target reflects the computation of the aiming solution.

We also observe a second, independent difference at the Critical target: reach angles are consistently more variable in the Algorithmic condition than in the Retrieval condition across all three experiments (Figure S6). This pattern is consistent with repeated online computation producing variability in the selected aiming solution, whereas retrieval of a cached stimulus–response association produces a more stable response. Importantly, a general carryover account based solely on increased cognitive demands does not readily explain why movements to the Critical target should also be systematically more variable. Nor is this pattern easily explained by a speed–accuracy tradeoff: the Algorithmic group had more preparation time yet nevertheless exhibited greater variability. Consistent with this notion, Velázquez-Vargas and Taylor (2024) found that retrieving cached solutions produced less variable and more precise movements than movements that are not cached in the memory trace. 

Third, we can conduct additional analysis to compare RT variability between algorithmic and retrieval groups at the critical target location. According to Logan instance theory (Logan, 1988), the retrieval of cached stimulus-response associations produces a stable RT profile, in contrast, trial-by-trial algorithmic computation can result in more variable trial-by-trial RT differences. 

While we agree that RT differences alone should not be taken as definitive evidence of distinct strategies, our specific experimental design, the longer and more variable RTs at the Critical target, the greater trial-by-trial variability at that same target, and, if confirmed, a parametric relationship between RT and reach angle provide converging evidence that participants in the two conditions relied on different strategy implementations when preparing movements to the Critical target.

Second, the interpretation of Experiment 3 is not entirely clear to me. The manuscript argues that the algorithmic group continued to exhibit greater reaching variability than the retrieval group. If this variability indeed reflects greater variability in movement plans, one might expect a broader implicit generalization function in the algorithmic group. However, the generalization widths were comparable between groups. Could this result instead suggest that the implicit recalibration process itself generalized more narrowly in the algorithmic group, thereby offsetting the broader distribution of movement plans? More generally, I would appreciate further clarification regarding the relationship between reaching variability, movement-plan variability, and the resulting width of the implicit generalization function.

We appreciate the reviewer’s thoughtful comment and agree that this is an important distinction. First, we would like to clarify the relationship among reaching variability, movement-plan variability, and the width of the implicit generalization function. Previous work has shown that when implicit recalibration occurs at a particular target location without an explicit aiming strategy, its generalization across the workspace can be described by a Gaussian-shaped function centered near the trained target location (Morehead et al., 2017). When an explicit aiming strategy is involved, however, implicit recalibration is centered closer to the planned aiming location rather than the visual target itself (McDougle et al., 2017). Thus, implicit recalibration is greatest near the direction in which the movement is planned, and a broader spatial distribution of movement plans can, in principle, produce a broader aggregate implicit generalization function. In the present study, we therefore use trial-to-trial variability in endpoint hand angle as a behavioral proxy for variability in planned movement direction, while recognizing that endpoint variability may also contain contributions from execution-related noise.

This framework motivated the progression from Experiments 1 to 3. In Experiment 1, participants in the algorithmic condition exhibited substantially greater reaching variability, consistent with the idea that they sampled a wider range of movement plans across trials. Because error feedback associated with these different movement plans can induce implicit recalibration around each planned direction, greater variability in strategy use could contribute to the broader implicit generalization observed in the algorithmic group. In Experiment 2, we imposed stricter controls on spillover from noncritical targets, which reduced the overall breadth of generalization; nevertheless, model fits still suggested a modestly broader implicit generalization function in the algorithmic group, consistent with the remaining difference in reaching variability.

Experiment 3 was designed to further reduce the direct influence of strategic variability on the induction of implicit recalibration by using a modified error-clamp paradigm. Error-clamp feedback has been shown to elicit implicit recalibration independently of task success and the participant’s explicit strategy (Morehead et al., 2017). We therefore used error-clamp feedback as an incidental signal to induce implicit recalibration while participants implemented either algorithmic or retrieval-based strategies. Importantly, however, Experiment 3 did not completely eliminate between-group differences in reaching variability: the algorithmic group continued to show greater variability around the critical 45-degree location than the retrieval group. We agree with the reviewer that, in principle, comparable generalization widths could arise if this broader distribution of movement plans were offset by a narrower local generalization of implicit recalibration in the algorithmic group. 

However, not all variability is equivalent—or well described by a Gaussian distribution. Depending on the direction of the skew, variability in aiming can produce different effects on the implicit recalibration function, appearing as either broader generalization or greater amplitude. These effects are difficult to appreciate in Figures 3 and 5 for Experiments 2 and 3, respectively. We therefore sought to illustrate this more clearly in Figure 6, which shows how differences in the underlying aim distributions can shape the resulting implicit recalibration function in directionally complex ways. What complicates matters further is that implicit recalibration can asymptote (Morehead et al., 2017; Kim et al., 2018; Wilterson & Taylor, 2021). As a result, plan-based generalization can distort the implicit recalibration function in different ways depending on which side of the aim the error falls. The block-by-block analysis, suggested by reviewer 2, may shed light on this issue because we can get a sense if implicit recalibration has reached asymptote. 

At a minimum, in the revised manuscript, we work to make clearer that subtle changes in the reach distribution may have a corresponding impact on the shape of implicit recalibration’s generalization function.  

Reviewer #2 (Public review):

This study addresses an important question in motor learning: whether algorithmic versus retrieval-based explicit strategies differentially shape implicit recalibration. The progressive experimental logic across three experiments is commendable, and the plan-based generalization account is a plausible and interesting interpretation. However, several methodological concerns limit the strength of the conclusions. I recommend the authors temper their claims accordingly, in the results/discussion section.

Concerns

(1) The retrieval group received 5 pre-exposure trials before main training began, which the algorithmic group did not. Faster RTs in the retrieval group could therefore reflect task familiarity from extra practice rather than efficient memory retrieval per se. I might have missed this, but I did not see performance data from these pre-exposure trials. The early training advantage in the retrieval group might be confounded with the 5 pre-exposure trials they received. Unless there is a direct comparison between the pre-exposure trials for the caching group and the first 5 trials of the algorithmic group, the claim that "storing and retrieving a memory from a short-term memory cache confers more rapid performance improvements than executing an algorithmic strategy" seems somewhat unwarranted.

We appreciate the reviewer raising this potential confound. We agree that the five pre-exposure trials in the Retrieval condition introduce a small difference in initial task familiarity. However, this account makes a straightforward prediction: if the shorter RTs in the Retrieval condition simply reflect five additional trials of general task experience, then the RT difference should disappear once the Algorithmic group has received a comparable amount of practice.

We can test this directly by comparing the five pre-exposure trials in the Retrieval condition with the first five trials of the Algorithmic condition. We will also compare these pre-exposure trials with a later five-trial window from the Algorithmic condition to determine whether additional practice substantially reduces Algorithmic RTs. Assuming the observed pattern is as expected, RTs in the Algorithmic condition remain substantially longer even after considerably more than five trials of practice. Thus, the group difference cannot be explained simply by the Retrieval group having five additional trials of task familiarity. This persistent RT difference, together with our prior work showing characteristic RT differences between algorithmic computation and retrieval of cached aiming solutions, supports our interpretation that the groups relied on different strategy implementations.

We are less certain what the reviewer means by the “early training advantage.” If this refers to angular error, we agree that the Retrieval group shows somewhat better performance very early in training, but this difference is not a central focus of the present study and largely disappears by the second or third training block. We will clarify the text so that we do not overinterpret this transient difference.

If instead the reviewer is referring to RT, then the matched-trial analysis directly addresses the concern. Five additional familiarization trials could plausibly produce a brief initial advantage, but such an effect should dissipate within a small number of subsequent trials. In contrast, the RT difference between the Algorithmic and Retrieval conditions remains robust throughout training. We therefore do not think that general task familiarity provides a sufficient explanation for the observed RT differences.

The algorithmic group also visited the critical target approximately 40% of trials across 356 trials (about 140 trials?). McDougle & Taylor (2019) showed that 300 trials of practice with 2 targets is enough transition from algorithmic to caching strategies. It seems likely that the number of visits to the critical target here was sufficient for caching to develop in the algorithmic condition. This concern about caching in the algorithmic group has implications for the implicit recalibration measurements. As I understand it, the 7 exclusion blocks were distributed throughout training, and so, implicit recalibration was measured across both early and late practice. If caching emerged in the algorithmic group during late practice, then the generalization functions - averaged across all 7 exclusion blocks - conflate early algorithmic strategy and later caching. The broader generalization function observed in the algorithmic group may therefore be driven primarily by early exclusion blocks, while later exclusion blocks may increasingly resemble the retrieval group as caching develops. This is testable in the data: if generalization breadth in the algorithmic group narrows across the 7 exclusion blocks while remaining stable in the retrieval group, that would be consistent with a strategy transition occurring during training. The authors should either report exclusion block-by-block generalization functions separately for each group, or acknowledge that the averaged generalization functions may obscure a strategy transition in the algorithmic group.

The reviewer raises an interesting possibility. In McDougle and Taylor (2019), however, the transition from algorithmic computation to retrieval occurred in a condition with only two targets in the task set. With repeated practice, participants needed to retain only two target-specific aiming solutions, making it feasible to replace online computation with retrieval of cached stimulus–response associations. By contrast, the Algorithmic condition in the present study contained 10 target locations. Our prior work suggests that caching becomes increasingly difficult once the number of target-specific solutions exceeds approximately four, at least over the timescale of several hundred trials (Velázquez-Vargas and Taylor, 2024; Bejjanki and Taylor, 2026). Thus, our task was designed to maintain pressure toward an algorithmic strategy throughout training.

The reviewer nevertheless raises a more specific possibility that is not ruled out simply by the size of the target set: participants might selectively cache the aiming solution for the frequently sampled Critical target while continuing to use an algorithmic strategy at the remaining targets. We think the existing behavioral data argue against such a clear transition.

First, reaction times at the Critical target in the Algorithmic condition remained substantially longer than those in the Retrieval condition throughout training. If participants had cached the aiming solution for the Critical target, we would expect preparation times at that location to be the same as the Retrieval condition. However, the RTs for the Algorithmic and Retrieval conditions are significantly different in the last block of training. 

Second, within the Algorithmic condition, reaction times at the Critical target remained similar to those at the Non-Critical targets. Selective caching of the Critical target predicts a different pattern: preparation should become faster at the Critical target than at the surrounding locations, where participants would still need to compute the appropriate aiming solution. However, we do not observe a significant difference between RTs at Critical and Non-critical targets for the Algorithmic conditions at the end of the training block. Taken together, these two observations suggest that the Critical target continued to be treated similarly to the other members of the 10-target set rather than becoming a privileged, cached stimulus–response association.

Third, participants would have to single out the Critical target as being distinct. All targets had the same visual appearance, the Critical target was never presented on consecutive trials, and participants were not informed that it had a special role in the experiment. However, we acknowledge that its higher sampling frequency, its somewhat greater separation from neighboring targets, and the location of the subsequent exclusion trials could nevertheless have made it more salient. Thus, we cannot rule out selective caching solely from the task structure.

For this reason, we agree that the reviewer’s proposed analysis provides a useful additional test. If the Critical-target strategy progressively transitioned from algorithmic computation to retrieval, one prediction is that the generalization function in the Algorithmic condition should become narrower across successive exclusion blocks and increasingly resemble that of the Retrieval condition. We will therefore attempt to estimate the width of the generalization functions as a function of the training block between the Algorithmic and Retrieval conditions.

There is, however, an important limitation to interpreting block-by-block generalization functions in this experiment. Implicit recalibration is both plan-based and temporally labile. Generalization is centered around the planned aiming direction (McDougle et al., 2017), and recent work indicates that implicit adaptation can decay over relatively short intervals (Zhou et al 2017; Hadjiosif et al 2023). Consequently, the first trial of an exclusion block provides the cleanest sample of the current state of implicit recalibration. Across later trials in the block, the measured response can be influenced both by temporal decay and by where the sampled target falls relative to the participant’s current aiming direction.

To minimize systematic sampling bias, the starting exclusion target was randomized across participants. This means that these effects should average out at the group level, but individual exclusion blocks do not provide equally precise samples of the entire generalization function. A fully balanced estimate of every position within each exclusion block would require substantially more participants than were included in the present experiments. We will therefore present the blockwise analysis while interpreting changes in the estimated breadth cautiously.

(2) The error-clamp paradigm in Experiment 3 introduces two problems. First, it breaks the relationship between planned movement direction and feedback of movement direction, likely reducing the sense of agency over movement feedback (indeed, typical error clamp study instructions tell participants to ignore the movement feedback). Reduced agency may itself suppress differences between algorithmic and caching conditions. First, if strategy type exerts its influence on implicit recalibration via the explicit plan - as the plan-based generalization account predicts - then severing the link between intended movement and feedback might close off the channel through which strategy could shape the implicit system, regardless of which strategy is used. Second, reduced agency could modify the explicit strategies themselves. For caching, the stimulus-response association might be reinforced by a consistent relationship between intended movement and observed outcome; the clamped feedback may make it more difficult to reinforce the cached response, weakening the stimulus-response association. For the algorithmic strategy, effortful mental rotation may depend on the perception that the computation meaningfully determines the outcome; as participants understand that clamped feedback does not depend on their behavior (although yes, the text-based "Excellent/Good Move feedback) does depend on their behavior, they may engage in somewhat less complete mental rotation. Both possibilities could contribute to convergence between groups in generalization. It is noted that the preserved RT difference between groups in Experiment 3 partially argues against a loss of effort under the algorithmic condition, but it does not rule out weakened formation of stimulation-response associations during caching.

The reviewer raises an important point. By design, the error-clamp manipulation in Experiment 3 decouples the participant’s planned movement from the visual consequence of that movement. While this gives us precise control over the error driving implicit recalibration, it could reduce agency over the cursor and thereby alter the interaction between explicit strategy and implicit learning in ways that are difficult to rule out completely. In particular, as the reviewer notes, reduced agency could potentially weaken either the influence of the explicit plan on implicit recalibration or the strategies themselves. Because Experiment 3 was intended to test for the absence of a strategy-dependent difference in implicit recalibration, we acknowledge that higher-order interactions of this kind represent an inherent limitation of our study if Experiment 3 is taken in isolation. 

There are nevertheless several observations that make us think that reduced agency is unlikely to provide the primary explanation for the convergence between groups. First, the progression across Experiments 1–3 is informative. In Experiment 1, where participants retained normal control over the cursor, the broader generalization function in the Algorithmic condition closely mirrored the broader distribution of reach directions. This relationship suggests that the apparent difference in implicit generalization could arise from differences in where participants planned their movements rather than from a direct effect of strategy type on the implicit system. In Experiment 2, we sought to reduce the difference in the distribution of planned movements while preserving normal action–outcome contingencies and, importantly, the generalization functions became correspondingly more similar. Experiment 3 then controlled the error signal itself and again produced similar generalization across strategy conditions. Taken together, this progression favors the interpretation that strategy affects the measured generalization function indirectly, through differences in the distribution of movement plans, rather than directly altering the underlying implicit recalibration process.

We nevertheless agree that these experiments cannot exclude all possible interactions between explicit and implicit learning systems. Indeed, whether these systems interact directly has been an important and persistent question in the sensorimotor adaptation literature. Several studies have reported evidence consistent with direct interactions (e.g., Albert et al., 2022; Maresch and Donchin 2021; t’Hart and Henriques 2024), whereas our own work has generally pointed toward indirect interactions mediated by factors such as movement planning and the current state of implicit adaptation (Taylor et al 2010; Taylor and Ivry 2011; McDougle et al 2017). Indeed, our recent study was designed specifically to distinguish these possibilities under tighter experimental control (Chen and Taylor, 2026), yet we found that the interaction between explicit and implicit processes is more complex than a simple independent-versus-interacting dichotomy. Going forward, we think it is more cautious to first rule out low-level statistical or distributional differences that could account for apparent effects before invoking higher-order interactions between learning systems.

Finally, one motivation for the present study was that much of the literature on implicit generalization trains participants at a single target location before measuring generalization across the workspace. Under such conditions, participants have ample opportunity to retrieve a stable target-specific aiming solution. If algorithmic and retrieval strategies fundamentally alter implicit generalization, then many existing estimates of generalization may characterize implicit learning under retrieval-like conditions rather than providing a strategy-independent property of the implicit system. Across the present experiments, we find little evidence for such a fundamental difference once the distribution of movement plans and the experienced error are better controlled. We therefore think the most parsimonious interpretation of the current results is that algorithmic and retrieval strategies primarily influence implicit generalization indirectly through how movements are planned. 

We plan to revise the manuscript to acknowledge that Experiment 3 cannot completely rule out higher-order effects associated with reduced agency under error-clamp feedback. We will also provide additional validation that participants were implementing distinct strategies, beyond the group-level RT differences, by testing whether RT in the Algorithmic condition scales with the instructed rotation magnitude, and whether RT variability shows group-level difference (Logan, 1988). If present, this relationship would provide stronger evidence that participants continued to engage the intended strategy under the clamp. We agree, however, that confirming distinct strategy use would not by itself rule out the possibility that reduced agency altered how those strategies interacted with implicit recalibration.

Reviewer #3 (Public review):

Summary:

This manuscript asks whether two forms of explicit strategy use in visuomotor adaptation, i.e., algorithmic mental rotation and retrieval of a cached aiming solution, differentially influence implicit recalibration. The question is relevant because much prior work treats explicit strategy as a unitary process, whereas the algorithmic/retrieval distinction is theoretically meaningful and grounded in cognitive theory. Across three experiments, the authors report that algorithmic strategy conditions initially produced broader fitted implicit generalization functions than retrieval conditions, but that this difference was reduced or eliminated when reach variability and sensory prediction errors were more tightly controlled.

Strengths:

The paper is clearly written, theoretically well-motivated, and employs a commendably transparent and progressive experimental logic. The three-experiment structure, in which confounds are systematically identified and addressed, represents a strong model of cumulative experimental design (I will certainly use it in teaching courses on experimental methods):

Experiment 1 establishes an apparent difference in implicit generalization breadth. Experiment 2 attempts to reduce error spillover from Non-Critical targets by increasing angular separation and using delayed endpoint feedback. Experiment 3 uses an error-clamp design to decouple variable reaching from error feedback. This sequence is appropriate for testing whether the initial difference reflects a strategy-dependent change in implicit recalibration or instead follows from the distribution of movement plans and error exposure. The authors also provide reaction-time and performance data that are broadly consistent with the intended distinction between algorithmic and retrieval-like task performance.

We thank the reviewer for this thoughtful and constructive assessment of the manuscript. We especially appreciate their recognition of the progressive experimental logic across the three experiments and of the broader theoretical motivation for distinguishing algorithmic and retrieval-based strategies. We are also grateful for the reviewer’s comments on the clarity and transparency of the work.

Weaknesses:

The evidence does not support the strongest claims made in the manuscript, namely that algorithmic and retrieval strategies generally do not reshape implicit recalibration.

In general, I am skeptical of the authors' interpretation of null results. Several central conclusions depend on non-significant group differences, especially in Experiment 3. Non-significant tests are repeatedly treated as evidence that groups are equivalent or that confounds are absent (e.g., implicit recalibration magnitude (Algorithmic: 11.43 {plus minus} 6.43{degree sign}; Retrieval: 15.49 {plus minus} 8.99{degree sign}; t(38) = −1.65, p = .11), adaptation level before Exclusion probes (F(1,256) = 3.04, p = .08) and Exclusion RT differences (F(1,266) = 3.15, p = .08), whereas a modest model-dependent breadth effect (bootstrap p = .02) is treated as meaningful (for more on the model-dependent breadth effect, see below).

Without confidence intervals, equivalence tests, or Bayesian analyses, I think that the authors' interpretations comprise an inferential gap. A failure to find a significant difference is not equivalent to evidence of equivalence, particularly given that the implicit recalibration signal gets progressively attenuated across experiments (Experiment 1: ~16-17{degree sign}; Experiment 2: ~11-15{degree sign}; Experiment 3: ~7-8{degree sign}). With a substantially diminished signal in Experiment 3, the null result could partly reflect reduced statistical sensitivity rather than true equivalence.

We agree with the reviewer that our original interpretation of several non-significant effects was too strong, especially without providing some form of equivalence test. Our central hypothesis predicts little or no difference between algorithmic and retrieval-based strategies under conditions in which movement plans and error exposure are controlled, and we therefore face the inherent difficulty of drawing conclusions from an expected null effect. As the reviewer notes, a non-significant conventional hypothesis test does not by itself provide evidence that two conditions are equivalent.

We therefore plan to supplement the existing analyses with quantitative assessments of the strength of evidence for the null/equivalence, using Bayesian factor analyses to confirm whether two conditions are equivalent. These analyses will allow us to distinguish between effects that are sufficiently small to support our theoretical interpretation and effects for which the data are simply inconclusive. We will also revise the manuscript throughout to avoid treating p > .05 as evidence of equivalence in the absence of such supporting analyses.

We also now appreciate that the magnitude of implicit recalibration decreases progressively across experiments. This reduction could diminish our sensitivity to differences between the Algorithmic and Retrieval conditions and therefore represents an important qualification on the null result. Because the experiments used similar trial structures and were conducted with the same experimental equipment, the source of this reduction is not immediately clear. The block-by-block analysis suggested by Reviewer 2 may provide useful insight into how implicit recalibration evolves over the course of training and whether this attenuation emerges gradually within experiments.

My main technical concern is the analysis of generalization breadth already alluded to. The central claims rely on group-level Gaussian fits to only seven Exclusion probe locations spanning −45{degree sign} to +45{degree sign} around the Critical target. In several cases, the fitted centers and widths are poorly constrained by the sampled range. For example, in Experiment 2 the algorithmic group's fitted center is shifted to approximately 29{degree sign}, meaning that the probe range samples the function asymmetrically relative to its own peak. In Experiment 3, fitted centers are near or outside the sampled range, while estimated widths are very broad. Under these conditions, the width parameter may partly reflect extrapolation or parameter trade-offs between center, amplitude, and width rather than a genuine difference in generalization breadth.

Based on prior work characterizing implicit generalization in relative isolation from explicit strategy (Morehead et al., 2017; Poh and Taylor, 2019), we expected a relatively narrow generalization function, with a full width at half maximum of approximately 30°. We therefore expected probes spanning −45° to +45° around the Critical target to capture most of the function. At the same time, prior work on plan-based generalization predicts that the function should shift toward the participant’s aiming direction (Day et al., 2016; McDougle et al., 2017; Chen and Taylor, 2026), which complicates the choice of where to center the probes. Expanding the range and density of probe locations is also not cost-free, because additional exclusion trials increase temporal decay (Hajiosif et al., 2023) and begin to overlap with trained locations.

We nevertheless agree with the reviewer that, when the fitted center approaches the edge of the sampled range, estimates of Gaussian width can become poorly constrained and may partly reflect parameter trade-offs or extrapolation beyond the observed data. We therefore plan to test whether the group differences persist when the Gaussian fits are constrained so that their centers fall within the sampled range. We will also examine complementary nonparametric measures of generalization breadth, such as the area between the group generalization curves across the sampled probe locations. Convergence across these approaches would provide stronger evidence that the reported differences reflect the observed shape of the generalization functions rather than instability in the Gaussian parameter estimates. If the results are not robust across approaches, we will revise the manuscript to qualify the interpretation of the fitted width estimates accordingly.

Lastly, I think that the authors' use of an error-clamp paradigm is, from an experimental point of view, quite elegant. By controlling the sensory prediction error independently of reach direction, they can isolate implicit recalibration from the confounds identified in Experiments 1 and 2. However, I see a fundamental problem or question concerning construct validity here: In Experiments 1 and 2, the algorithmic strategy was operationalized as participants computing a counterrotated aiming direction in response to a visible cursor rotation. This is a naturalistic context where mental rotation is both required and meaningfully connected to task success. In Experiment 3, however, there is no visuomotor rotation to compensate for. The error-clamp renders the cursor feedback task-irrelevant. Instead, participants are instructed via text commands (e.g., "move towards 45{degree sign}") to reach invisible locations, rendering the "algorithmic strategy" in this context essentially an instructed spatial navigation toward arbitrary angular locations, not genuine visuomotor mental rotation driven by an error signal.

To put it differently, are we sure that the cognitive process engaged by the algorithmic group in Experiment 3 is the same as the algorithmic mental rotation strategy in Experiments 1 and 2? If not, then the null result in Experiment 3 may not speak to the original question about how algorithmic strategies interact with implicit recalibration after all. Instead, it may reflect the absence of a genuine strategy manipulation.

This concern is closely related to that raised by Reviewer 2. We are fairly confident that participants in Experiment 3 were nevertheless engaging in the intended strategy manipulation. Participants in the Algorithmic condition showed substantially longer RTs than those in the Retrieval condition, and they were able to accurately generate the instructed angular reach directions across trials. The two conditions also differed in the variability of both RT and reach direction, consistent with online computation of an aiming solution in the Algorithmic condition and retrieval of a more stable cached response in the Retrieval condition. We can provide an additional validation by examining the relationship between RT and reach angle and comparing RT variability across two conditions. If RT scales parametrically with instructed reach angle in the Algorithmic condition but not in the Retrieval condition, this would provide stronger evidence that participants were engaging an online mental-rotation-like computation rather than simply following arbitrary spatial instructions. Moreover, RT yielded by the retrieval strategy would tend to be less variable than the algorithmic strategy.

We agree, however, that this does not fully address the reviewer’s broader concern. Experiment 3 necessarily changed the context in which the strategy was implemented. In Experiments 1 and 2, mental rotation was used to counteract a visuomotor perturbation and was therefore directly tied to successful control of the cursor. In Experiment 3, the error clamp removed this instrumental relationship: participants still had to compute and execute different angular reach directions, but those computations no longer determined the visual cursor outcome. In that sense, the algorithmic process in Experiment 3 was less naturally embedded in the task and could reasonably be viewed as a somewhat different instantiation of the task.

We therefore acknowledge that Experiment 3 cannot establish with certainty that the same higher-order cognitive process was engaged in exactly the same way as in Experiments 1 and 2, nor can it rule out the possibility that this change in task relevance altered how explicit strategy interacted with implicit recalibration. At the same time, when considered together with Experiments 1 and 2, we think the overall pattern remains informative. The apparent strategy-dependent difference in generalization was largest when movement plans and error exposure differed most, became smaller when these factors were better controlled while normal action–outcome contingencies were preserved, and was eliminated when the error signal itself was experimentally controlled. This progression is more consistent with an indirect influence of strategy through differences in movement planning and error exposure than with a robust direct effect of strategy type on implicit recalibration.

Nonetheless, we agree that Experiment 3 should not be interpreted as a definitive test of whether algorithmic strategy, in its more relevant visuomotor adaptation context, can lead to different interactions with implicit recalibration compared to a retrieval strategy. We plan to revise the manuscript to make this limitation explicit.  

To their credit, the authors report a compelling RT dissociation that mirrors Experiments 1 and 2: The algorithmic group shows slower RT, which is decreasing over training (0.98s → 0.76s), whereas the retrieval group exhibits faster, stable RT (0.52s → 0.45s). While this pattern is consistent with genuine strategy differences persisting in Experiment 3, it could also reflect the greater spatial precision demands of reaching to invisible targets from text instructions, rather than genuine mental rotation per se. Reaching to an invisible location defined by a verbal angular label is inherently more demanding than reaching to a visible target, regardless of strategy type, and this demand is asymmetrically present in the two groups, since Non-Critical targets are invisible for the algorithmic group but visible for the retrieval group.

Thus, from my point of view, experiment 3 should not be used as definitive evidence that algorithmic and retrieval strategies during standard visuomotor adaptation cannot differentially influence implicit recalibration.

We agree that the RT difference in Experiment 3, by itself, cannot rule out the possibility that the Algorithmic condition imposed greater spatial precision demands because participants were reaching to invisible locations specified by angular instructions. We can, however, test for a more diagnostic signature of algorithmic computation by examining whether RT scales parametrically with the instructed reach angle. A general cost associated with reaching to invisible targets could increase overall RT, but it would not necessarily predict the characteristic increase in preparation time with the magnitude of the required angular transformation.

We will therefore examine the relationship between RT and instructed reach angle in Experiment 3. If RT increases systematically with angular displacement in the Algorithmic condition, this would provide additional evidence that the longer RTs reflect online computation of the instructed aiming direction rather than simply the greater difficulty of reaching invisible targets.

We can also compare this RT–angle relationship across experiments. If participants are engaging the same underlying algorithmic computation in Experiments 1–3, we would expect the slope relating RT to angular displacement to be similar across experiments, even if the overall intercept differs because of differences in task structure and spatial demands. A comparable slope would therefore provide converging evidence that the same computational process was engaged despite the altered task context in Experiment 3.

We acknowledge, however, that similarity of the slopes would itself require yet another inference from a null difference and should therefore be interpreted cautiously. As with the generalization functions, we will use a Bayes factor analysis to quantify the strength of evidence for the null.

Overall, the manuscript addresses a meaningful question and the multi-experiment structure is useful. The evidence is incomplete for the broad claim that implicit recalibration is insensitive to strategy type. The study would make a clearer contribution if the authors narrowed the claims, strengthened the generalization analyses, and treated null effects with appropriate inferential tools.

Based on the reviewers’ comments and the additional analyses they have suggested, we think we will be able to place our conclusions on a firmer empirical footing while also tightening and narrowing them. In the revised manuscript, we will strengthen the generalization analyses, use more appropriate inferential tools for interpreting null effects, and temper our broader claims about the insensitivity of implicit recalibration to strategy type. We will also more explicitly acknowledge the limitations of the present experiments, especially Experiment 3.

Author response:

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

Reviewer #1 (Public review):

Summary and Strengths:

Shin et al deepen our understanding of high-frequency oscillations in the frontal cortex during REM in a manner that sheds important light on the roles of these events. In particular, they reveal that cortical HFOs are modulated by theta oscillations, occur in chains and recruit cortical neuronal activation patterns in a manner that is distinct from other high-frequency events during non-REM or in the hippocampus. They also show that these events occur during increased oscillatory cross-talk between hippocampus and cortex and may protect cortical neurons from downregulation of firing during sleep. Overall, this is important work with several novel observations pointing towards an important role for these events that will become increasingly understood over time.

I also wanted to comment that 2D is a beautiful illustration of separate and essentially exclusive communication channels used during HF events in NREM vs REM. They almost perfectly complement each other's frequencies.

Weaknesses:

I have only one major scientific critique: I believe we need to see quantification of how phasic REM theta waves with versus without HFOs differ. What do REM HFOs add to the "normal" theta oscillation? Without this comparison, it is more difficult to interpret the meaning of these events. Given that HFO chains have IEIs around the time of a theta cycle duration, are the repeating spiking activities stronger during HFO repeats than during adjacent theta waves without HFOs?

Here, we provide additional analyses to demonstrate that the phasic, theta-modulated PFC activity that we observe during HFOs is specifically tied to the occurrence of HFOs and not a strong phenomenon during non-HFO-associated theta periods. In Figure S5 M (middle and right), we find that aligning PFC multiunit activity to theta periods in phasic REM but temporally distant from HFOs does not elicit the same degree of theta-modulated activity as aligning to HFOs (as in Figure 2A and Figure S5 M, left).

Additionally, we provide analyses of the theta periods adjacent to HFOs (at different temporal thresholds) and demonstrate that this theta-modulated spiking activity is largely absent (Figure S5; compare to Figure 2A). Unlike Figure S5, this analysis was not restricted to putative phasic REM.

We have now added Supplementary Figures S5L-N to the revised manuscript.

What percentage of theta waves contain HFOs, and what is the firing rate during those theta waves with vs without HFOs? Is there differential firing rate modulation? The authors may even consider that all REM-HFO-specific quantifications should be shown as differential from phasic theta cycles without HFOs.

Although theta oscillations are continuously expressed during REM sleep, HFOs occur only intermittently, such that only a small subset of theta cycles contain HFOs. Across all animals and epochs included for analysis, we found that ~7.4% of theta cycles contain HFOs. We present an epoch-level quantification of this in Author response image 1, where the proportions were calculated across all, tonic, and phasic theta cycles. As expected, a higher proportion of putative phasic theta cycles contain HFOs.

Regarding differential firing rate modulation, we refer reviewer to normalized MUA plots in the manuscript (Figures 2A and 4F). We would like the emphasize that what we show is PFC multiunit activity that is normalized by the mean population firing rate during REM sleep. Thus, these figures, specifically the chain HFO aligned figure, indicate that there are peaks in activity around baseline level in the background of an overall decrease in population activity relative to baseline (i.e. the troughs surrounding the peaks have lower activity compared to baseline, as in Figure 9C). While this suggests that there is an overall decrease in firing rates during HFOs as compared to baseline theta periods without HFOs, this simply provides a qualitative account of this difference. In Figure S5N, we present firing rate comparisons during HFO chains versus theta periods during putative phasic REM bouts at least 4 theta cycles away from HFOs. We find that HFO chain-associated PFC neuron firing rates are lower compared to non-HFO theta periods, supporting our finding of activity suppression during HFOs.

Author response image 1.

Proportion of theta cycles with HFOs. (A) Proportion of theta cycles with HFOs across all, tonic, and phasic cycles (***p = 4.90e-05, rank sum test).

Lastly, we appreciate the reviewer's suggestion that REM HFO quantifications could be framed relative to phasic theta cycles without HFOs. We agree that such comparisons are informative and ensure that the results we present are specific to periods with detected HFOs. In response, we have added additional analyses of theta periods outside of HFOs in Figure S5. Furthermore, while we found that a larger proportion of chain HFOs occurred during bouts of putative phasic REM compared to isolated events (Figure S5 and Figure S3C), most of the analyses that we performed were on events pooled across putative tonic and phasic, since putative phasic REM is relatively scarce (<10%).

We also refer the Reviewer to our response to Reviewer 2’s major comment #1 below where we reiterate several of our findings that demonstrate the HFO-specificity of the reported dynamics, as well as our extended response to Reviewer 3’s Public Review comment #1 where we show that the dynamics associated with REM HFOs are absent during HFOs detected during awake behavior (comparable theta state) on the W-Track (Figure S11). We hope that the additional control analyses we present as well as our expanded explanations adequately address the Reviewer’s concerns.

As a non-scientific comment on the manuscript itself: unfortunately, the paper is difficult to read and understand at times, requiring great effort by the reader. This is to an extent that communication is hindered. The paper is dense with changing methods, often from panel to panel. Unfortunately, the panel quantifications are not explained in the results section in a manner that readers can understand without going to read the methods, often for each individual panel. These measures should be explained in a way that lets readers understand the conclusions of each panel and what gross calculations were used to reach those. Instead, too much jargon is used rather than clear descriptions of the overall calculations being done for each panel.

We have now split and updated the figures in a more logical progression of ideas:

Figure 1: Prefrontal cortical HFOs in REM sleep using spectral analyses.

Figure 2: Characteristic spiking modulation in PFC during REM HFOs.

Figure 3: HFO and gamma distinction in theta cycles, and PFC-CA1 coherence (including chain/ isolated HFOs in phasic and tonic REM stages).

Figure 4: Differential modulation of PFC spiking activity during REM PFC HFOs vs. NREM PFC ripples.

Figure 5: Characteristic PFC population activity during REM HFO chains.

Figure 6: Comparison of PFC reactivation during REM PFC HFOs vs. NREM PFC ripples.

Figure 7: Differential engagement and excitability modulation of CA1 neurons by REM HFOs.

Figure 8: REM theta phase shifting CA1 neurons preferentially engaged by REM HFOs.

Figure 9: (Model) Network model with ACh reproduces spiking modulation during REM PFC HFOs vs NREM PFC ripples.

Figure 10: (Model) Model reproduces restricted REM coactivity vs. widespread NREM coactivity.

We have also rearranged the figures to parallel the main figures and results section.

The authors mention in the discussion section that they see increased functional connectivity between mPFC and CA1, but most data suggesting this seems to be based on LFP rather than spiking. Functional connectivity is best defined by spiking-spiking relationships. And these authors have spiking data. So I believe either the descriptive language should be pulled back to something like "oscillatory coupling" or more analyses should be dedicated to showing spike-spike coordination across regions.

We have updated the manuscript accordingly. Specifically, we have modified the text on Page 13, Lines 23-24:

“These chains are associated with increased measures of oscillatory coupling between PFC and CA1…”

Reviewer #1 (Recommendations for the authors):

(1) Please ensure that analytical methods are presented in the same order in the methods section as they are in the results section - panel by panel. That said, the methods section is well-written and presented.

We apologize for any confusion this may have caused. We have now reorganized the methods section to ensure they presented in the same order as the panels in the main figures.

(2) Please specify whether the recordings/behaviors occur during the animal's light circadian phase.

We have added a statement in the methods under the “Behavior” section on Page 34, Lines 9-12 indicating that the experiments took place during the light phase:

“During the recording day, animals were introduced to the novel W-maze (~80 × 80 cm with ~7 cm wide tracks) for the first time and learned the task rules over eight behavioral sessions during the animals’ light phase between the hours of 9 AM and 6PM.”

(3) Please specify how many tetrodes are in mPFC and how many in CA1?

We have added this clarification on Page 33, Lines 27-28:

“Tetrodes were split equally between PFC and CA1 (15, 16, or 32 tetrodes in each region).”

(4) All mentions of "coherence" should have frequency bands specified. "Theta coherence", for example.

We have now added this information to all relevant mentions of “coherence”.

(5) The intuitive logic of the phase slope index (2K) should be briefly explained for maybe half a sentence in the results section. The intuition should be explained better in the methods section devoted to it.

We have added more clarification on the phase slope index method, both in the legend of Figure 3 on Page 21, Lines 22-23:

“Phase slope index (PSI), which is a measure of phase lag consistency across different frequencies…” and in the methods section under “Phase slope index” on Page 39, Lines 21-26:

“In practice, PSI is used to assess the consistency of phase lag relationships between two signals across different frequency bands and is a measure that is weighted by oscillatory coherence. We opted to use PSI to estimate the directional flow of information instead of other methods, such as Granger causality, since it has been demonstrated that PSI is less prone to false positives.”

(6) "Cofiring" and "coactivity" should be defined clearly as measures - preferably in the results section if possible. They sound similar and are somewhat jargon-y without self-explanatory meaning (or difference from each other). How should readers understand and interpret them?

We apologize for the confusion regarding these two terms, which are both used throughout the manuscript. Here, we specifically used to term “cofiring” to specify the explicit quantification of coincident activity between pairs of neurons (e.g. Figure 4E, left) as described in the Methods section under “Ripple and HFO co-firing”. There were instances where “coactivity” was used to refer to this quantification, and they have been changed to “cofiring”. We have now added a statement to the manuscript to clarify that “cofiring” is a quantification of coincident activity between neurons on Page 7, Lines 34-35:

“Overall cortical co-firing, which is a measure of coincident activity between neuron pairs during discrete events”

Additionally, the term “coactivity” in the manuscript is used when describing neuronal activity in the model or when there are mentions of coincident activity other than the explicit quantification described above.

(7) The temporal threshold for "cofiring" should be stated in the results to enable interpretation of the results.

We apologize for the lack of clarity regarding the cofiring metric. Here, the temporal threshold that we are imposing is determined by the ripple/HFO event times (see Methods section “LFP event detection”). If both neurons in a pair emit spikes within the defined window of an event, they are considered to have “cofired” (Cheng and Frank 2008, Singer and Frank 2009, Sosa, Joo et al. 2020).

We have now clarified this in the results section on Page 7, Lines 34-35:

“Overall cortical cofiring, which is a measure of coincident activity between neuron pairs during discreet events…”

We have also added a clarifying statement in the Methods section under “Ripple and HFO cofiring” on Page 40, Lines 24-25:

“Here, cofiring assesses coincident activity between neuron pairs within the start and end times of events, and thus, no explicit temporal threshold was implemented.”

(8) Please clarify more systematically in which region the NREM ripples were detected. The natural assumption is the hippocampus, but at times it is mentioned that they are detected in the cortex. Are they cortical in all analyses? Readers could easily get confused about this and misinterpret "ripples". To clarify further, if these are always cortical events, I suggest renaming "ripples" in this text to "cortical NREM HFOs".

We apologize for the confusion. For all mentions of “ripples” in the text, we are referring to PFC ripples specifically in NREM sleep. When hippocampal ripples are mentioned, we differentiate them by explicitly using “sharp-wave ripples” or “SWRs”. Our decision to use “ripples” for NREM sleep was based on previous studies that investigated NREM high-frequency events in cortex (Khodagholy, Gelinas et al. 2017, Helfrich, Lendner et al. 2019, Vaz, Inati et al. 2019, Aleman-Zapata, Morris et al. 2022, Ghosh, Yang et al. 2022, Shin and Jadhav 2024). Furthermore, we elected to use the “HFO” nomenclature for high-frequency events in REM sleep, since it has been used in previous studies to describe these events (Tort, Scheffer-Teixeira et al. 2013, Bueno-Junior, Ruckstuhl et al. 2023). Thus, to remain consistent with the literature, we decided to use these terms to describe these sleep-state-specific events throughout the manuscript:

Hippocampal sharp-wave ripples (SWRs) in NREM sleep

PFC ripples in NREM sleep

PFC HFOs in REM sleep

We have now added the following statement on Page 5, Lines 1-3:

“However, to avoid ambiguity, and to conform to previous nomenclature, we refer to cortical NREM events as ripples, cortical REM events as HFOs, and hippocampal sharp-wave ripples in NREM as SWRs throughout.”

(9) The analysis performed for 4B is not explained clearly. It is somewhat better explained in the methods. I believe the reader should understand that each HFO is treated as an event, and spiking participation per unit was measured, and then the similarity of that pattern was assessed between HFOs. I also find the x-axis being quartiles makes understanding this graph particularly difficult.

Why not label by raw lag and show a correlation plot rather than break down by quartiles? Alternatively, labeling the millisecond values of these quartiles on the x-axis labels may make comprehension much easier.

We apologize for the lack of clarity regarding this method. We have added points to clarify the analytical procedure used for Figure 4B (Now Figure 5B) on Page 8, Lines 25-28:

“We represented each HFO as a binary vector of PFC neurons active during the event, and computed the Pearson correlation between the vectors of every pair of consecutive HFOs” As well as in the Figure 5 legend on Page 24, Lines 7-10:

“Here, the PFC spiking activity during each HFO was binarized across all neurons and the Pearson correlation coefficient was calculated between adjacent events as a measure of pattern similarity. Then the relationship between pattern similarity and IEI was reported.”

In addition to the quartile labels, we have now added the average inter-event interval (IEI) of each quartile to the x-axis labels of Figure 5B to improve comprehension as well as a statement in the figure legend on Page 24, Line 11:

“Below each quartile is the average IEI of that quartile in milliseconds.”

(10) "Rank order analysis" should be again defined in the results in a manner that the reader can follow the point of the analysis and figure. For example, the goal is to assess the spike sequence across HFO events by looking at the regularity of spike timing rank for each neuron in each HFO event. Also, could this correlation be more simply calculated and presented as just a standard deviation around the mean of that cell's rank?

We apologize for not including an explanation of this analysis in the results section. We have now added more detail about the rank order analysis to the Figure 5 legend on Page 24, Lines 18-21:

“The mean rank-order correlation from the leave-one-out cross-validation procedure. Each event’s rank was correlated with the averaged rank across all other events. The average across all events compared to a distribution of means generated by jittering (n = 1000) spike times is shown.”

We also provided a short description of the procedure in the results section on Page 8, Lines 32-36:

“Furthermore, we examined whether the order in which individual PFC neurons fired during HFOs within a chain was preserved across chains. For each chain, we extracted each cell's first-spike rank order and compared it to a leave-one-out template constructed from the average normalized rank across all other chains.”

Regarding the Reviewer’s second comment about the correlation, if we presented the result as the standard deviation around the mean of the cell’s rank, the result would be similar to the example rank order in Figure 5C, which we provided as a visualization of the rank-order template procedure we used. However, this would not necessarily demonstrate the consistency of population activity across HFO chains. To demonstrate consistency in activity across HFO chains, we used a leave-one-out cross-validated approach where each chain event was assessed separately. For each event, the neurons firing during that event was ranked and normalized 0-1. Then, the average rank of each neuron across all other events was calculated. Lastly, the correlation between the ranks of the left-out event and the average ranks of the template was taken to assess similarity in sequential activity. We opted to use this method since it has been demonstrated to be effective for evaluating similarities in sequential across events (Stark, Roux et al. 2015, Valero, Viney et al. 2021).

(11) In Figure 5B and the related results section, I gather that "spatial" relates to place field location rather than anatomical/tetrode location of the neuron? This was not my original understanding and should be stated clearly.

We apologize for the lack of clarity regarding this result. Yes, the term “spatial” refers to spatial rate map correlation between CA1 neuron pairs, specifically during the behavioral W-Track session prior to the sleep session where cofiring was assessed. We have updated the y-axis label of Figure 5B (Now Figure 7B) to include “rate map” and have updated the results section on Page 9, Lines 32-33:

“…we observed a higher degree of spatial rate map correlation for high cofiring pairs…”

(12) Figure 5E and its caption are almost totally unable to be explained since axes aren't explained well in either. It is only by inference from the results text that meaning can be assumed.

We apologize for the lack of clarity regarding Figure 5E (Now Figure 7E). We have now updated the y-axis labels on both updated figures (Figures 7E and 8B) and have reworded and added more detail to the figure legend on Page 28, Lines 1-5:

“High REM PFC HFO cofiring CA1 neurons exhibited a greater degree of suppression during NREM PFC ripples. For a description of modulation index, see Methods section Ripple/HFO aligned modulation. Here, since CA1 neurons exhibit a robust decrease in activity in response to NREM PFC ripples, we refer to the modulation as suppressive.”

(13) Figure 5F is interesting, supporting the concept that HFOs "protect" neurons from downscaling. However, how can a "neuron" be cofiring? Would cofiring not be defined in a pairwise manner, and so each unit of the cofiring measure would be a pair of neurons? This question applies to other panels in this figure. Please clarify this.

We apologize for the lack of clarity regarding the exact cofiring metric that we use. For Figures 7D-F and 8A, since we wanted to relate cofiring to changes in firing rate and modulation state during NREM PFC ripples, we calculated single cofiring values for each CA1 neurons by averaging across all pairings with PFC neurons. Thus, this metric gives us an estimate of the overall cofiring strength of each CA1 neuron. We have now added a new section in the Methods under “Calculation of a single cofiring metric and separation into populations of high and low cofiring neurons” on Page 44, Lines 34-43:

“Since we wanted to relate the above cofiring metric to other measures, we needed to obtain a single-value cofiring metric for each neuron. To do this, we averaged the cofiring values across all pairings for a neuron (e.g. 1 CA1 neuron paired with all PFC neurons) and reported it as the cell’s cofiring. Furthermore, since we observed a bimodal distribution of CA1-PFC cofiring values in REM sleep, we split the population based on whether the average (across all cell-cell combinations) cofiring value or correlation coefficient of a cell was above or below 0 (High cofiring > 0; low cofiring < 0). Also, since the NREM ripple cofiring distribution was unimodal, we additionally split the populations using the mean of the average cofiring or correlation coefficient distributions (High cofiring > mean; low cofiring < mean).”

We have also clarified this in the Figure 7 legend on Page 27, Lines 25-28:

“For comparisons between cofiring and other metrics (e.g. firing rate), a single cofiring value was calculated for each neuron by averaging the cofiring metric across all neuron pairings. Additionally, high and low cofiring CA1 neurons were split based on average cofiring values > 0 and < 0, respectively.”

Reviewer #2 (Public review):

Summary:

In this study, the authors investigate high-frequency oscillations (HFOs) in the prefrontal cortex during REM sleep. They identify a specific pattern where these HFOs occur in "chains" that are phase-locked to theta oscillations, primarily during the "phasic" periods of REM. The study contrasts these events with isolated HFOs and NREM ripples, suggesting a unique role for these chains in coordinating activity between the prefrontal cortex and the hippocampus. Most notably, the authors report that a specific subset of hippocampal cells-those that co-fire with the prefrontal cortex during these HFOs-increase their firing rates over the course of sleep, suggesting a potential mechanism for selective memory consolidation.

Strengths:

The study addresses an under-explored area of sleep physiology: the fine-grained temporal coordination between the cortex and hippocampus during REM sleep. The identification of HFO "chains" and their association with higher theta power provides an interesting framework for understanding how the brain might organize information transfer outside of NREM sleep. The observation that specific hippocampal populations show differential firing rate changes based on their participation in these HFO events is a striking finding that warrants further investigation.

Weaknesses:

The primary weakness of the study lies in the lack of a clear distinction between global brain states and the specific events being analyzed. Because the authors compare HFOs across different sleep stages (NREM, tonic REM, and phasic REM) without sufficient controls, it is difficult to determine if the observed differences are intrinsic to the HFOs themselves or simply a reflection of the different physiological states in which they occur.

We would first like to note in case it was unclear – as clearly noted in our manuscript title, state-dependence is an integral part of our results, with the primary comparison in the manuscript being between REM cortical HFOs and NREM cortical ripples, and correspondingly spiking activity patterns observed in prefrontal cortical-hippocampal circuits during these event-types that occur in the two sleep stages. As noted in response to Reviewer 1’s Comment #8 and Reviewer 3’s Comment #1, to avoid ambiguity and to remain consistent with existing literature, we use the following terms to describe these sleep-state specific events throughout the manuscript: Hippocampal sharp-wave ripples (SWRs) in NREM sleep, PFC ripples in NREM sleep, and PFC HFOs in REM sleep.

We refer the Reviewer to our Response to Reviewer 1’s first comment where we provide additional analyses of theta periods outside of HFO times (i.e. baseline REM periods), including Figure S5. We also further address these comments as a response to Reviewer 2’s major comment #1 below.

Furthermore, the evidence for "structured reactivation" is not yet convincing. The temporal alignment of these reactivation events appears inconsistent, with peaks occurring well before the HFO itself, and the analysis does not sufficiently control for pre-existing cellular assembly strengths.

We have now addressed this as a response to Reviewer 2’s major comments #3 and #8 below, including Figure 6.

Additionally, some of the sleep architecture presented appears atypical, such as very short REM bouts and direct NREM-to-REM transitions that bypass standard progression, raising questions about the consistency of the sleep detection across animals.

We have now addressed this as a response to Reviewer 2’s major comment #2 below, including Figure S1 and Figure S3. We expect that addition of these figures will mitigate concerns about our sleep staging procedures and will clarify certain points raised by the Reviewer.

Finally, the study does not account for potential confounds like baseline firing rates when interpreting the behavior of "high-cofiring" neurons, which may simply be the most active cells in the population.

We have now addressed this as a response to Reviewer 2’s major comment #6 below.

Reviewer #2 (Recommendations for the authors):

In this study, the authors detect activity periods during REM sleep that feature high-frequency oscillations in the prefrontal cortex. They term these REM HFOs and report that they occur in "chains" phase-locked to theta oscillations. They contrast these with HFOs that appear in isolation and with ripples observed during NREM sleep, either in the PFC or in the hippocampus. The data presented is very interesting in places. The authors show that these HFOs are observed primarily during "phasic REM" periods that have higher theta power. It appears that overall firing is substantially lower surrounding these events. Intriguingly, it appears that CA1 cells that co-fire with the PFC during HFOs increase their firing rates over the course of sleep, whereas other neurons show a firing decrease. This seems to be the most striking finding of this study.

Major:

(1) The findings are generally intriguing, but the study makes some choices that are hard to understand. They begin comparing HFOs that occur in chains to HFOs that occur in isolation, even though it appears that chained and isolated HFOs likely occur at different times, some during tonic REM, some during phasic REM, and others during NREM. The lack of control for sleep state makes it difficult to determine if the reported differences are intrinsic to the HFO patterns or merely reflections of the underlying global brain state. Overall, I just didn't quite understand the motivation for comparing isolated and chain HFOs, as it seems natural that chains would occur during periods of greater synchrony.

We appreciate the Reviewer for raising these points and agree that the properties of ripples and HFOs cannot be interpreted independently of the underlying brain state. As we mentioned in the initial response, we do expect that the generation of these ripples/HFOs in NREM and REM sleep are inextricably linked to global brain state (ex., cholinergic tone, as shown in the model in Figures 9-10), which results in differing patterns of activity across sleep states. We noted in the response to the public review comment #1 above that as clearly noted in our manuscript title, state-dependence is an integral part of our results, with the primary comparison in the manuscript being between REM cortical HFOs and NREM cortical ripples, and correspondingly, spiking activity patterns observed in cortical-hippocampal circuits during these event types that occur in the two sleep stages.

Sleep state: Our primary goal in comparing isolated and chain HFOs (chain vs. isolated HFOs are only compared in REM periods, not NREM periods) was not to suggest that the differences that we observe are state-independent, but rather to provide evidence that temporal clustering of HFOs underlies distinct PFC dynamics, as well as enhanced CA1 engagement. Rather than attempting to dissociate ripple/HFO occurrence and the differential physiology that underlie NREM and REM sleep states, we view them as complementary—both sleep states are permissive to generation of high-frequency oscillations. Similarly, putative tonic and phasic REM substates (low vs high theta power) are differentially permissive for isolated and chain HFOs (Figure S3C). We add additional detail on tonic vs. phasic REM substages in Supplementary Figure S3, showing that the rate of HFOs and HFO chains is significantly elevated in putative phasic REM. While we would have liked to analyze REM HFOs during tonic and phasic states separately to be able to make more concrete conclusions, the scarcity of phasic REM sleep made it difficult to make accurate comparisons between the two, especially for spiking modulation. We have therefore removed the qualifying term “phasic REM” from the abstract.

Also, we would like to clarify that while we investigated chains of events (ripples) in NREM sleep as a comparison to REM HFOs, we do not refer to them as HFOs in NREM anywhere in the manuscript. In NREM, while there are PFC ripples that are clustered into chains based on our definition (separation of <200 ms), we do not observe a prominent peak in the IEI distribution that would suggest entrainment by other oscillations (e.g. theta or spindles). This analysis was only to show that associated results are specific to REM HFO chains, and not seen during comparable chains of NREM cortical ripple events.

Chain vs isolated HFOs: Regarding the Reviewers comment about why we chose to compare isolated and chain HFOs, the motivation is clearly demonstrated by differences in these events in spectral properties (Figure 3H-I) and spiking modulation (Figure 4F-G). Our initial motivation to investigate these chains of events in REM sleep came from our observation that PFC population activity aligned to REM HFOs was theta-modulated (multipeaked, suggesting multiple high-frequency events over a short duration). This led us to hypothesize that there may be chaining of events in REM sleep, which in line with previous studies demonstrating the clustering of events, such as spindles in NREM sleep (Darevsky, Kim et al. 2024). In that study (Darevsky, Kim et al. 2024), the authors showed that reactivation of motor patterns was more persistent during trains of spindle events as compared to isolated spindles. Furthermore, trains/chains of multiple hippocampal SWRs have been shown to underlie the replay of extended experience (Davidson, Kloosterman et al. 2009). Thus, the separation of high-frequency events into isolated and chained events has precedence and may have functional significance. Furthermore, since we see that isolated and chain events have a bias for occurring during putative bouts of tonic and phasic REM sleep, respectively (Figure S3C), characterization of both event types is an important step for understanding potential differences in interregional interactions during REM sleep. Furthermore, a recent appreciation for the role of sleep stage sub-states (Chang, Tang et al. 2025) further emphasizes the importance of investigating these events separately. We expect future studies to further dissect the roles of tonic and phasic REM states in memory and cognition, and our finding provides an account of the existence of different events for future reference.

HFO chains during periods of greater synchrony: While it may seem natural that chaining would occur during periods of high synchrony (theta synchrony here), we show that our result is HFO-specific, especially for spiking activity modulation (Figures 4F-H and Supplementary Figures S5K-N), which makes it novel and important. Previous studies have focused on theta-gamma cross-frequency phase amplitude coupling, which has been proposed as a mechanism where slower theta oscillations temporally organize faster local population activity, thereby synchronizing neural ensembles within and across brain regions (Belluscio, Mizuseki et al. 2012). Here, we present a comparison of HFOs and gamma events and show that while gamma events can also occur in chains (added to Supplementary Figure S4H), possibly due to increased synchrony as the Reviewer stated above, we do not observe theta-modulated population activity aligned to these events (Supplementary Figure S4J), which is a defining property of HFOs that we propose underlies our results. This indicates that our reported results are unique to periods of synchrony associated with HFOs.

Control analyses for theta periods: Regarding the comment about lack of control for sleep state, we refer the Reviewer to our response to Reviewer 1’s comments. We have performed additional control analyses comparing PFC activity during REM theta periods adjacent to detected HFOs and demonstrate that phasic PFC population activity is largely absent (Figure S5).

We are aware that it is difficult to dissociate the generation of ripples and HFOs from the underlying brain state, since they are so tightly linked. However, we do expect that our clarifying points in addition to the REM theta state controls provide strong evidence that the results that we present are intrinsic to HFOs and not general reflections of activity during baseline theta activity in REM. Here, we further reiterate a few of the main results that demonstrate this:

(1) Phasic spiking modulation of PFC population activity associated with HFOs is not present during baseline theta periods (Supplementary Figure S5K).

(2) Phasic spiking modulation during HFOs is not linked to extracted gamma events (Supplementary Figure S4J).

(3) Phasic spiking modulation, as well as activity suppression, is strongest during chains of HFOs (Figure 4F, Supplementary Figure S4J).

(4) PFC-CA1 theta coherence surrounding HFOs increases relative to baseline (Figure 3E, z-scored relative to baseline coherence).

(5) Assembly peaks are sequentially organized surrounding HFO chains but not during isolated or shuffled (baseline) HFO times (Figure 6C, Supplementary Figure S7E, and Author response image 2).

(6) A higher proportion of CA1-CA1 pairs are high cofiring during HFOs as compared to baseline periods (Figure 7B), indicating specific CA1 engagement during HFOs (in addition to coherence).

Lastly, we show that HFOs detected during periods of active behavior (high theta) on the W-Track are not associated with many of the defining features of HFOs in REM sleep, thus demonstrating the specificity of REM HFOs despite similar background theta activity (Figure S11, in response to Reviewer 3 comment #1).

(2) It is crucial that the study provides REM-specific sleep examples for each of the data sessions, marking tonic and phasic REM and indicating when isolated and chain HFOs are observed. It remains unclear how interspersed these events are. Do some REM episodes just have isolated HFOs and others chains?

We thank the Reviewer for raising this point and apologize for the lack of clarity. For additional transparency, we now provide example sleep state plots for each animal (Supplementary Figure S1H-I).

We also provide hypnograms that show bouts of putative phasic REM on top of REM periods (Supplementary Figure S3). Additionally, as a compact way of demonstrating the validity of our separation of putative tonic and phasic bouts, we provide a plot showing the average velocity and spectrogram surrounding putative phasic REM bouts across all putative phasic REM transitions (Supplementary Figure S3A). Regarding the incidence of HFOs in tonic and phasic REM, we refer the Reviewer to Supplementary Figure S3D, where we show that HFO rate is significantly higher during putative bouts of phasic REM, during which they tend to be organized in chains as compared to putative tonic bouts (Supplementary Figure S3E). In line with this, we additionally report that although both isolated and chain HFOs occur in putative tonic and phasic bouts of REM sleep, the proportion of chain HFOs during phasic REM is significantly higher than that of isolated HFOs (Figure S3), indicating a bias for chains to occur in phasic REM sleep, potentially due to stronger theta input. However, since putative phasic REM accounts for <10% of REM sleep in our dataset, consistent with previous reports using similar methods (Mizuseki, Diba et al. 2011), we were unable to restrict spiking analysis to HFOs in phasic REM. We found that chain HFOs during both putative tonic and phasic REM sleep elicited theta modulated population activity in PFC, thus we pooled HFOs across REM states for analysis.

While a larger proportion of chain events occur in putative bouts of phasic REM sleep as compared to isolated events (Figure S3), chain and isolated events occur in both putative tonic and phasic substates (Proportion of events in putative tonic REM is (1 - proportion in phasic) shown in Figure S3C, right). Thus, the majority of analyses comparing isolated and chain HFOs, especially for spiking data, were pooled across states. Instead of showing example plots for all 22 sleep epochs (22 out of 36 epochs with >5 s of putative phasic REM), we expect that this analysis will be sufficient to illustrate the distributions of isolated and chain HFOs across putative REM sleep substates. We have also removed the qualifying term “phasic REM” from the abstract.

To clarify this, we have added a statement to the new “Limitations” section of the manuscript on Page 16, Lines 10-20:

“Third, we did not record eye movements or ponto-geniculo-occipital (PGO) waves, both of which would have allowed for more accurate segregation of tonic and phasic REM sleep states. (Simor, van der Wijk et al. 2020) Although we observed a bias for isolated and chain HFOs to occur in putative tonic and phasic REM substates, respectively, the scarcity of putative phasic REM bouts made the direct comparison based on substage difficult. Finally, although our model predicts that distinct cell-type activity profiles shape REM sleep HFO dynamics, we did not record a suDicient number of interneurons to test these predictions directly. Future studies using appropriate behavioral tasks, longitudinal sleep recordings, and cell-type specific opto-tagging will be able to resolve these limitations and further clarify the roles of high-frequency oscillations in REM sleep.”

We have now added Supplementary Figure S3.

This is also important because some of the REM sleeps detected and shown in Figure S1H seem unusual. For example, in Animal 1, there are multiple bursts of REM that seem very irregular. In some other sessions, animals occasionally appear to enter REM sleep with very little preceding NREM, which goes against existing literature. It's not clear which ones of these meet the 30 s duration threshold. Are the chain events occurring in these periods?

In reference to the hypnograms shown in Supplementary Figure S1H (Now Supplementary Figure S1I), these were generated by concatenating all 9 sleep epochs regardless of whether they passed the inclusion criterion of > 30 s of total REM sleep. Furthermore, only a subset of the epochs shown were included for analysis based on a secondary, manual inspection that is performed to confirm inclusion. Sleep state plots (e.g. Supplementary Figure S1H) were visually inspected to further confirm the transition into REM sleep, ensuring absence of noisy T/D ratio or spurious detection due to noisy signals – epochs where microarousals or persistent subthreshold fluctuations in animal movement induced noisy TD ratio increases, and thus inaccurate REM designation, were excluded. We thus used a total of 36 sleep sessions from a possible 90 sleep sessions.

We apologize for not specifying what portions of data represented by the hypnograms were included. We have now provided updated hypnograms only illustrating the sleep epochs included for analysis (Figure S1I).

We have now added Supplementary Figure S1.

Regarding the Reviewer’s point “Are the chain events occurring in these periods?”: Yes, all of the chain events (and isolated events) come from these updated epochs that are now shown. No events in the excluded epochs were included, since we wanted to only analyze the data that came from curated REM epochs that we were confident in.

(3) The analysis supporting structured reactivation was not generally convincing. Figure 4E does not provide convincing evidence of this. Indeed, reactivation strength is lowest around the time of the event, and appears highest 0.5s before. The example panel seems rather anecdotal. It's also not clear why REM reactivations should be compared to NREM ones here. I could not follow what was done in Figures 4F-H. Why should the first half and second half of an HFO event be correlated?

We appreciate the Reviewer for raising these concerns. We agree that this section is somewhat dense and at time hard to follow, so we will clarify with further explanations and analyses (see also response to Comment #8 with new reactivation figures).

In Figure 6B (originally Figure 4E), our intention was to show that if you simply align assembly activation to REM HFOs, a relatively flat response is observed when averaged across all assemblies, in stark contrast to assembly reactivation during NREM cortical ripples. This could suggest a couple of things: 1) There is no real assembly activation in response to REM HFOs or 2) Assembly activation is organized differentially (compared to NREM) surrounding HFOs. What we hypothesized, and then quantified based on observations, is that assembly activity is sequentially organized around HFOs. If this were true, it would suggest a consistent temporal relationship between REM HFOs and assemblies (for example, assembly 1 tends to be active 115 ms after the onset of chains, assembly 2 is active 230 ms after, etc.). Of course, the sequential pattern that we show in Figure 6A may arise trivially, especially since these types of sequential visualization plots can simply arise from noise. Thus, a cross-validation method must be utilized to ensure the sequences are indeed reflective of an underlying computation.

In the methods section “Assembly sequence detection surrounding HFOs” we explain the splitripple/HFO procedure that we used to compare assembly sequences across two halves of the data, similar to methods used in hippocampal place cell sequence cross-validation (Plitt and Giocomo 2021, Sosa, Plitt et al. 2025). For every split and assembly alignment, a sequence similar to Figure 6A, right is generated based on the first half of aligned data. Then the second half of aligned data is sorted based on the peak indices of the first half of data and the correlation between the peak reactivation indices across all assemblies for the two datasets is calculated. A high correlation indicates high sequence similarity across the two halves of data (not two halves of an HFO as the Reviewer mentioned), suggesting temporal consistency of assembly reactivation. By utilizing this method, we show that assembly reactivation sequences across randomly chosen halves of data are most similar for chained HFOs (Figure 6C and Supplementary Figures S7C-F). We have now provided an additional control analysis that investigates this sequential assembly activity for time-shifted chain events (Author response image 2). As in Figure 6, assembly activity was aligned to the first event in each time-shifted chain. In addition to the analyses in Supplementary Figure S7, this control further indicates that sequential assembly activity is preferentially restricted to HFO chains.

Author response image 2.

Assembly sequences surrounding time-shifted HFO chains. (A) Distributions of r values calculated from the Pearson correlation between peak reactivation bins across all assemblies for two randomly chosen halves of the shifted HFO-aligned data. There was no difference between r values for time-shifted chains and shuffled data, indicating no structured assembly activity during periods outside of real HFOs chains.

To further quantify this, we calculated two additional metrics: 1) the slope difference between fitted lines for the two halves of data for each split and 2) the absolute peak difference between assemblies in the two halves of data. First, for the slope difference metric, the slope of the best-fit line between assembly ID and peak reactivation index was taken for the two halves of data and compared. A smaller slope difference compared to shuffled data in Figure 6D indicates that assembly reactivation is structured in a more similar manner across the two halves of the real data. Secondly, Figure 6E is a quantification of the peak reactivation displacement between the two halves of data. If there is a high probability of small peak differences, as in the real data, this indicates that the timing of peak reactivation of assemblies relative to HFO chain onset is similar across the two halves of data.

We apologize for the omission of the description of the slope and peak difference metrics that we used in Figures 6D,E. We have added information in the Methods section under “Assembly sequence detection surrounding HFOs” on Page 43, Lines 23-33:

“Furthermore, the slope and peak differences were calculated as additional metrics of sequence and temporal reactivation consistency between the two halves of data, respectively. For the slope difference metric, the slope of the best fit line between assembly ID and peak reactivation index was taken for the two halves of data and compared. A smaller slope difference compared to shuffled data indicates that assembly reactivation is structured in a more similar manner across the two halves of the real data. For peak reactivation difference, the temporal displacement of the peak reactivation index between the two halves of data was calculated and compared to shuffle. A high probability of small peak differences indicates that the timing of peak reactivation of assemblies relative to HFO chain onset is similar across the two halves of data. Shuffling of assembly strength was carried out as above.”

(4) The authors argue that the occurrence of HFOs, rather than theta power, is the reason for lower MUA activity, but the analysis for this (Figure S4I) is quite confusing. The left panel actually seems to indicate that MUA is indeed lower when theta power is high.

We apologize for the confusion regarding this figure and appreciate the Reviewer’s point that periods of high theta power can also appear to be associated with reduced MUA. We agree that the original presentation may not have clearly separated the contributions of theta and HFOs. What we convey with Supplementary Figure S5K (originally Supplementary Figure S4I) and new Supplementary Figures S5L-M is that the observed theta-modulated PFC spiking response (Figure 2A) cannot be solely explained by baseline theta periods (outside of HFOs) in REM sleep. Since theta oscillations are ubiquitous during REM sleep, an important control is to demonstrate that the theta-modulated population activity is not simply a consequence of ongoing theta activity. Thus, we aligned PFC activity to theta oscillations of varied power and show that the fluctuating, theta-modulated population activity is absent, indicating that HFOs associated with the theta oscillation are driving this phasic response.

We are not solely arguing that the presence of HFOs is the driver of decreased PFC multiunit activity. In both the data and model, we show that the magnitude of theta power detected in PFC (possibly input to PFC) is inversely related to multiunit activity (Figure 9E). Our interpretation is not that theta is unrelated to MUA, but rather that HFO occurrence provides additional explanatory power beyond theta alone. Accordingly, we show directly in Supplementary Figures S5L-M, in response to Reviewer 1’s comment #1, that theta periods in phasic REM not associated with HFOs do not elicit the MUA activity suppression similar to HFOs.

The phase-alignment performed is hard to follow and is not being applied to HFO periods. If the study is trying to argue that high-theta periods without HFOs in the same recording sessions show lower MUA, then perhaps some sort of shuffle or jitter would be more suitable. For example, in Figure 1B, it seems there are some high-theta periods that don't have HFOs and appear to have higher MUA.

We expect that the new analyses where we provide additional baseline theta controls for periods adjacent to HFOs in Supplementary Figures S5L-M now clarifies this point. Briefly, alignment to theta phases at different temporal distances from detected HFOs does not exhibit the same fluctuating PFC activity as HFO alignment.

Regarding the phase alignment procedure that we used for the control analysis, since REM sleep is characterized almost entirely by ongoing theta activity, the control condition was not a separate brain state but rather theta periods outside of HFOs. We therefore needed a systematic way to select comparable theta cycles and phase bins in order to make a valid comparison with HFO-aligned PFC population activity. Since we demonstrated that there is significant phase amplitude coupling between theta and HFOs, thus a theta phase preference of HFOs, we used that specific phase bin across multiple theta cycles to align PFC activity. This phase bin selection was performed separately for each epoch to account for inter epoch and animal variability in phase preference. We reasoned that this procedure would allow for a valid comparison as compared to random alignment, since activity was aligned to similar phases in the baseline theta vs HFO conditions.

(5) As far as I could tell, the study does not distinguish between putative excitatory and inhibitory neurons in the PFC, but only in the CA1, even though these play very different roles in the model. What is the rationale for not separating these? How are reactivations to be interpreted among interneurons?

We apologize for the lack of emphasis on this point, which was originally highlighted in Supplementary Figure S2G (now in Supplementary Figure S2F), and for omitting the explanation as to why we did not separately analyze putative excitatory and inhibitory neurons. When we plot the average waveform peak-to-trough and mean firing rates of the PFC neurons, we observe a large cluster with moderate mean firing rates and peak-to-troughs consistent with recording primarily from pyramidal neurons (Supplementary Figure S2F, left). We therefore decided to pool and not separate the populations into putative pyramidal cells and interneurons for the spiking analyses presented. To further validate our decision to pool the cells, we separated the population into putative pyramidal cells and interneurons based on peak-to-trough. Putative interneurons were identified as cells with a peak-to-trough <0.3 ms (we obtained similar results when using a hyperplane to separate units based on both peak-to-trough and firing rate, with a smaller subset identified as putative interneurons). When these putative interneurons were excluded from the HFO-aligned multiunit PFC plot, we observed very similar activity to Figure 2A (Supplementary Figure S2F, right). We thus decided to pool the cells into a single population for the purpose of this manuscript, as we did not have enough interneurons to investigate them separately. We are, however, aware that different cell types may contribute to the phenomenon that we report here and attempt to more thoroughly differentiate the contribution of pyramidal cells and interneurons with our modeling result in Figures 9 and 10.

We have now added the following to the figure legend on Page 51, Lines 21-24:

“REM HFO aligned PFC multiunit response when spikes from putative interneurons are excluded (compare to Figure 2A). Due to this similarity of the phasic PFC response when putative interneurons are omitted, we decided to pool PFC neurons for all further analyses.”

Regarding the interpretation of reactivation in the context of interneurons, we expect reactivation reflects coordinated ensemble activity with excitatory neurons encoding task-relevant information, and inhibitory interneurons shaping timing and neural synchronization. We however did not record enough distinct interneurons to test the predictions of the model, which is now noted in the Limitations on Page 16.

Relatedly, we find that PFC assemblies detected from pooled data have task relevant representations (Figures 5F-G).

(6) Are the high-cofiring CA1 neurons generally higher-firing than the other cells? Could this perhaps explain why they behave differently?

We apologize that this information was not more evident in the manuscript, as it is an important control. In Supplementary Figure S9A, we show that there was no difference in baseline firing rate between low and high cofiring CA1 neurons.

We have now explicitly referenced this figure in the main text on Page 9, Lines 42-45:

“Analysis of low and high cofiring CA1 neurons during REM HFOs showed that high cofiring neurons exhibited elevated activity during chained events as compared to low cofiring neurons (Figure 7D), independent of baseline firing rates (Figure S9A).”

(7) It appears that the decreased firing around HFO's could be a consequence of the stronger firing modulation around these periods, related to time averaging, rather than suppression per se. How does the firing rate compare to other periods with similar modulation that might not have HFOs?

We thank the Reviewer for raising this important point. We expect that the new analyses, where we provide additional baseline non-HFO-associated theta periods, and theta periods adjacent to HFOs at different temporal distance as controls in also Supplementary Figure S5L-N now clarifies this point. These figures show that the decreased firing rate is specific to HFO chains (Supplementary Figure S5N). Indeed, if the suppression that we observe is related to time averaging, or another analytical artifact, our claims of suppression during HFOs would not be valid. We present a number of results and provide further explanations to support the accuracy of our characterization of PFC population suppression.

First, event-aligned multiunit activity was quantified as baseline-normalized population firing relative to detected events. For both NREM and REM, activity was normalized by the mean population firing rate during a baseline period within the same sleep state in which events were detected. Values are therefore expressed as deviations from baseline. This normalization allows comparison of relative changes in firing around events within each state. Importantly, values below baseline reflect reductions relative to the state-matched baseline period.

Second, we show that smoothing activity with a larger gaussian kernel preserves the dip in population activity, consistent with suppression of activity surrounding HFOs (Figure 9C, note that this is a data figure presented in the context of the model). However, as raised by the Reviewer, this normalized measure does not on its own distinguish sustained suppression from transient deviations introduced by event-locked temporal structure in firing.

Third, to address this, we employed an alternative method to demonstrate that HFO chains tend to occur during periods of PFC suppression (Figure 4G). Briefly, we detected events in PFC where activity fell below a threshold and calculated the probability of HFOs surrounding these “suppression” events. We refer the Reviewer to the Methods section under “Detection of population suppression” where we explain this procedure in more detail. We found that chain ripples, during which the strongest suppression is observed (Figure 4F), are associated with decreases in PFC activity (Figure 4G and Supplementary Figure S6).

Fourth, we refer the reviewer to Figure S5N, where we compare the firing rates of PFC neurons during HFO chains and theta periods outside of HFOs during putative phasic REM bouts. The observed reduction in firing during true HFO chains compared to non-HFO periods therefore reflects HFO event-specific activity suppression rather than a common occurrence during baseline REM periods.

Lastly, we performed a control analysis complimentary to Supplementary Figure S5K where we aligned PFC activity to the preferred theta phase of HFOs and investigated how distance from detected HFOs modulates PFC activity (Figure S5). We found that there was no consistent theta-modulated activity aligned to HFO-adjacent theta phases.

Regarding the final comment, if the Reviewer meant “modulation” as in the theta modulation or suppression observed when PFC population activity is aligned to HFOs (Figures 2A and 4F), we are not aware of any other REM periods where this strong theta modulation or suppression of PFC population activity is present. To our knowledge, we are the first to demonstrate such a modulation of PFC population activity in REM sleep. The closest comparison that we can make is PFC activity aligned to gamma events that are coordinated with HFOs (suppression of PFC), but this is explained only with association with HFOs, as shown in Supplementary Figure S4J.

(8) The assembly reactivation measure does not control for pre-existing assemblies. The term "activation strength" would therefore be more appropriate.

We thank the reviewer for this important methodological point. The concern that ICA-based reactivation strength does not, by itself, distinguish behavior-induced reactivation from pre-existing assembly activity/structure is well-taken, and we have implemented several complementary analyses that directly address these concerns.

First, the interleaved structure of our recordings (8 run epochs interleaved with 9 sleep epochs) allows us to investigate the within-session pre/post assembly strength differences (i.e. each W-Track run session has a preceding (pre) and following (post) sleep session). An increase in assembly strength from pre to post is a hallmark of behaviorally relevant assembly reactivation (Kudrimoti, Barnes et al. 1999, Peyrache, Khamassi et al. 2009). For each run epoch, the same run-derived templates were projected onto the preceding and following sleep epochs, and the pre and post strengths were compared. The distribution of post-minus-pre reactivation differences across all epoch pairs is significantly skewed toward positive values (Figure 6F), indicating that templates from the run epochs are more strongly expressed in the post-sleep epochs. This asymmetry cannot be explained by pre-existing assembly structure, which would predict similar assembly strengths.

Second, reactivation strength in post-experience sleep increases across the experiment, with templates from later running epochs producing the strongest reactivation in the following post-sleep (Figure 6G). This increase in reactivation strength over time cannot be explained by preexisting assembly structure, which predicts similar assembly expression strength independent of experience.

Third, the detected assemblies carry behaviorally meaningful structure. Assembly activation maps computed during running exhibit spatially organized "assembly fields" similar to single-cell place fields (Figure 6H), demonstrating that the detected assemblies represent specific spatial locations or task variables rather than behavior-independent states. Pre-existing co-firing structure unrelated to ongoing experience would not be expected to produce spatially tuned, task-locked assembly activation. Furthermore, this spatial tuning of assemblies was verified by comparison with surrogates, where assembly maps were generated using circularly shuffled activation times (1000 shuffles). Assemblies with p < 0.05 (z > 1.65) were considered to have significant spatial structure (Figure 6I).

These results establish that what we measure is the selective re-expression of behaviorally relevant assemblies in subsequent sleep epochs, consistent with the use of "reactivation" in the established literature (Peyrache, Khamassi et al. 2009, Lopes-dos-Santos, Ribeiro et al. 2013). We have therefore retained the term "reactivation strength" and have added text to the manuscript noting these new results that justify the use of “reactivation” strength.

We have now added Figure 6.

We have also added the procedure for the calculation of spatial information to the Methods section under “Spatial information of assembly fields” on Page 44, Lines 8-23.

(9) Can the study rule out that the rank-ordering in Fig 4C is related to firing rates? Higher-firing rates tend to fire earlier, and lower-firing cells later.

We thank the Reviewer for raising this interesting point. Here, we assume that the Reviewer meant the baseline firing rates of the neurons, not the intra-HFO firing rates of the neurons. Indeed, when we look at baseline REM firing rates of these PFC neurons, we do find that neurons with higher firing rates tend to fire earlier than low-firing-rate neurons (Author response image 3). This is also true when PFC rank and firing rate are assessed for isolated REM HFOs and NREM PFC ripples (Author response image 3). Similarly, we also observe this relationship in CA1 during SWRs, during which rank order correlation is typically assessed as a method for replay detection. In line with this, a previous study has shown that CA1 neurons with high excitability at animals’ current location tend to initiate replay events (Karlsson and Frank 2009). Furthermore, high-firing-rate, rigid CA1 neurons are more active during SWRs than low-rate, plastic neurons (Grosmark and Buzsaki 2016), and there are distinct populations of neurons in both hippocampus and PFC that are preferentially active during immobility in sleep epochs (Jarosiewicz, McNaughton et al. 2002, Kay, Sosa et al. 2016, Tang, Shin et al. 2017), potentially biasing replay activity during high-frequency events. Similar dynamics may underlie activity during PFC ripples and HFOs in NREM and REM sleep, respectively. The critical point here is in the leave-one-out cross-validation that we implemented to determine sequence similarity—each left out event’s cell rank was correlated with the averaged rank of the template that was generated from all other events. This analysis provides a basis for our claim that there is preserved sequential PFC activity across HFO chains. We did not observe neuron firing consistency during isolated HFOs or during pseudo-HFO chains (coherently shifted chain HFO times), which indicates that REM HFO chains are unique temporal windows during which PFC activity proceeds in a more structured manner.

Author response image 3.

Firing rate difference of low and high rank neurons (A) Comparison of baseline firing rates of PFC and CA1 neurons split by average rank across all PFC REM HFOs, PFC NREM ripples, or CA1 SWRs. Baseline rates were calculated separately for NREM and REM sleep.

Minor:

(1) It gets confusing that the authors sometimes (but not always) refer to HFOs during NREM as "ripples" but not if they occur during REM. The terminology is inconsistent. When they refer to HFO chains, it seems they now pool between REM and NREM periods, as well as across phasic and tonic REM periods, which is confusing.

We apologize for the confusion regarding the terminology. In the revised manuscript, we now use NREM ripples exclusively for NREM events and REM HFOs exclusively for REM events. We have removed mixed labels such as “ripple/HFO” except where a collective term is explicitly defined. We also clarified that HFO chains refer to REM events only and revised the relevant text/figure legends to avoid any implication that chain analyses pool NREM and REM events.

(2) P7 L8: It might be helpful to emphasize "broader temporal distribution".

We thank the Reviewer for the suggestion. We have updated the text on Page 8, Line 18:

“Since we observed a broader temporal distribution of activity…”

(3) P8 L9: What do they mean by spatial? Do they mean the place-fields of these same neurons during a previous task period?

We apologize for the confusion. The Reviewer is correct. Here, we calculated the spatial rate map correlation between CA1 neurons as a measure of place field similarity during the W-Track session prior to the sleep epoch being assessed.

For clarification, we have added “rate map” to the text on Page 9, Line 33:

“…spatial rate map correlation…”

We have also updated the y-axis label for Figure 7B for clarity.

(4) P8 L27: What do they mean by "coordinated SWRs"? As opposed to what?

Here, we are referring to our previous study where we investigated ripples in NREM sleep and showed that ripples and SWRs in PFC and CA1, respectively could either be independent from or coordinated with events in the other region (Shin and Jadhav 2024). A main result in the study showed that CA1 neurons are strongly suppressed during independent PFC ripples and that there was a relationship between activity suppression and reactivation during coordinated SWRs (CA1 SWR-PFC ripple coordination in NREM). We specifically mentioned “coordinated” since these are SWRs that are also coupled with SOs and spindles as compared to SWRs that are independent from PFC ripples (Shin and Jadhav 2024). Overall, we wanted to frame this result in the context of oscillatory coupling and mechanisms of memory consolidation.

(5) P37 L28 says "we observed a bimodal distribution" but L31 says "unimodal". Which is it?

We apologize for the confusion. We observed a bimodal distribution for CA1-PFC cofiring in REM sleep, but a unimodal distribution in NREM sleep. Because of these two observations, we decided to split the CA1 population into high and low cofiring neurons based on two different thresholds:

(1) Splitting the population by cofiring values greater than (high cofiring) or less than (low cofiring) 0.

(2) Splitting the population by cofiring values greater than (high cofiring) or less than (low cofiring) the mean of the distribution of averaged cofiring values.

Using two separate thresholds to split high and low cofiring CA1 neurons demonstrates the robustness of the firing rate change result in Figures 7F and Supplementary Figures S9B-D.

We added a statement that clarifies that the bimodal distribution was seen in REM sleep only on Page 44, Lines 37-43:

“Furthermore, since we observed a bimodal distribution of CA1-PFC cofiring values in REM sleep, we split the population based on whether the average (across all cell-cell combinations) cofiring value or correlation coefficient of a cell was above or below 0. Also, since the NREM ripple cofiring distribution was unimodal, we additionally split the populations using the mean of the average cofiring or correlation coefficient distributions.”

Reviewer #3 (Public review):

Summary:

Shin et al. examine hippocampal-prefrontal interactions during sleep using simultaneous CA1 and prefrontal cortex recordings in rats performing a spatial memory task. They identify high-frequency oscillation (HFO) events in PFC during REM sleep that occur in theta-modulated chains and are associated with increased CA1-PFC coherence and sequential, sparse reactivation of cortical ensembles. This pattern contrasts with the synchronous reactivation observed during NREM cortical ripples. Together with a simple cholinergic network model, the authors propose that REM HFO chains represent a distinct mechanism for hippocampal-cortical coordination that complements NREM ripple-mediated processing during sleep.

Strengths:

A major strength of the work is the extensive electrophysiological dataset, which includes simultaneous recordings of large neuronal populations in both hippocampus and prefrontal cortex across behaviour and subsequent sleep. The analyses linking high-frequency events to population dynamics, interregional coherence, and ensemble reactivation are technically sophisticated and provide an incredibly detailed description of REM-associated cortical activity patterns. In particular, the demonstration that REM HFOs occur in chains aligned to theta phase and organise sequential activation of cortical assemblies represents a potentially important advance in understanding the neural structure of REM sleep activity. The integration of experimental data with a computational model further provides a useful framework for interpreting the observed differences between REM and NREM network states in terms of neuromodulatory influences.

Weaknesses:

While overall this study provides a highly valuable body of work, there are two primary limitations, which, if overcome, would provide substantially more significance to the overall characterisation of REM HFOs. Specifically:

(1) Distinction from wake HFOs

The results largely support the authors' claim that REM HFO chains represent a distinct pattern of neural coordination compared to NREM cortical ripples. The analyses consistently show differences between REM and NREM events in terms of neuronal modulation, ensemble structure, and interregional coupling. However, similar high-frequency events during wake are not examined. Since REM sleep shares several network features with wakefulness, including strong theta oscillations, evaluating whether comparable PFC HFOs occur during wake would provide clarity on whether these events are specific to REM sleep (and its associated functions) or represent a more general theta-associated phenomenon.

To investigate PFC high-frequency oscillations during running behavior on the W-Track, events were extracted in the same manner as NREM and REM events (Methods). Events during wake were subset by periods where the animals’ velocity was >4 cm/s to provide a comparison of events during periods of high theta. While we were able to detect HFOs during wake that exhibited a similar spectral profile in the high frequency band, we did not observe 1) strong association with gamma or theta oscillations, 2) prominent HFO chaining, 3) HFO aligned theta modulated PFC activity, 4) comparable levels of theta phase amplitude coupling, 5) association with population suppression, or 6) a relationship between peri-event theta power and multiunit activity (Supplementary Figure S11). Many of the defining features of PFC REM HFOs are absent during wake, indicating REM specificity of the results we present.

(2) Link to memory consolidation

The manuscript proposes throughout that REM HFO chains may contribute to memory consolidation by coordinating hippocampal-cortical reactivation, but the evidence for this functional role remains indirect. The authors do highlight this as a limitation of the study - the inability to link their findings to learning - but it is not clear why. Further details of the behaviour results should be included. If no learning occurred across the eight behavioural sessions, this should be reported. If learning did occur, but could not be linked to HFO events, this should also be reported.

To address these concerns, we have now added an explicit “Limitations” section in the main text of the manuscript that includes a statement about learning. We have also added Supplementary Figure S1 in the manuscript, which illustrates the performance of all 10 animals on the W-Track task. Finally, we have also included Figures 6F G in the manuscript, showing that PFC assembly reactivation strength during sleep epochs increases during learning.

Reviewer #3 (Recommendations for the authors):

Most of my specific comments were related to further clarification that will help the reader's understanding.

(1) I'd recommend simplifying terminology. Open to debate, but would it not be simpler and clearer to just say NREM HFO vs REM HFO? Obviously, there is a need to mention how NREM HFOs have previously been referred to as cortical ripples, but I'm not sure it is such a helpful terminology to continue for the field, given, as you state, how different cortical ripples are from hippocampal SWRs. If not, I'd at least provide a clearer explanation early in the manuscript, distinguishing NREM ripples from REM HFOs but collectively still calling them 'cortical events'.

We appreciate the Reviewer’s suggestion regarding terminology and agree that it would be simpler and clearer to use a single term, ripple or HFO, to describe these events. Initially, we had used a unified term (ripples across both states) but ultimately decided to switch to state-specific terminology due to previous comments we received on the manuscript and to emphasize the distinctions between NREM and REM events. Ultimately, we decided on calling them ripples in NREM and HFOs in REM since there is precedence for both terms in each respective sleep state (Khodagholy, Gelinas et al. 2017, Vaz, Inati et al. 2019, Bueno-Junior, Ruckstuhl et al. 2023, Shin and Jadhav 2024), but we do agree that this distinction can be confusing if not clearly stated. Thus, we have added an additional statement in the manuscript on Page 4, Line 44 to Page 5, Lines 1-3 for clarity:

“Similar criteria were used to detect cortical high-frequency events in NREM and REM states; however, to avoid ambiguity and to conform to previous nomenclature, we refer to cortical NREM events as ripples, cortical REM events as HFOs, and hippocampal sharp-wave ripples in NREM as SWRs throughout”

(2) I assume experiments occurred during the light phase, but it would be good if this could be stated explicitly.

We have now added text specifying that these experiments took place in the light phase on Page 34, Lines 9-12 of the Methods section under “Behavior”:

“During the recording day, animals were introduced to the novel W-maze (~80 × 80 cm with ~7 cm wide tracks) for the first time and learned the task rules over eight behavioral sessions during the animals’ light phase between the hours of 9 AM and 6PM.”

(3) Page 2 Line 14: Rephrase to make clearer, e.g. 'that have a shift in...'.

We have rephrased the sentence for clarification on Page 2, Lines 13-15:

“REM HFO chains also preferentially engage CA1 neuronal populations that demonstrate a shift in their preferred theta-phase from behavior to REM sleep.”

(4) Page 4 Line 36 - 'and find coherent shifts in TD', this is self-fulfilling. I would rephrase to something like 'resulting in...'.

We have rephrased the sentence on Page 4, Lines 36-38:

“We separated NREM and REM sleep stages based on theta-to-delta (TD) ratio in CA1, which revealed coherent shifts in TD ratio across CA1 and PFC at the onset and offset of REM sleep…”

(5) Figure 1H left - clarify how many animals or multiunits this is based on.

We have now updated Figure 1 legend to specify the number of animals and epochs included on Page 19, Line 4:

“REM HFO aligned multiunit activity (MUA) in PFC (n = 10 animals, 36 epochs)…”

(6) Figure 1I (right), it would be useful to see the x-axis frequency start from 0, since you are cutting the peak in power.

We thank the Reviewer for this suggestion. We had initially set the frequency limits to 4 and 12 to specifically illustrate the absence of theta-modulated activity during NREM ripples. However, as suggested by the Reviewer, it is informative to expand the frequency range to ascertain the location of the peak frequency for NREM. Indeed, the peak frequency of NREM ripple-aligned PFC activity tends to be lower than 4 Hz, which is consistent with a single peak of activity that lasts <1 s.

We have now updated Figure 2C with these new panels.

(7) Figure 5 E/I - use of ** is confusing, it looks like a significance comparing e.g. quartile 2 to 1, but I think this is the correlation significance. I'd move ** to the top right corner and ideally include rho values.

We thank the Reviewer for this suggestion. We have now added the r values for the correlation to Figures 7E and 8B to resolve any ambiguity. In addition, we updated Figure 7F, right and Figure 5B to maintain consistency across main figures.

(8) Figure 7D - Why are stimulated and non-stimulated cells so different at baseline? This is not the case for the NREM results.

The y-axes in Figures 10C,D (Formerly Figure 7) show the fraction of cells with at least one spike per 10ms bin, either for all pyramidal cells or all interneurons. We report in the figure legend that the stimulated cells represent only 30% of the network for any given stimulus (Page 32, Line 18), so at baseline in both the NREM and REM simulations, there are roughly 3x as many non-stimulated cells with a spike per 10ms bin compared to stimulated cells, as these populations are active at roughly equal firing rates per neuron outside of stimulation periods.

(9) Methods - there is limited info on spike sorting procedure - can you provide a reference with further details (I couldn't find)? Is this method equally valid for identifying PFC units?

Matclust is a MATLAB-based spike sorting graphical user interface that allows for manual curation of neuron clusters through the visualization of spike waveform amplitude, peak-to-trough, and principal components. Polygons or boxes are drawn around spike data points, and single unit clusters are resolved through refinement in multiple dimensions. It was developed by Mattias Karlsson and was first used in a publication reporting replay of remote experiences in the hippocampus (Karlsson and Frank 2009). Although there is no formal reference, it can be found at https://bitbucket.org/mkarlsso/matclust/src/master/. Other labs have used the software for clustering neurons from cortical areas (Yu, Liu et al. 2018, Proskurin, Manakov et al. 2023), which demonstrates its robustness across multiple brain areas.

Additionally, examples of clustered neurons in PFC over the course of the experimental paradigm used here can be found in our previous publication (Shin, Tang et al. 2019). In addition to the aforementioned references, we show that PFC neurons can be accurately clustered and that neurons are stable over time, according to a number of cluster metrics.

(10) Why were there no further analyses of pyramidal cells and interneurons beyond Figure S2?

We thank the Reviewer for bringing up this important point, which is similar to Reviewer 2, comment #5 above. We repeat our response here. When we plot the average waveform peak-to-trough and mean firing rates of the PFC neurons, we observe a large cluster with moderate mean firing rates and peak-to-troughs consistent with primarily recording from pyramidal neurons (Supplementary Figure S2F, left). All results are similar if we exclude putative interneurons. To validate our decision to pool the cells, we separated the population into putative pyramidal cells and interneurons based on peak-to-trough. Putative interneurons were identified as cells with a peak-to-trough <0.3 ms (we obtained similar results when using a hyperplane to separate units based on both peak-to-trough and firing rate, with a smaller subset identified as putative interneurons). When these putative interneurons were excluded from the HFO aligned multiunit PFC plot, we observed very similar activity to Figure 2A (Supplementary Figure S2F, right). We thus decided to pool the cells into a single population for the purpose of this manuscript. We are, however, aware that different cell types may contribute to the phenomenon that we report here and attempt to more thoroughly differentiate the contribution of pyramidal cells and interneurons with our modeling result in Figures 9 and 10.

We have now added the following to the figure legend on Page 51, Lines 21-24:

“REM HFO aligned PFC multiunit response when spikes from putative interneurons are excluded (compare to Figure 2A). Due to this similarity of the phasic PFC response when putative interneurons are omitted, we decided to pool PFC neurons for all further analyses.”

(11) Looking at Figure S1B, the second to last main block of NREM sleep shown has a clear peak passing TD threshold, but oddly not classed as REM - I can only assume this is due to the duration limits on your classification?

Yes, this is due to the REM duration threshold that we implement in our sleep scoring algorithm. We used a minimum REM bout threshold criterion of 10 s for inclusion, as in previous reports (Rothschild, Eban et al. 2017, Zhang, Zhang et al. 2020). Additionally, we have included example sleep plots for all 10 animals in Supplementary Figure S1.

(12) Include details of how head speed was calculated - just based on the 30fps video?

Yes, the head speed of the animal was determined by tracking the animals’ position and calculating the speed based on cm/pixel values. We have now added more detail on this in the Methods section under “Surgical implant and electrophysiology” on Page 33, Line 44 to Page 34, Lines 1-2:

“Additionally, the animals’ speed was calculated based on predetermined cm/pixel values and the position displacement between frames captured at 30 fps.”

(13) Page 31 line 7 - With the reference you cite, they didn't really show tonic and phasic REM can be segregated based on theta frequency - they just defined it as such. You've done it for some, but I'd ensure all references to phasic REM are defined as putative - mostly missed within the discussion - I'd also add this as a brief limitation (without recording of eye movements or PGO waves).

We thank the Reviewer for these suggestions. We have now ensured that all mentions of “phasic REM” are qualified with “putative” and have added the requested limitation in the Limitations section on Page 16, Lines 10-15:

“Third, we did not record eye movements or ponto-geniculo-occipital (PGO) waves, both of which would have allowed for more accurate segregation of tonic and phasic REM sleep states.(Simor, van der Wijk et al. 2020) Although we observed a bias for isolated and chain HFOs to occur in putative tonic and phasic REM substates, respectively, the scarcity of putative phasic REM bouts made the direct comparison based on substage difficult.”

We have also modified the wording in the Methods section under “Theta inter-peak intervals during bouts of high and low theta power” on Page 37, Lines 14-15 to indicate that the referenced article simply used the theta frequency-based method to define tonic and phasic REM – not to explicitly separate the two states:

“Since previous studies have segregated putative tonic and phasic substages of REM sleep based on CA1 theta frequency…”

References:

Abdou, K., M. Nomoto, M. H. Aly, A. Z. Ibrahim, K. Choko, R. Okubo-Suzuki, S. I. Muramatsu and K. Inokuchi (2024). "Prefrontal coding of learned and inferred knowledge during REM and NREM sleep." Nat Commun 15(1): 4566.

Aleman-Zapata, A., R. G. M. Morris and L. Genzel (2022). "Sleep deprivation and hippocampal ripple disruption after one-session learning eliminate memory expression the next day." Proc Natl Acad Sci U S A 119(44): e2123424119.

Belluscio, M. A., K. Mizuseki, R. Schmidt, R. Kempter and G. Buzsaki (2012). "Cross-frequency phase coupling between theta and gamma oscillations in the hippocampus." J Neurosci 32(2): 423–435.

Bueno-Junior, L. S., M. S. Ruckstuhl, M. M. Lim and B. O. Watson (2023). "The temporal structure of REM sleep shows minute-scale fluctuations across brain and body in mice and humans." Proc Natl Acad Sci U S A 120(18): e2213438120.

Cairney, S. A., S. J. Durrant, R. Power and P. A. Lewis (2015). "Complementary roles of slow-wave sleep and rapid eye movement sleep in emotional memory consolidation." Cereb Cortex 25(6): 1565–1575. Chang, H., W. Tang, A. M. Wulf, T. Nyasulu, M. E. Wolf, A. Fernandez-Ruiz and A. Oliva (2025). "Sleep microstructure organizes memory replay." Nature 637(8048): 1161–1169.

Cheng, S. and L. M. Frank (2008). "New experiences enhance coordinated neural activity in the hippocampus." Neuron 57(2): 303–313.

Darevsky, D., J. Kim and K. Ganguly (2024). "Coupling of Slow Oscillations in the Prefrontal and Motor Cortex Predicts Onset of Spindle Trains and Persistent Memory Reactivations." J Neurosci 44(43). Davidson, T. J., F. Kloosterman and M. A. Wilson (2009). "Hippocampal replay of extended experience." Neuron 63(4): 497–507.

Ellenbogen, J. M., P. T. Hu, J. D. Payne, D. Titone and M. P. Walker (2007). "Human relational memory requires time and sleep." Proc Natl Acad Sci U S A 104(18): 7723–7728.

Foster, D. J. and M. A. Wilson (2006). "Reverse replay of behavioural sequences in hippocampal place cells during the awake state." Nature 440(7084): 680–683.

Ghosh, M., F. C. Yang, S. P. Rice, V. Hetrick, A. L. Gonzalez, D. Siu, E. K. W. Brennan, T. T. John, A. M. Ahrens and O. J. Ahmed (2022). "Running speed and REM sleep control two distinct modes of rapid interhemispheric communication." Cell Rep 40(1): 111028.

Grosmark, A. D. and G. Buzsaki (2016). "Diversity in neural firing dynamics supports both rigid and learned hippocampal sequences." Science 351(6280): 1440–1443.

Helfrich, R. F., J. D. Lendner, B. A. Mander, H. Guillen, M. PaD, L. Mnatsakanyan, S. Vadera, M. P. Walker, J. J. Lin and R. T. Knight (2019). "Bidirectional prefrontal-hippocampal dynamics organize information transfer during sleep in humans." Nat Commun 10(1): 3572.

Jarosiewicz, B., B. L. McNaughton and W. E. Skaggs (2002). "Hippocampal population activity during the small-amplitude irregular activity state in the rat." J Neurosci 22(4): 1373–1384.

Ji, D. and M. A. Wilson (2007). "Coordinated memory replay in the visual cortex and hippocampus during sleep." Nat Neurosci 10(1): 100–107.

Karlsson, M. P. and L. M. Frank (2009). "Awake replay of remote experiences in the hippocampus." Nat Neurosci 12(7): 913–918.

Kay, K., M. Sosa, J. E. Chung, M. P. Karlsson, M. C. Larkin and L. M. Frank (2016). "A hippocampal network for spatial coding during immobility and sleep." Nature 531(7593): 185–190.

Khodagholy, D., J. N. Gelinas and G. Buzsaki (2017). "Learning-enhanced coupling between ripple oscillations in association cortices and hippocampus." Science 358(6361): 369–372.

Kudrimoti, H. S., C. A. Barnes and B. L. McNaughton (1999). "Reactivation of hippocampal cell assemblies: effects of behavioral state, experience, and EEG dynamics." J Neurosci 19(10): 4090–4101. Lee, A. K. and M. A. Wilson (2002). "Memory of sequential experience in the hippocampus during slow wave sleep." Neuron 36(6): 1183–1194.

Leemburg, S., V. V. Vyazovskiy, U. Olcese, C. L. Bassetti, G. Tononi and C. Cirelli (2010). "Sleep homeostasis in the rat is preserved during chronic sleep restriction." Proc Natl Acad Sci U S A 107(36): 15939–15944.

Lopes-dos-Santos, V., S. Ribeiro and A. B. Tort (2013). "Detecting cell assemblies in large neuronal populations." J Neurosci Methods 220(2): 149–166.

Mizuseki, K., K. Diba, E. Pastalkova and G. Buzsaki (2011). "Hippocampal CA1 pyramidal cells form functionally distinct sublayers." Nat Neurosci 14(9): 1174–1181.

Nitsche, M. A., M. Jakoubkova, N. Thirugnanasambandam, L. Schmalfuss, S. Hullemann, K. Sonka, W. Paulus, C. Trenkwalder and S. Happe (2010). "Contribution of the premotor cortex to consolidation of motor sequence learning in humans during sleep." J Neurophysiol 104(5): 2603–2614.

Peyrache, A., M. Khamassi, K. Benchenane, S. I. Wiener and F. P. Battaglia (2009). "Replay of rule-learning related neural patterns in the prefrontal cortex during sleep." Nat Neurosci 12(7): 919–926.

Plitt, M. H. and L. M. Giocomo (2021). "Experience-dependent contextual codes in the hippocampus." Nat Neurosci 24(5): 705–714.

Proskurin, M., M. Manakov and A. Karpova (2023). "ACC neural ensemble dynamics are structured by strategy prevalence." Elife 12.

Rothschild, G., E. Eban and L. M. Frank (2017). "A cortical-hippocampal-cortical loop of information processing during memory consolidation." Nat Neurosci 20(2): 251–259.

Shin, J. D. and S. P. Jadhav (2024). "Prefrontal cortical ripples mediate top-down suppression of hippocampal reactivation during sleep memory consolidation." Curr Biol 34(13): 2801–2811 e2809.

Shin, J. D., W. Tang and S. P. Jadhav (2019). "Dynamics of Awake Hippocampal-Prefrontal Replay for Spatial Learning and Memory-Guided Decision Making." Neuron 104(6): 1110–1125 e1117.

Siapas, A. G. and M. A. Wilson (1998). "Coordinated interactions between hippocampal ripples and cortical spindles during slow-wave sleep." Neuron 21(5): 1123–1128.

Simor, P., G. van der Wijk, L. Nobili and P. Peigneux (2020). "The microstructure of REM sleep: Why phasic and tonic?" Sleep Med Rev 52: 101305.

Singer, A. C. and L. M. Frank (2009). "Rewarded outcomes enhance reactivation of experience in the hippocampus." Neuron 64(6): 910–921.

Sosa, M., H. R. Joo and L. M. Frank (2020). "Dorsal and Ventral Hippocampal Sharp-Wave Ripples Activate Distinct Nucleus Accumbens Networks." Neuron 105(4): 725–741 e728.

Sosa, M., M. H. Plitt and L. M. Giocomo (2025). "A flexible hippocampal population code for experience relative to reward." Nat Neurosci 28(7): 1497–1509.

Stark, E., L. Roux, R. Eichler and G. Buzsaki (2015). "Local generation of multineuronal spike sequences in the hippocampal CA1 region." Proc Natl Acad Sci U S A 112(33): 10521–10526.

Tang, W., J. D. Shin, L. M. Frank and S. P. Jadhav (2017). "Hippocampal-Prefrontal Reactivation during Learning Is Stronger in Awake Compared with Sleep States." J Neurosci 37(49): 11789–11805.

Tort, A. B., R. Scheffer-Teixeira, B. C. Souza, A. Draguhn and J. Brankack (2013). "Theta-associated high-frequency oscillations (110-160Hz) in the hippocampus and neocortex." Prog Neurobiol 100: 1–14.

Valero, M., T. J. Viney, R. Machold, S. Mederos, I. Zutshi, B. Schuman, Y. Senzai, B. Rudy and G. Buzsaki (2021). "Sleep down state-active ID2/Nkx2.1 interneurons in the neocortex." Nat Neurosci 24(3): 401–411.

van de Ven, G. M., S. Trouche, C. G. McNamara, K. Allen and D. Dupret (2016). "Hippocampal Offline Reactivation Consolidates Recently Formed Cell Assembly Patterns during Sharp Wave-Ripples." Neuron 92(5): 968–974.

van der Helm, E. and M. P. Walker (2011). "Sleep and Emotional Memory Processing." Sleep Med Clin 6(1): 31–43.

Vaz, A. P., S. K. Inati, N. Brunel and K. A. Zaghloul (2019). "Coupled ripple oscillations between the medial temporal lobe and neocortex retrieve human memory." Science 363(6430): 975–978.

Wilson, M. A. and B. L. McNaughton (1994). "Reactivation of hippocampal ensemble memories during sleep." Science 265(5172): 676–679.

Yang, S. R., H. Sun, Z. L. Huang, M. H. Yao and W. M. Qu (2012). "Repeated sleep restriction in adolescent rats altered sleep patterns and impaired spatial learning/memory ability." Sleep 35(6): 849–859.

Yu, J. Y., D. F. Liu, A. Loback, I. Grossrubatscher and L. M. Frank (2018). "Specific hippocampal representations are linked to generalized cortical representations in memory." Nat Commun 9(1): 2209.

Zhang, L. B., J. Zhang, M. J. Sun, H. Chen, J. Yan, F. L. Luo, Z. X. Yao, Y. M. Wu and B. Hu (2020). "Neuronal Activity in the Cerebellum During the Sleep-Wakefulness Transition in Mice." Neurosci Bull 36(8): 919– 931.

Reviewer #1 (Public review):

We appreciate the authors have provided answers to many of the points we raised, and the changes made to their manuscript, which we think strengthen the overall evidence presented. However, we find that some important controls are still missing across experiments.

Major comments:

(1) Shortcomings in Immunofluorescence experiments:

a. Antibody cross-reactivity was only tested against CK1ɛ, but should also be tested against CK1α, which is abundant in U2OS cells, and is also known to be involved in cell-cycle regulation.

b. Fig. 1: Statistical analyses are missing from the analysis.

c. Fig. 2: No colocalisation analysis shown for figure 2, only some arrowheads pointing to puncta. Appropriate colocalisation statistics are important since for practical reasons, only a few representative images can be shown on the figure.

d. Fig. 6: Even if the figure is illustrative, it is important to show centrosome staining to visualise CK1ẟ's recruitment to the centrosome in G2/prophase, especially since this information is used to propose the model in figure 7.

e. For all figures: Please mention the number of independent biological replicates in the figure legends (1, 2, 6). For figure 1, if there are 3 independent biological replicates, the quantification should take all of them into account (as opposed to the data points corresponding to 10 cells), and statistics must be done appropriately, taking those independent replicates into account. Same for the colocalisation analysis in figure 2 once you include it.

(2) Shortcomings in biochemistry experiments:

On CalA control, this is not a matter of confirming that CalA treatment works in principle, but rather to confirm that CalA treatment worked in this specific replicate. Aliquots may lose potency (e.g. with freeze-thaw cycles / exposure to light), hence checking for enrichment of phospho-proteins is essential to confirm the treatment was successful in this particular instance. In the worst-case scenario, the company may have sent the wrong compound altogether! A positive and a negative control is the basis for every experiment to make meaningful interpretation. On a separate note, many experiments have control and siRNA or compound treatments on two different gels - this should be rectified as they are meaningless if different exposures have been selected for different immunoblots.

(4) As the authors mention, the kinase is not fully inactive when tail phosphorylated. Recent research has also suggested that tail-phosphorylated CK1ẟ may show increased catalytic activity for a few select, specific substrates, in the co-occurrence of pT220 (Cullati et al., 2022; Cullati et al., 2024). It is thus tricky to directly infer that phosphorylated CK1ẟ is inhibited, when no positive control for CK1ẟ inhibition was shown in the evidence presented. It would be necessary to either nuance your claim or include a positive control for CK1ẟ inhibition. Please revise statements in the manuscript accordingly.

(5) It would be important to include statistical analyses for the immunofluorescence data in Fig. 1 and 2.

(9) The authors mentioned "In the eLife study, we show that inhibition of kinase activity by PF670462 stabilizes CK1δ and that the overexpressed kinase-dead mutant CK1δ-K38R is stable." Unfortunately, the data from biochemical analyses presented in the eLife publication is uninterpretable due to a lack of loading controls.

(10) While the data presented in Penas et al. strongly suggests a link between CK1ẟ stabilisation and the APC/C-Cdh1 complex, it is the only study to have shown it. Given that (1) science relies on data reproducibility and (2) your proposed model relies heavily on the relationship between CK1ẟ stabilisation and the APC/CCdh1 complex, it would be appropriate to include the investigations mentioned in our original comment.

Author response:

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

eLife Assessment

This important study identifies a non-canonical essential role for acyl carrier protein in maintaining apicoplast metabolism and blood-stage survival in Plasmodium falciparum. The main conclusions are largely supported by strong genetic and biochemical evidence, although some claims regarding the dispensability of fatty acid synthesis pathways remain incomplete. The work provides novel mechanistic insight into ACP-mediated stabilization of pyruvate kinase II and will be of broad interest to the malaria and apicoplast biology communities.

We note that the major and most important conclusion of our manuscript is that apicoplast ACP has an essential stabilizing interaction with pyruvate kinase II that is required for organelle function and biogenesis. This conclusion is entirely independent of our growth experiments with ∆ACP and ∆FabD parasites in low-lipid conditions, which in principle could be removed from the manuscript without weakening the major conclusions. Nonetheless, we feel that these findings in low-lipid conditions have merit, especially since they contrast with a prior study in the literature regarding P. falciparum growth in low-lipid conditions. We hope that these contrasting results and the questions they raise will stimulate future studies to fully test and understand FASII function under different conditions, including low-lipid conditions.

We kindly ask that the editorial assessment be revised to focus on the major conclusions. Alternatively, we would respectfully suggest revising the second sentence to something akin to “The main conclusions are largely supported by strong genetic and biochemical evidence, while function of fatty acid synthesis pathways in low-lipid conditions will require future studies to fully resolve.”

Public Reviews:

Reviewer #1 (Public review):

This study provides evidence that the apicoplast-locaized isoform of acyl-carrier protein (ACP) has acquired important non-enzymatic functions in the malaria parasite. Previous studies have shown that the apicoplast-located FASII-dependent pathway of fatty acid synthesis is not essential in Plasmodium blood stages. In contrast, genome-wide knockout studies suggested that ACP, a key protein in this pathway, is essential in these stages, indicating that it may have additional non-canonical functions. In this study, the authors confirm that ACP is essential in Pf blood stages (using both apicoplast IPP rescue and conditional knockdown); show that this essential function requires modification with 4-phosphopantetheine and use proximity biotinylation and complementary immunoprecipitation pull-down approaches to provide compelling evidence that ACP binds to and stabilizes the apicoplast-located isoform of pyruvate kinase II. Notably, these interactions appear to differ from those associated with the binding of mitochondrial isoforms of ACP to proteins involved in Fe-S biosynthesis. Loss of ACP was shown to lead to a decrease in PKII levels and apicoplast DNA/RNA synthesis, consistent with loss of NTP synthesis in this organelle. The data are clear and very well described, and the findings represent a significant advance in our understanding of metabolic regulatory mechanisms in apicomplexan apicoplast studies.

Strengths:

The study uses a variety of complementary genetic approaches to demonstrate the essentiality of ACP and the enzyme involved in its activation with 4-PP in Pf blood stages, demonstrating that the ascribed non-enzymatic function is mediated by holo-ACP. Similarly, a number of complementary biochemical approaches, including proximity biotinylation, immunoprecipitation, and co-expression of PfACP and PK-II in a heterologous bacterial expression system, are used to confirm the physiological significance of the PfACP and PK-II interaction. The study also reports additional findings, such as the independence of P. faciparum blood stages on exogenous (media) fatty acids, indicating that intracellular stages can salvage all of their requirements from the red blood cell.

Weaknesses:

Overall, this is a very strong study. While questions remain around the function of other apicoplast ACP-interacting proteins detected in this study, I don't have any suggestions for significant improvements.

We thank the reviewer for these positive comments.

Reviewer #2 (Public review):

This study focuses on revealing the essential divergent function of the Acyl Carrier protein (ACP) in the deadliest human malaria parasite, Plasmodium falciparum. More precisely, using inducible KO, cellular and biochemical approaches, the authors determined that instead of a canonical role for ACP allowing the de novo synthesis of fatty acids in the apicoplast (essential relict plastid) of the parasite, the enzyme couples with pyruvate kinase II to generate nucleoside triphosphate to maintain parasite survival during blood stages. The study is novel, well-designed, providing interesting new data on Plasmodium and apicomplexa biology. The results convincingly support the major claim of the study. However, it is currently incomplete to support some claims on the essentiality of some apicoplast pathways.

In this study, Geher et al. focused on deciphering the role of the Acyl Carrier Protein (ACP) present in the relict non-photosynthetic plastid, i.e. the apicoplast of the most lethal human malaria parasite, Plasmodium falciparum. More particularly, they determined an essential function of ACP independent of its usual/typical function as the central protein for the normal function of the apicoplast Type II fatty acid synthesis (FASII) pathway. Rather, the protein seems to associate with the apicoplast Pyruvate Kinase II, together generating an essential nucleoside triphosphate (NTPs) source to fuel the apicoplast and parasite survival instead.

By generating a TetR-DOZY-based inducible KD line for ACP, they confirmed that the protein is indeed essential to maintain apicoplast integrity and parasite survival during asexual blood stages, as previously predicted and experimentally shown. They showed that ACP requires a biochemical modification, typically activating the protein for its function in the FASII pathway, i.e. binding of the 4-PP group by holoACP synthase. Then, they showed that the other enzymes of the FASII pathway are likely dispensable during the blood stage, as they were able to generate a KO line of the first enzyme of the pathway, FabD (which was predicted to be essential in P. falciparum). Based on a cell culture approach in a controlled culture medium, they further claimed that, unlike current evidence-based hypotheses, the FASII pathway (and thus a potentially FASII-linked ACP) has no role/activity during blood stages. Using a proximity biotinylation approach, they determined that ACP associates with the apicoplast pyruvate Kinase II (PKII), previously shown to generate NTPs in the apicoplast for energy and DNA/RNA maintenance (Xia et al. 2019), and not to fuel the FASII pathway as its main function in blood stages. Finally, they showed that the disruption of ACP induces the reduction of the presence/content in PKII in the parasite, as well as the drastic reduction of the apicoplast DNA and RNA content. Together, they concluded that the main function of ACP is indeed the NTP formation via its association with PKII, rather than its canonical role for the generation of fatty acids in the apicoplast.

To clarify, we conclude that the essential function of ACP in blood-stage P. falciparum parasites includes a critical stabilizing interaction with pyruvate kinase II. Apicoplast ACP presumably still plays a central biochemical role in FASII pathway function, but that role in FASII is dispensable for blood-stage parasites.

This study is novel and focuses on a topic of particular interest in malaria biology, but also for most of the apicomplexa-related diseases, and beyond for plastid bearing orgnaisms and this unusual role for ACP. The study is well thought out with proper biochemical approaches that convincingly point to this association of ACP with PKII for NTP synthesis as a major function during P. falciparum blood stages. However, there are currently some important experimental issues/flaws, missing experiments that induced wrong interpretations and thus do not support some important claims of the study, notably for the role of FASII and the interaction between ACP and PKII.

We note that the major and most important conclusion of our manuscript is that apicoplast ACP has an essential stabilizing interaction with pyruvate kinase II that is required for organelle function and biogenesis. This conclusion is entirely independent of our growth experiments with ∆ACP and ∆FabD parasites in low-lipid conditions, which in principle could be removed from the manuscript without weakening the major conclusions. Nonetheless, we feel that these findings in low-lipid conditions have merit, especially since they contrast with a prior study in the literature regarding P. falciparum growth in low-lipid conditions. We hope that these contrasting results and the questions they raise will stimulate future studies to fully test and understand FASII function under different conditions, including low-lipid conditions.

We elaborate on these points and address the reviewer’s critiques below.

Therefore, at this point, the study is only partial and would require major additions and/or important text edits/revisions before being considered for acceptance.

We note that the manuscript has already been accepted for publication in accordance with the current eLife publishing model.

Major points:

From the graph of P. falciparum growth, we can see that in the lipid-rich condition, where both FabH KO and ACP KO can survive, the addition of mevalonate was essential for the growth of ACP KO. Along with the other evidence (PKII association, DNA levels...), we therefore agree that PfACP is involved in the mevalonate pathway.

To clarify, our model is that ACP supports IPP synthesis by the apicoplast nonmevalonate/MEP pathway indirectly by stabilizing and thus supporting function by pyruvate kinase II that supplies the pyruvate and NTPs required for IPP synthesis by the MEP pathway.

The authors claim that the FASII pathway is inactive/not essential in the P. falciparum blood stage. However, the authors have not shown any evidence on whether ACP is or not involved in the FASII pathway during the asexual blood stage.

To clarify, there is overwhelming data in the prior published literature that we cite (including refs. 13, 14, and 32) to establish that FASII is dispensable for blood-stage Plasmodium growth in vivo in rodent parasites and in vitro culture in human parasites. Prior studies also strongly support a role for apicoplast ACP as the central scaffold for FASII-mediated acyl chain synthesis. However, our and prior studies support the conclusion that essential ACP function in blood-stage parasites is independent of its role in FASII.

As currently designed, the experiments presented cannot conclude on that point for several reasons. Indeed, it was previously shown that (i) the expression of the protein from the FASII pathway are all present in blood stages and are significantly upregulated in patients that are under under "nutrient starvation" (Daily et al. Nature 2007), (ii) that, growing parasites under similar low lipid conditions in vitro induces an activation/upregulation of FASII, which can be measured by stable isotope precursor labelling and lipidomics (Botté et al. 2013).

We are aware of these prior studies and cite and discuss the Botté et al. 2013 reference in our manuscript, which provided isotope-labeling evidence to support FASII activity in low-lipid growth conditions for P. falciparum. We note that neither study addresses whether FASII activity is required for growth in low-lipid conditions.

(iii) that growing the PfFabI KO line under deprived lipid conditions leads to parasite death (Amiar et al. 2020), indicating that the FASII pathway can become critical, if not essential, depending on the host nutritionnal content together correlating patients' data and metabolic adaptation for the same reasons in the related parastie Toxoplasma gondii (Amiar et al. 2020, Krishnan et al. 2020, Liang et al. 2020, Primo et al. 2021, Charital et al. 2024, Dass et al. 2024, Bitew et al. 2025).

All of the studies cited by the reviewer focus primarily or exclusively on Toxoplasma gondii parasites. We agree with the reviewer that these and other studies provide strong evidence that FASII activity contributes to growth of T. gondii parasites, including roles for apicoplast ACP that appear to differ from what we have unveiled for P. falciparum malaria parasites. We acknowledge and discuss these differences from T. gondii in the final section of the Discussion section and think that exploring these differences will be a fascinating area for future study.

The Amiar et al. 2020 paper cited by the reviewer is the only study we are aware of that has directly tested the ability of a ∆FASII parasite (in this case, ∆FabI) to grow in low-lipid conditions. We acknowledge that they observed little to no growth of ∆FabI parasites in these conditions. Our growth assays with ∆ACP and ∆FabD parasites indicated a different outcome in which both WT and ∆FASII parasites grew similarly in low-lipid conditions. Our results thus contrast with the prior study. As noted below, the minimal lipid growth conditions explicitly reported in the methods section of the Amiar et al. paper are identical to those used in our study: fatty acid-free BSA, 30 µM palmitic acid, and 45 µM oleic acid (all sourced from Sigma) with daily media changes. Thus, the basis for these differences is unclear and additional follow-up work will be needed to explore and resolve these differences.

We have revised the final paragraph of the second results section of our manuscript to incorporate this perspective:

“These results contrast with the prior study [49] of ∆FabI parasites and the proposed model that blood-stage P. falciparum requires FASII activity for growth in low-lipid conditions and suggest that parasites can rely on scavenging host-derived fatty acids over a wide range of lipid conditions. Future studies involving tandem growth and isotope-labeling experiments of WT and ∆FASII parasites will be required to fully test and understand FASII function and the dependence of P. falciparum growth on this pathway in low-lipid conditions.”

Here, the authors are expecting to show that FabH (and thus the FASII pathway) is not essential in an experiment that is not designed to be in low lipid conditions but rather in lipid rich conditions: Such high lipid conditions of culture in this study is granted by daily feedings with high fatty acid supplement (30-90 uM palmitic acid and 30-60 uM oleic acid). These fatty acid concentrations were used previously by Mitamura et al. (2005) and Miichi et al.(2007) to replace non-determined supplements such as Serum or Albumax supplement to grant similar growth by a completely controlled culture medium.

This means the concentrations above do not represent limited fatty acid concentrations, especially not with daily feeding (representing an excess supplied amount of lipids, unlike regular 48h feedings) that allowed the authors to easily reach very high non-physiological parasitaemia of more than 20%!! Amiar et al. previously showed essentiality of FabI in P. falciparum in the limited fatty acid culture at a lower concentration (<30uM 16:0, <45um 18:1), than the Mi-Ichi et al. controlled medium with regular 48 h culture feeding. Therefore, with the current experimental settings, the FAH KO is placed in high lipid conditions, thus preventing any conclusion on its essentiality under low lipid conditions.

The basis for the reviewer’s statements here is unclear, as this critique and the conditions it describes do not conform to the published conditions reported in the Amiar et al. 2020 paper. The methods section of that study for “Plasmodium falciparum growth assays” explicitly states (page e7):

“Media was replaced daily, sub-culturing were performed every 48 h when required, and parasitemia monitored by Giemsa-stained blood smears. Growth assays in lipid-depleted media were performed by synchronizing parasites before transferring trophozoites to lipid-depleted media as previously reported (Botte ´ et al., 2013; Shears et al., 2017). Briefly, lipid-rich AlbuMAX II was replaced by complementing culture media with an equivalent amount of fatty acid-free bovine serum albumin (Sigma), 30 µM palmitic acid (C16:0; Sigma) and 45 µM oleic acid (C18:1; Sigma).”

We used identical culture conditions to those described above: fatty acid-free BSA in place of lipid-rich AlbuMAX, 30 µM palmitic acid, and 45 µM oleic acid. We thus obtained growth results that contrast with the prior study and suggest that additional, future studies will be required to understand and resolve these differences.

Furthermore, it is too uncertain to conclude that ACP is only essential for the mevalonate pathway.

Please see our response above that clarifies our model for ACP function in supporting pyruvate kinase II and the many apicoplast pathways that appear to depend on PKII.

This would be a similar discussion to the Yeh et al. 2011 and the Swift et al., where induced Apicoplast knockout caused parasites to require IPP to survive, but there were always remnant apicoplast vesicles and thus the putative presence of an active FASII in the parasite, where de novo fatty acid synthesis could be maintained.

It is extremely unlikely that FASII remains active upon apicoplast disruption and loss of the apicoplast genome. The apicoplast-encoded SufB is lost upon apicoplast disruption and can no longer participate in making Fe-S clusters. Without Fe-S synthesis, the apicoplast lipoate synthase (LipA) cannot make lipoate to activate pyruvate dehydrogenase (E2 subunit) and produce the acetyl-CoA needed for FASII activity. There is no experimental evidence that FASII remains active upon apicoplast disruption and loss of the apicoplast genome.

Amiar et al. (2020) and Krishnan et al. (2020) showed that disruption of FASII and absence of de novo FA synthesis in T. gondii could be compensated by the exogenous supplementation of myristic acid, C14:0.

As explained above, we acknowledge that FASII contributes to Toxoplasma gondii growth and includes functions that appear to differ from P. falciparum.

Here, high fatty acid supplementation using commercially available fatty acids may include unexpected fatty acid species such as myristic acid in palmitic acid or oleic acid, since all commercially available fatty acids guarantee only >99% but not 100%. If P. falciparum requires a very, very low amount of myristic acid to survive, the amount of possible contamination, like 1 nM, may be sufficient to maintain their survival. Thus, ACP and FabH might be very important to generate de novo fatty acids within parasites, but this was not shown by the authors.

As noted above, we used identical culture conditions and commercial sources of defined fatty acids to those reported in the Amiar et al. study. We do not see a basis for the reviewer’s critique that the two studies utilized differing culture conditions. Nevertheless, we agree that future studies are needed to understand and resolve these differences.

Therefore, the manuscript currently contains incorrect conclusions on the potential essentiality/use of FASII, against current experimental evidence.

As explained above, we do not see a basis for the reviewer’s critique here or for viewing one study as more or less definitive than the other, as identical culture conditions were used yet contrasting results were obtained for reasons that remain uncertain. Future studies beyond the scope of the present manuscript will be required to fully understand and resolve these differences.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

We either request more solid experimental evidence showing the absence of fatty acid synthesis at low fatty acid conditions by re-doing the growth assay in the lower fatty acid feeding conditions without daily feeding to clarify if the ACP and FabH are essential in the blood stage growth, or not; as well as showing the absence of fatty acid synthesis at low fatty acid conditions using isotope labelled precursor. Without these, the authors cannot conclude on this important point. Alternatively, toning down the text to acknowledge the possibility of FASII being active and critical under certain conditions would be acceptable.

We note that the Amiar et. al 2020 study cited by the reviewer reported growth assays for WT and ∆FabI NF54 P. falciparum in low-lipid conditions that similarly lacked direct tests of FASII activity by isotope labeling.

We agree that our results, which utilized distinct ∆ACP and ∆FabD NF54 (PfMev) lines, contrast with the results and conclusions of the Amiar et al. study. We fully agree with the reviewer that future studies, utilizing tandem growth assays and isotope-labeling metabolic flux assays (e.g., mass spectrometry), will be required to fully test and understand the dependence of FASII activity on the lipid content of the growth medium and the functional dependence of P. falciparum growth on FASII activity in low-lipid conditions.

We have revised the final paragraph of the second results section of our manuscript to incorporate this perspective:

“These results contrast with the prior study [49] of ∆FabI parasites and the proposed model that blood-stage P. falciparum requires FASII activity for growth in low-lipid conditions and suggest that parasites can rely on scavenging host-derived fatty acids over a wide range of lipid conditions. Future studies involving tandem growth and isotope-labeling experiments of WT and ∆FASII parasites will be required to fully test and understand FASII function and the dependence of P. falciparum growth on this pathway in low-lipid conditions.”

Author response:

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

We again thank the editor and reviewers for their detailed attention to our work. In our previous revisions we endeavored to address the principal concerns raised by reviewers that we were capable of addressing. We recognize that asymptomatic pertussis transmission represents a particularly thorny area of epidemiology and public health, where multiple (and sometimes overlapping) mechanisms have been proffered even as empirical evidence remains thin, particularly in low-resource settings such as sub-Saharan Africa. A key finding of our work is that prospective surveillance in such a low-resource setting revealed abundant evidence of otherwise unobserved asymptomatic incidence. Moreover, as we note in our prior revisions, this finding is supported by recent work in South Africa and elsewhere (Kayina et al., 2015; Moosa et al., 2019, 2025). As such, we believe that further prospective surveillance in similar settings would be highly informative, a point that we have sought to emphasize in our present manuscript (and associated commentary).

While we broadly agree with many of the concerns raised by the reviewers, we believe that we are unable to significantly strengthen the present work through further revisions. We do, however, wish to respond to several points raised in these reviews. Of note, a reviewer raises the possibility of a "breakthrough strain" without reference to existing literature. We agree that we cannot test this hypothesis, and though it is not incompatible with our own findings, it is, however, not consistent with recent molecular surveillance in South Africa (Moosa et al., 2023). The reviewer also raises the potential of low adult vaccination coupled with recent reintroduction. This hypothesis relies on our investigation looking "at the right place and the right time", and further does not explain how immunologically naive adults would have escaped morbidity. We have adopted what we believe is a more parsimonious interpretation of our results (i.e., that asymptomatic infection represents evidence of previous immune exposure), though we agree that a more thorough exploration of this particular issue is warranted, particularly in light of our persistently colonized mothers. In addition, we have noted similar studies in sub-Saharan Africa that also found widespread evidence of asymptomatic pertussis, which we believe is inconsistent with a “right time, right place” interpretation.

A reviewer also pointed to the work of Warfel et al. (2014) and Althouse and Scarpino (2015). We are familiar with both of these studies and agree with their broad relevance to the field (our apologies for omitting Warfel et al.). The reviewer states that, "If the mechanism underlying the results in Zambia is that either WP or natural infection does not block transmission (in the absence of a breakthrough strain), that would upend many of the assumptions in pertussis research." Critically, we believe that our prospective field study of human patients in a real-world public health system complements previous research, including animal trials and simulation studies. Simply put, given that our study was unable to establish the prior vaccination or exposure status of participants, we do not claim to have shown evidence for transmission despite wP vaccination or prior infection.

Regarding Althouse & Scarpino (2015), we believe that, for the majority of readers, the most compelling analysis in their paper was the examination of genome sequences that pointed to substantial asymptomatic transmission in the US. This conclusion emerged from their population model, which required that “births” (representing transmission events) exceeded “deaths” (representing recovery of infectious individuals) in order to be consistent with the sequence data. Unfortunately, this paper does not provide a detailed explanation of their methods and data sources, nor is this work directly reproducible through, for example, an open-access code/data repository. We have explored the availability of US genome sequences over the time period of their study and were able to find only 36 sequences: 2 from the pre-vaccine era, 8 from the wP vaccine era, and 26 from the aP vaccine era. Given this notable imbalance in the number of sequences (and thus sequence diversity) that was biased in favour of the most recent time period, is it then surprising that the “birth rate” in their model had to exceed the “death rate” in order to match the genetic diversity in the data? Based on a careful inspection of this work, we do not consider its conclusions to represent a gold standard against which all subsequent studies should be judged. We also note that genomic surveillance and analysis of pertussis remains sparse relative to other fields, though recent works have added dramatically to the corpus of available sequences (Bridel et al., 2022).

Finally, we note that our previous revisions addressed several concerns raised in the present reviews. For example, we previously sought to address reviewers' about our presentation of the strength of our evidence. In this regard, we broadly agree with the reviewers, and we now state that our results "suggest that pertussis transmission occurs between minimally symptomatic mothers and their newborn infants." We believe this largely addresses a present reviewer's concern that 'the mother-to-infant transmission pathway should be framed as "highly suggestive" rather than "confirmed"'. We also note that our results examine three different threshold Ct values (survival analysis, Fig 4), a point that we believe partially addresses a reviewer's suggestion to "including a sensitivity analysis using a stricter cut-off" and concerns about "the decision to use a Ct<45 threshold, as this is higher than standard clinical cut-offs". Indeed, we discuss the issue of clinical cut-offs (and their appropriateness) at some length in the section, "Test reliability, disease surveillance, and public health where we state, "We recognize that such weak and potentially ambiguous signals may not be appropriate for clinical diagnosis. However, our results demonstrate that they nonetheless contain valuable information about pathogen presence and infection intensity that can (and should) be leveraged for disease surveillance." We have also included in the present work a detailed discussion of qPCR sensitivity and efficiency that we believe should interest others working in pertussis surveillance.

We do not view our own research as the "last word" in this rather controversial subject. In this spirit, we have attempted to present our work transparently, state our claims carefully, and underscore future activities that we believe would benefit the pertussis research community going forward. For example, we agree that further attention to shared exposure and functional immune data among low-resource communities could provide valuable insights into epidemiology and ecology of pertussis. However, we also believe the trade-offs of including one set of activities over another should be clearly acknowledged by researchers, clinicians, and public health officials. To simply state that we must measure more fails to account for the very real resource constraints that we all face.

Althouse, B. M., & Scarpino, S. V. (2015). Asymptomatic transmission and the resurgence of Bordetella pertussis. BMC Medicine, 1–12. https://doi.org/10.1186/s12916-015-0382-8

Bridel, S., Bouchez, V., Brancotte, B., Hauck, S., Armatys, N., Landier, A., Mühle, E., Guillot, S., Toubiana, J., Maiden, M. C. J., Jolley, K. A., & Brisse, S. (2022). A comprehensive resource for Bordetella genomic epidemiology and biodiversity studies. Nature Communications, 13(1), 3807. https://doi.org/10.1038/s41467-022-31517-8

Kayina, V., Kyobe, S., Katabazi, F. A., Kigozi, E., Okee, M., Odongkara, B., Babikako, H. M., Whalen, C. C., Joloba, M. L., Musoke, P. M., & others. (2015). Pertussis prevalence and its determinants among children with persistent cough in urban Uganda. PLoS One, 10(4), e0123240.

Moosa, F., du Plessis, M., Weigand, M. R., Peng, Y., Mogale, D., de Gouveia, L., Nunes, M. C., Madhi, S. A., Zar, H. J., Reubenson, G., & others. (2023). Genomic characterization of Bordetella pertussis in South Africa, 2015–2019. Microbial Genomics, 9(12), 001162.

Moosa, F., du Plessis, M., Wolter, N., Carrim, M., Cohen, C., von Mollendorf, C., Walaza, S., Tempia, S., Dawood, H., Variava, E., & others. (2019). Challenges and clinical relevance of molecular detection of Bordetella pertussis in South Africa. BMC Infectious Diseases, 19, 1–11.

Moosa, F., Kleynhans, J., Makhathini, L., du Plessis, M., Tempia, S., McMorrow, M. L., Moyes, J., Buys, A., Maake, L., Smit, S., & others. (2025). Bordetella pertussis infection and antibody dynamics in household cohorts in two South African communities, 2016–2018: Findings from the PHIRST study. Journal of Infection, 106550.

Warfel, J. M., Zimmerman, L. I., & Merkel, T. J. (2014). Acellular pertussis vaccines protect against disease but fail to prevent infection and transmission in a nonhuman primate model. Proceedings of the National Academy of Sciences, 111(2), 787–792. https://doi.org/10.1073/pnas.1314688110

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study investigates the role of asymptomatic pertussis carriage in transmission between mothers and their infants, in particular. The authors used a longitudinal cohort study that involved 1,315 mother-infant dyads in Lusaka, Zambia, and they utilized qPCR-based detection of IS481 to track Bordetella pertussis transmission over time. Insights from the study suggest that minimally symptomatic or asymptomatic mothers may act as a reservoir for B. pertussis transmission in the infants, thus challenging the traditional surveillance methods that focus on symptomatic cases. Additionally, the study also identified a subgroup of persistently colonized individuals where mothers were majorly asymptomatic despite sustained bacterial presence.

The authors aimed to improve comprehension of pertussis transmission dynamics in high-burden low-resource settings, and they advocated for enhanced molecular surveillance strategies to capture full pertussis infection, including those that might have gone undetected.

Strengths:

The strengths are the use of innovative study design, especially the longitudinal approach and routine sampling, rather than symptom-driven testing that minimizes bias in the study. The methodology was also rigorous and transparent by evaluating the IS481 signal strength to classify pertussis detection and conducting retesting to assess qPCR reliability. There were also important epidemiological insights, and the findings challenge the traditional wisdom by suggesting that pertussis transmission may frequently occur outside of symptomatic cases. The findings also showed its relevance to global health and policy by arguing for the incorporation of molecular tools like qPCR for surveillance of pertussis in low-resource settings.

Weaknesses:

These include reliability on qPCR-based detection without additional validation measures like confirmatory culture or serology. There are also potential alternate explanations for transmission patterns observed in the study such as shared environmental exposure or household transmission. Additionally, there is limited generalizability as the study was done in a single urban site in Zambia. There is also a lack of functional immune data.

Reviewer #2 (Public review):

Summary:

In this paper, the authors describe the results of a longitudinal study of pertussis infection in mother/infant dyads in Lusaka, Zambia. Unlike many past studies, the authors assessed the infection status of individuals independently of whether they were symptomatic for a respiratory infection. As a result, this work represents one of the first studies specifically designed to assess asymptomatic transmission of pertussis. Using qPCR, the authors find strong evidence for the role of asymptomatic transmission from mothers to infants and also evidence for long-term bacterial carriage. This work represents an important contribution to our understanding of the global burden of pertussis. Also, it highlights the still under-appreciated role of asymptomatic transmission across many infectious diseases (including vaccine-preventable ones).

Strengths:

Unlike many past studies, the authors assessed the infection status of individuals independently of whether they were symptomatic for a respiratory infection. As a result, this work represents one of the first studies specifically designed to assess asymptomatic transmission of pertussis. Using qPCR, the authors find strong evidence for the role of asymptomatic transmission from mothers to infants and also evidence for long-term bacterial carriage.

Weaknesses:

While I am quite enthusiastic about the work, I am concerned that a number of likely relevant confounders were not discussed and that the broader implications of their findings were not well grounded in the existing literature. For example, I could not find information on the vaccination status of the mothers in the study. Given the conclusions about asymptomatic transmission and the durability of immunity, it is important to know the vaccination status of the mothers. Moreover, did the authors have other metadata on the mother/infant dyads, e.g., household size, vaccination status of household members, etc.? Given the potential implications of more widespread asymptomatic transmission associated with pertussis infection, I believe the authors should better couch their results in the context of the broader debate around asymptomatic transmission.

We appreciate the reviewers' detailed feedback. We provide an overview of our responses here and we address specific recommendations below. In light of reviewers’ comments, we have revised our manuscript in order to improve the clarity of our presentation and to better situate our results within the context of the existing literature. Unfortunately, as the field study has been concluded, many of the reviewers’ recommendations are not possible. These include additional testing (i.e., culture or serology) or sequencing. We have updated the manuscript to more clearly indicate our knowledge regarding maternal vaccine status and immunological immunity of study participants. We have also provided a more comprehensive overview of existing pertussis studies, including genomic surveillance and details regarding sub-Saharan Africa and Zambia in particular. Finally, we have revised the formatting of Figure 4 (survival analysis) to more clearly highlight differences between mothers and infants and to better align with the text, and note that the underlying results are unchanged.

A particular concern raised in the reviews that we wish to address is the recommendation of culture- or serology-based tests as "confirmatory". We have revised the manuscript in light of this feedback to better reflect our own position on this matter. We believe these recommendations do not adequately account for important trade-offs between testing sensitivity and specificity that are widely recognized in both clinical practice and epidemiology (Enøe et al., 2000; Florkowski, 2008; Swift et al., 2020). When the results of different testing methodology disagree, rarely is one method, a priori, correct. Rather, the disagreement may point to specific test limitations or important biological questions about the study system.

In the case of pertussis detection, cell culture is recognized for its very low sensitivity, while serological detection is complicated by debate around appropriate threshold levels and time horizons for seroconversion and subsequent decay (Lee et al., 2018; van der Zee et al., 2015). Furthermore, while anti-PT antibodies are a common target of serological detection, these are not reliable correlates of protection (Mills, 2001; Wilk et al., 2019), nor are they reliably generated in response to colonization (de Cellès & Rohani, 2024; Graaf et al., 2020). Overall, the detailed relationship between exposure, carriage, transmissible infection, and the dynamics of anti-PT serology remains poorly characterized (Craig et al., 2020; de Cellès et al., 2025).

While we agree that these are important questions in epidemiology and public health, we nonetheless wish to highlight that there is no “free lunch": each additional test and protocol comes with additional cost and complexity that should be evaluated based on the specific goals of the intended surveillance. In our case, the repeated sampling of longitudinal surveillance serves as a low-cost "confirmatory" testing regime. We disagree that cell culture would have added value to the present study and would not recommend its addition to future studies (primarily due to low sensitivity). While we agree that before-and-after serology of mothers would have added important context to the present study, we nonetheless expect that significant ambiguity would have surrounded any such results (e.g., Moosa et al. (2025)).

One area that we strongly agree warrants further attention is the household dynamics in pertussis transmission, particularly in low-resource settings where crowding is common. In our study we were not able to rule out environmental and/or shared transmission events, though our survival analysis did demonstrate a greater impact of mothers on infants than vice versa, results which suggest a causal mechanistic role. In previous studies we detailed the demographics of household size, number of children, and mothers' age (Gill et al., 2021; Gunning et al., 2020), though we have not conducted formal analyses of these important covariates here. We also note that the code and data are freely available, allowing for others to build on our work.

We believe that future prospective studies are an invaluable tool for directly tracking pertussis disease transmission, including both community and household studies. We have argued here for the value of qPCR-based community surveillance, which could integrate into existing public health activities. Regarding household studies, we note that a key challenge in implementing these studies is selecting an appropriate sampling interval and duration to best capture epidemiological linkages. Our results suggest that qPCR-based real-time population-level surveillance could be used to initiate such a prospective household study during a pertussis outbreak so that a higher sampling frequency (e.g., weekly swabs) could be gainfully employed over a shorter time period.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Enhance Validation of qPCR Findings:

We address these comments above at greater length. We also note that the term “false positive” is rather ambiguous here, as we lack a clear distinction between carriage and transmissible infection. We note that our manuscript includes a considerable discussion of qPCR validation, including negative controls and sample retesting. We agree that test sensitivity and specificity remains an important question, and have endeavored to clearly indicate these concerns throughout the manuscript.

(2) Clarify Transmission Dynamics:

While we agree that this is an important question, we lack the relevant sequence data to test it. Notably, we suspect that any such phylodynamic linkage would require genomic sequencing due to the relatively low genetic diversity observed in pertussis (see, e.g., population-level estimates of time to most common ancestor in Lefranc et al., (2022). However, sequencing pertussis genomes remains resource-intensive, and we expect that the deployment of such sequencing at scale would be cost-prohibitive in low-resource settings.

We have revised our manuscript to underscore uncertainties around shared/household exposure. We also direct the reviewer’s attention to our survival analysis, where a notable asymmetry exists between mothers and infants. Here, mothers’ prior qPCR signals exhibit a larger impact on their infants than infants on their mothers (Fig 4). If shared exposure was the principal cause of the observed increase in hazard in ego from alter, then we would expect no such asymmetry between mothers and infants.

(3) Expand Discussion on Public Health Implications:

As noted above, we have revised our introduction and expanded our discussion to better account for the existing literature. And, while we are hesitant to put forward specific recommendations based on our study, we feel confident in stating that active pertussis surveillance in low-resource settings is A) almost entirely absent B) possible to achieve, and C) necessary to resolve long-standing questions about pertussis epidemiology at regional and national levels. We have endeavored to clarify these points, particularly within the discussion.

(4) Address the Role of Immunity More Directly:

While we lack such immune data, we have pointed to recent work from the notable PHIRST study in South Africa, as well as highlighted ambiguities surrounding these data.

Reviewer #1 (Recommendations for the authors):

(1) Do we know the vaccination status of the mothers in the study? … If these data are not available, I think that the paper must be re-framed to acknowledge that all the conclusions are statistical in nature, based on publicly available vaccine coverage data from Zambia.

We do not have information on the immunization status of mothers, though we cite national rates for Zambia across the relevant time period. We have clarified this point in the revised manuscript. We have endeavored to clearly acknowledge that many of our conclusions are statistical in nature and to clearly quantify the strength of evidence.

We strongly disagree that anomalously low vaccination rates amongst mothers (i.e., relative to national averages) would materially alter the interpretation of our findings.

Overall, our findings strongly suggest ongoing pertussis transmission in this population. Based on this, we expect that mothers in our study who were not vaccinated would likely have some degree of infection-derived immunity. Indeed, some have argued that the preponderance of mild/asymptomatic infections in mothers is, of itself, evidence of prior immunological exposure (Fine & Clarkson, 1982).

(2) Do we know anything about rates of pertussis in Zambia, especially in the study site?

We address this important question in the discussion. In particular, we state that: “As a populous, middle-income and primarily urban country, Zambia offers an evocative example of pertussis surveillance, where no cases have appeared in official WHO reports since 2009”.

(3) I couldn't find information in the paper related to the severity of infection in the infants. It's mentioned in the section describing results in Figure 5, but I only saw analyses with symptoms (as opposed to severe symptoms). Do you have outcome data from infants testing positive?

This question was addressed in more detail in our previous work (Gill et al., 2021), which we briefly summarize in the Introduction. We also show the frequency of severe symptoms in Fig 5 (bottom panel), and detail mild versus serious symptoms in our subgroup analysis (Fig 7D).

(4) Do we know anything about vaccine-resistant strains of pertussis in Zambia?

We are not aware of any such work. As we noted above (and now address in our Discussion), widespread genomic surveillance and microbiological characterization of pertussis are sorely lacking across Africa.

(5) While I believe sequencing is beyond the scope of the current study, the authors should comment on the potential utility of sequencing elements of the pertussis genome and use that to demonstrate causality and direction of transmission more strongly.

We believe that existing literature has addressed the potential of sequence data and phylodynamics to infer transmission, particularly for pathogens with high mutation rates such as RNA viruses. To date, research into the phylodynamics of pertussis has focused exclusively on population-level dynamics (Lefrancq et al., 2022), where estimates of time to most recent common ancestor (TMRCA) are long, indicating low genomic variability at the scale of countries and years. To our knowledge, no work on pertussis has directly inferred transmission chains from sequence data. Given the existing evidence, we expect that any such work would require genome-level sequencing, which would likely be cost-prohibitive in low-resource settings.

(6) … However, it would be helpful to understand more about how your results fit into the broader story around pertussis resurgence. … if the infant cases were all mild, they might never have been captured in surveillance data sets.

We believe that a key result of our study is the remarkable mismatch between country-level symptoms-based surveillance and prospective surveillance, which demonstrates that such mild cases have almost certainly not been captured. These findings are mirrored by recent work in South Africa (now addressed in our Discussion, see Moosa et al. (2025)). We believe that prospective surveillance, particularly in under-surveilled regions, is critical to understanding pertussis transmission writ large, which we have attempted to communicate throughout our discussion.

(7) Relatedly, if there are still high rates of asymptomatic mother-to-infant transmission with whole cell vaccination, then why is there an observed drop in infant pertussis following whole vaccination in most countries?

In previous work, we demonstrated that some infants in this cohort exhibited asymptomatic infection (Gill et al., 2021). We note that a drop in pertussis incidence amongst infants after the roll-out of the whole-cell vaccine is not contradictory with our findings. We want to clarify that our results, and evidence that mother-to-infant transmission can occur, does not imply that the whole-cell vaccine fails to protect against transmission.

We have previously used epidemiological evidence to infer the population-level impacts following the roll-out of whole-cell pertussis infant immunization. For example, we observed an increase in the inter-epidemic period that, together with the drop in infant cases, are consistent with a reduction in transmissible infections (Broutin et al., 2010; Rohani et al., 2000).

References

Broutin, H., Viboud, C., Grenfell, B. T., Miller, M. A., & Rohani, P. (2010). Impact of vaccination and birth rate on the epidemiology of pertussis: A comparative study in 64 countries. Proceedings of the Royal Society B: Biological Sciences, 277(1698), 3239–3245.  https://doi.org/10.1098/rspb.2010.0994  

Craig, R., Kunkel, E., Crowcroft, N. S., Fitzpatrick, M. C., Melker, H. de, Althouse, B. M., Merkel, T., Scarpino, S. V., Koelle, K., Friedman, L., Arnold, C., & Bolotin, S. (2020). Asymptomatic Infection and Transmission of Pertussis in Households: A Systematic Review. Clinical Infectious Diseases, 70(1), 152–161. https://doi.org/10.1093/cid/ciz531

de Cellès, M. D., & Rohani, P. (2024). Pertussis vaccines, epidemiology and evolution. Nature Reviews Microbiology, 1–14. https://doi.org/10.1038/s41579-024-01064-8

de Cellès, M. D., Wong, A., Dalby, T., & Rohani, P. (2025). Natural immune boosting biases pertussis infection estimates in seroprevalence studies. Nature Communications, 16(1), 8883. 

Enøe, C., Georgiadis, M. P., & Johnson, W. O. (2000). Estimation of sensitivity and specificity of diagnostic tests and disease prevalence when the true disease state is unknown.  Preventive Veterinary Medicine, 45(1–2), 61–81.

Fine, P. E. M., & Clarkson, JacquelineA. (1982). The recurrence of whooping cough: Possible implications for assessment of vaccine efficacy. The Lancet, 319(8273), 666–669.  https://doi.org/10.1016/S0140-6736(82)92214-0 

Florkowski, C. M. (2008). Sensitivity, specificity, receiver-operating characteristic (ROC) curves and likelihood ratios: Communicating the performance of diagnostic tests. The Clinical Biochemist Reviews, 29(Suppl 1), S83.

Gill, C. J., Gunning, C. E., MacLeod, W. B., Mwananyanda, L., Thea, D. M., Pieciak, R. C., Kwenda, G., Mupila, Z., & Rohani, P. (2021). Asymptomatic Bordetella pertussis infections in a longitudinal cohort of young African infants and their mothers. eLife, 10, e65663. https://doi.org/10.7554/elife.65663

Graaf, H. de, Ibrahim, M., Hill, A. R., Gbesemete, D., Vaughan, A. T., Gorringe, A., Preston, A.,  Buisman, A. M., Faust, S. N., Kester, K. E., Berbers, G. A. M., Diavatopoulos, D. A., & Read, R. C. (2020). Controlled Human Infection With Bordetella pertussis Induces Asymptomatic, Immunizing Colonization. Clinical Infectious Diseases: An Official Publication of the Infectious Diseases Society of America, 71(2), 403–411.  https://doi.org/10.1093/cid/ciz840

Gunning, C. E., Mwananyanda, L., MacLeod, W. B., Mwale, M., Thea, D. M., Pieciak, R. C., Rohani, P., & Gill, C. J. (2020). Implementation and adherence of routine pertussis vaccination (DTP) in a low-resource urban birth cohort. BMJ Open, 10(12), e041198.

Lee, A. D., Cassiday, P. K., Pawloski, L. C., Tatti, K. M., Martin, M. D., Briere, E. C., Tondella, M. L., Martin, S. W., & Group, C. V. S. (2018). Clinical evaluation and validation of laboratory methods for the diagnosis of Bordetella pertussis infection: Culture, polymerase chain reaction (PCR) and anti-pertussis toxin IgG serology (IgG-PT). PLoS One, 13(4), e0195979.

Lefrancq, N., Bouchez, V., Fernandes, N., Barkoff, A.-M., Bosch, T., Dalby, T., Åkerlund, T.,  Darenberg, J., Fabianova, K., Vestrheim, D. F., Fry, N. K., González-López, J. J.,  Gullsby, K., Habington, A., He, Q., Litt, D., Martini, H., Piérard, D., Stefanelli, P., … Brisse, S. (2022). Global spatial dynamics and vaccine-induced fitness changes of Bordetella pertussis. Science Translational Medicine, 14(642), eabn3253.  https://doi.org/10.1126/scitranslmed.abn3253 

Mills, K. H. G. (2001). Immunity to Bordetella pertussis. Microbes and Infection, 3(8), 655–677. https://doi.org/10.1016/s1286-4579(01)01421-6 

Moosa, F., Kleynhans, J., Makhathini, L., du Plessis, M., Tempia, S., McMorrow, M. L., Moyes, J., Buys, A., Maake, L., Smit, S., & others. (2025). Bordetella pertussis infection and antibody dynamics in household cohorts in two South African communities, 2016–2018:  Findings from the PHIRST study. Journal of Infection, 106550. 

Rohani, P., Earn, D. J., & Grenfell, B. T. (2000). Impact of immunisation on pertussis transmission in England and Wales. The Lancet, 355(9200), 285–286. https://doi.org/10.1016/S0140-6736(99)04482-7 

Swift, A., Heale, R., & Twycross, A. (2020). What are sensitivity and specificity?  Evidence-Based Nursing, 23(1), 2–4.

van der Zee, A., Schellekens, J. F., & Mooi, F. R. (2015). Laboratory diagnosis of pertussis.  Clinical Microbiology Reviews, 28(4), 1005–1026.

Wilk, M. M., Allen, A. C., Misiak, A., Borkner, L., & Mills, K. H. G. (2019). The immunology of Bordetella pertussis infection and vaccination. In Pertussis: Epidemiology, Immunology & Evolution. Oxford University Press.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The manuscript by Fisher et al describes the molecular mechanism underlying how G beta gamma subunits engage with the beta 3 isoform of PLC. The paper used a combination of cryo EM, BRET assays, and biochemical assays of PLC beta activity. A key discovery is that G beta gamma is not sufficient to drive membrane binding by itself, and instead promotes G alpha activation. The work is important, but suffers slightly from some ambiguity in the actual interface that is present in their cryo EM model, as crosslinkers could stabilise a transient and non-native complex. This is somewhat abrogated by the careful mutational analysis, which shows that mutation of any of these three sites does somewhat block PLC beta G beta gamma activation. However, there could be some improvement in the presentation of this data, as well as possible mutant selection. Overall, this paper is a nice complement to the Falzone et al paper, showing the membrane-bound complex of PLCB3 on membranes, with this work building on this work, highlighting the importance this will have in our full understanding of PLC beta activation.

Thank you for the positive feedback.

Major concerns:

My biggest concern is the potential that this interface is artefactual based on the crosslinking strategy utilised. Here are thoughts on how this could be better validated, presented in a more convincing way.

(1) The authors' main claim is that there is a degree of plasticity of G beta gamma binding to the PLC beta 3 isoform, with three possible binding sites. The main complication of this is, of course, the possibility that the crosslinking stabilises a non-native complex, driven by a mutated cysteine.

Because of this, any other additional details about this interface are going to be critical for the scientific audience to judge if this is accurate.

What would greatly help Figure 1 is an evolutionary conservation analysis of the novel Gbg interface in PLC, to see how well this is conserved, and compare this to the conservation of the previously annotated sites. Conservation of these sites on both the G beta gamma and PLC side would help justify this as a native complex.

This will also help orient the reader to the identity of the mutated residues assayed in Figure 3.

We agree that crosslinking can capture non-physiologically relevant interfaces. However, because we do not observe any crosslinking between Gβγ and a PLCβ3 variant that retains a cysteine in the X–Y linker or between PLCβ3 and any other cysteine in the Gβγ heterodimer, we believe it is site-specific.

The question about sequence conservation in the Gβγ–PLCb3 interfaces is interesting and we have included this information in Figures S8 and S9.

(2) The g beta gamma orientation is also different than what I have observed in previous g beta gamma effector structures. Is there any precedent for this as an effector interface? A supplemental figure comparing this structure to other g beta gamma interfaces from other enzymes, for example recent Tesmer structure with PI3K.

We agree that the orientation of Gβ in the crosslinked structure is different. We include a comparison of this reconstruction to other published Gβγ–effector complexes as Figure S6.

(3) The mutational analysis in Figure 2D-G seems to give some strange results, and I have some question why certain residues were chosen rather than others. Mutation of the Gbg side will be more complicated, as of course that can affect any of the three surfaces. My main question is that, from the way Figure 2A is oriented, the main salt bridge in their novel interface to me looks like R199-D228, with K183 being in the wrong orientation to E226, and D167 being far from any charged residues. Why did the authors not make the corresponding R199 to D or E mutation?

Thank you for pointing this out, and we expanded our analysis to include this residue. The R199A and R199E mutations had no defects in basal or Ga_q-stimulated activities. However, R199A had 3-fold lower activation by Gβγ, while R199E was not activated in this assay. The R199E mutation also had significantly decreased agonist-dependent BRET with Gβγ and decreased PI(4,5)P2 hydrolysis, while retaining robust recruitment to the plasma membrane by Gα_q. These data is included in the main text and Figures 2-4.

(4) To help the reader's interpretation of Figure 2A, I would recommend a supplemental figure showing the density for interfacial residues, as that also would increase confidence in the interface.

Thank for the suggestion. In revised Figure S3, we show the Gβγ–PLCb3 D892-PH_cys complexes determined in this study at different contour levels.

Reviewer #2 (Public review):

In this manuscript, the authors dissect how Gβγ potentiates PLCβ3 signaling in cells. Using engineered crosslinking to stabilize a Gβγ-PLCβ3 complex, single particle cryo-EM, and cell-based functional assays, they identify and map multiple putative Gβγ interaction surfaces on PLCβ3, including a previously unrecognized binding mode. Structure-guided mutagenesis supports the functional relevance of these interactions and suggests that Gβγ potentiation is not primarily mediated by PLCβ3 membrane recruitment, but instead enhances PLCβ3 activity after the lipase is already at the membrane.

Previous reconstitution work on the membrane surface (Falzone & MacKinnon, 2023) proposed a recruitment/partitioning-centric model in which Gβγ increases PLCβ3 output largely by elevating its membrane surface concentration, whereas Gαq primarily increases catalytic turnover; under those reconstitution conditions, the two inputs can combine approximately multiplicatively. In receptor-driven cellular signaling, however, PLCβ3 is robustly recruited to the plasma membrane upon Gαq activation, which raises the question of whether Gβγ contributes mainly through additional recruitment or through a post-recruitment mechanism once PLCβ3 is already at the membrane.

This manuscript helps address that gap by using membrane-anchored PLCβ3 and complementary cellular readouts to separate "getting PLCβ3 to the membrane" from "boosting activity once PLCβ3 is already there." Their results argue that, in cells, membrane recruitment is largely dominated by Gαq·GTP, while Gβγ can further potentiate PIP2 hydrolysis after membrane association, consistent with a modulatory role at the membrane rather than primary recruitment.

Overall, the work provides a structural and mechanistic framework for Gβγ-PLCβ3 cooperation and helps clarify the basis of Gq pathway amplification. The manuscript is generally strong, but some issues need to be addressed.

Thank you for the positive comments.

Major comments:

(1) BMOE/BM(PEG)2 crosslinking may enforce a non-native docking geometry, potentially compromising the physiological relevance and precision of the Gβγ-PLCβ3 interface as described. Although a >50% 1:1 crosslinked complex is formed and remains active, the solution maps show lower local resolution for Gβγ, consistent with a dynamic, potentially heterogeneous, interface. One interface is captured via a single engineered cysteine pair (PLCβ3 E60C-Gβ C271), which could potentially bias the pose. It would be helpful if the authors could provide additional orthogonal support (e.g., alternative crosslinked sites) and bolster the clarification of its uniqueness and relevance.

We did attempt to isolate other crosslinked complexes. PLCβ3-D892 self-crosslinked under all reaction conditions, while PLCβ3-D892 XY_Cys, which retains an endogenous cysteine within the X–Y linker (C516), did not result in any crosslinked product when incubated with Gβγ. Only the PLCβ3-D892 E60C crosslinked to Gβγ. With the exception the C68S mutation at the C-terminus of Gg to eliminate its prenylation site, all endogenous cysteines were retained in both Gβ and Gγ. Indeed, Gβ contains two solvent-exposed cysteines in its canonical effector binding surface (C204 and C271), but we did not observe any crosslinker density involving C204. While we cannot exclude the possibility that crosslinking occurred between PLCβ3-D892 E60C and other residues in Gβγ, we were unable to identify any 2D classes corresponding to these alternative conformations. These observations, together with the high efficiency of crosslinking, are consistent with a stable and persistent interaction.

(2) In the crosslinked structure, the authors report that GβD228 interacts with PLCβ3 R199 and K183. In Figure 2A, R199 appears closer to Gβ D228 than K183, yet only K183 is functionally tested. Testing R199 (e.g., R199E/R199A) would strengthen the structure-guided validation of this interface.

We agree, and functional analysis of PLCb3 R199E is included in the revised manuscript (see Figures 2-4).

(3) The mutagenesis strategy appears inconsistent across figures/assays, which makes it difficult to interpret phenotypes and directly link the functional data to the proposed interfaces. For example, in Figure 2E, we see R185L but R215E, while residue L40 is mutated to Gly in the IP accumulation assays but to Glu/Lys (L40E/K) in the BRET assays (Figures 3B/3D/3F). The authors should (i) clearly justify the rationale for each substitution (conservative vs charge-reversal, interface disruption, etc.) and (ii), where possible, test the same mutants across assays (or provide evidence that alternative substitutions yield consistent conclusions).

Mutagenesis experiments were initially carried out independently in the Lambert and Lyon Labs. As the study progressed, additional mutants were identified and/or designed based on results from both groups. The residues subject to mutagenesis are overall consistent across the different assays, with differences in the identity of the mutation varying in some cases. The L40G mutation is one such example, where given its modest impact on Gβγ-mediated activation in the IP accumulation assay, more impactful changes were made (L40E and L40K) for the BRET and signaling assays. In the revision, we now state that mutations were designed to maximally disrupt the three observed interfaces, such as by changing the size of the side chain and/or introducing charge reversal mutants.

Reviewer #3 (Public review):

Summary:

PLCβ3 is activated by both Gαq and Gβγ subunits. This paper follows previous solutions and cryoEM studies of PLCβ3 / Gβγ, trying to understand the molecular details of activation using cellular BRET assays and cryoEM.

Strengths:

The authors find evidence for multiple binding sites on PLCβ3 for Gβγ and suggest that Gβγ is not bone fide activator per se but enhances Gαq activation by positioning the catalytic site towards substrate, although this is not completely convincing. Although these sites may not naturally be operative, the authors might want to develop the potential role of these sites.

The authors also find that this activation is not through recruitment of the enzyme to the membrane by Gβγ released upon G protein activation, in accord with other PLCβ enzymes, but not for PLCβ3, and again, the authors might want to develop this point further.

Thank you for the suggestions. We are investigating whether the other PLCb isoforms contain multiple Gβγ binding sites and the relative importance of preactivation by Ga_q for a manuscript in preparation.

Weaknesses:

(1) I'm confused as to why the authors feel that their mechanism is distinct from the two-state enzyme, the synergistic activation proposed by Ross in 2011, using a primarily thermodynamic argument. As written, the authors appear to be very reliant on structural and BRET studies that do not give the details that would disprove this interpretation. The main issue is that the author's mechanism does not fully explain how Gβγ activation occurs for PLCβ2 in reconstituted systems in the absence of Gαq subunits.

The reconstitution experiments are under extremely artificial conditions, using nM-µM of purified proteins and liposomes that contain up to 30% PI(4,5)P2. Under these conditions, we think the increased activity is due to interfacial activation promoted by Gβγ binding to the lipase once it is associated with the liposome surface. This would be sufficient to account for the dose-dependent increase in both PLCb2 and PLCb3 activity as a function of Gβγ concentration. Given the higher basal activity of PLCβ2 and its decreased sensitivity to activation by Ga_q, one possible explanation is that this isoform differs in its autoinhibition and/or structure of its proximal CTD that Ha2’ displacement is not a prerequisite for activation. In addition, Gβγ may also be a direct activator of PLCβ2. Further studies, ideally in cell-based systems, are needed to answer these questions.

(2) In a recent study, McKinnon presents a model showing that Gαq and Gβγ activate PLCβ3 by two distinct pathways and that activation by Gβγ occurs through membrane recruitment. It is not surprising that the authors find that this is not true since the pelleting method used by McKinnon is subject to error. The authors should directly address the limitations of this previous work and the changes in proteoliposomes with sedimentation that alter partition coefficients. Although the inability of Gβγ to drive membrane binding is in accord with the quantitative studies of Scarlata, showing that the affinity of PLCβ3 to Gβγ is fairly weak as compared to the intrinsic membrane partition coefficient.

We have added some of the limitations of proteoliposome sedimentation experiments to the discussion.

(3) It was proposed many years ago that in signaling complexes Gαq - Gβγ may not have to fully dissociate when binding PLCβ, but rather shift their relative orientation when binding to PLCβ to allow activation. Is their model consistent with this? Is it possible that PLCβ3 keeps Gβγ from diffusing to enhance the rate of Gq / Gβγ re-association?

Our crosslinked complex is compatible with simultaneous binding of a Gα_q-Gβγ heterotrimer to the PLCb3, without disrupting the observed interface. If Gαq were to interact with the Gβγ molecules bound to the PH or EF hands, the interaction would be mediated by the N-terminal helix of Gα_q. It is possible Gβγ–PLCβ3 interactions may slow heterotrimer reassociation, but this may be complicated by the intrinsic GAP activity of the lipase.

(4) The authors find that Gβγ binds multiple sites, and it is clear that the PH domain site is the primary one in accord with previous work. Could these weaker sites be an artifact of the elevated concentrations used in cryoEM and BRET assays?

While more studies have focused on the PH domain as a Gβγ binding site, our data does confirm the EF hands are also functionally relevant. To our knowledge, the role of the EF hands has not been investigated in this capacity until very recently, and so we hesitate to label them primary or secondary. It is possible the EF hands may be a lower-affinity site for Gβγ and the protein concentrations needed in cryo-EM drive complex formation. However, it is also possible the concentration of free Gβγ adjacent to an activated receptor may be high enough to saturate the PH and EF hand binding sites.

(5) Although their assays infer differences in binding affinities, it would strengthen the paper if the authors could estimate the association energies of these different binding sites. This estimation would also address the concern stated above.

We appreciate this suggestion and quantifying the affinities of the Gβγ–PLCβ3 interactions is the subject of future studies.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Please correct PIP2 to the correct PIP2 (many examples throughout).

These have been corrected.

Reviewer #2 (Recommendations for the authors):

Minor comments:

(1) Figure S1B: The lane-condition labels above the third gel appear to be incorrect, as both lanes are marked identically (Gβγ +/+, PLCβ variant +/+, BMOE +/+) despite clearly different banding patterns. Please confirm.

We have confirmed the markings above the gels are correct.

(2) In Figure S2, the authors show three fitted models, but the helical density for Gβγ cannot be seen in two of them at the displayed contour level. The authors should provide views of the map at different contour levels (thresholds) to better support the model fitting. Otherwise, it is difficult to assess whether the Gβγ subunit could adopt alternative orientations (i.e., whether it may be rotated) within the density.

We have included a new figure (Figure S3) that provides images of the maps at different contour levels.

(3) Page 5: "where PLCβ3 is increased by the overexpression of either Gβγ or Gαq" should be revised to "where PLCβ3 activity is ...".

This sentence has been corrected.

(4) Figure 2: Please label residue R215 in Figure 2A/2B (or the relevant structural panel), since R215E is tested in 2E but the position is not shown.

R215 is now included in Figure 2C.

(5) Page 19, Figure 2 legend: "Changes ... Figure S3" should be "Changes ... Figure S5".

We have corrected this figure call.

Reviewer #3 (Recommendations for the authors):

The studies seem well carried out, although more details regarding the BRET controls and the significance of the values should be included.

We have revised the captions to provide more details about the experimental controls and a brief description of significance. Individual p-values are included in the supplemental tables.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

I thank the authors for the revised manuscript and for the detailed responses.

I think the main points raised in the review have now been addressed. In particular, the new experiment with TbPLK inhibition and mass spectrometry is an important addition, as it provides direct evidence that phosphorylation of KIN-G at Thr301 and Ser569 depends on TbPLK activity in cells.

I also appreciate that the authors have toned down the interpretation of the Golgi phenotype. The revised text now makes clear that the fluorescence data show altered Golgi/ERES organization or duplication, but do not prove a structural defect in Golgi biogenesis.

The added discussion of the T301A result is also helpful. The finding that only a small fraction of KIN-G is phosphorylated at Thr301 in asynchronous cells makes the lack of a strong T301A phenotype more understandable.

Overall, I am happy with the revision of the beautiful manuscript.

Thank you for your critical review and insightful comments.

Reviewer #2 (Public review):

Summary:

The authors identify KIN-G as an in vitro substrate for phosphorylation by TbPLK and show that several of the in vitro P-ated sites, including T310, overlap with P-ation sites seen in live cells. The authors further show that PLK-mediated P-ation inhibits KIN-G binding to microtubules in vitro, as does a KIN-G-T301D mutant, and that expression of a KIN-G-T301D Phospho-mimic in T. brucei phenocopies KIN-G RNAi knockdowns, producing defects in cell division, morphogenesis of the centrin arm, FAZ and other cellular structures, as well as misplaced cytokinesis furrow.

Understanding cytoskeletal rearrangements that drive cell division in T. brucei is an important and unresolved problem, so the work addresses important questions that are of great interest. PLK and KIN-G have previously been shown to be important for cell division and morphogenesis of cytoskeletal structures that drive cell division in T. brucei. The current work advances our understanding by suggesting a potential mechanism by which PLK and KIN-G might participate, namely through PLK-dependent P-ation to control KIN-G MT binding activity.

Strengths:

The authors use a rigorous combination of biochemistry, phosphoproteomics, cell biology, and mutant analysis to support their conclusion that PLK-mediated P-ation of KIN-G negatively regulates KIN-G microtubule binding and this may explain the observation that a KIN-G T301 phosphomimic mutant blocks cell division and perturbs biogenesis of cytoskeletal structures that drive cell division and morphogenesis. Combining rigorous and informative in vitro studies with mutant analysis in live cells is a great strength. The work is solid and important, though a few pieces are needed to fully connect the in vitro findings with the in vivo observations, as detailed below.

Weaknesses:

Overall, I find this work to be solid, and to provide an important addition to our understanding of mechanisms controlling cell division in T. brucei. The biochemistry, in particular, is rigorous and convincingly demonstrates PLK can P-ate KIN-G, altering its MT-binding ability. Analysis of phospho-mutants of KIN-G in live T. brucei support the conclusion that P-ation of KIN-G at T301 negatively affects KIN-G function in vivo. I think, however, that the results fall short of supporting the title, because, although the data convincingly show that PLK can phosphorylate KIN-G at T301 in vitro, and that T301 is P-ated in vivo, they do formally demonstrate (nor even test) whether PLK is the kinase responsible for this phosphorylation in vivo (experiments to address this seem quite feasible). I also do not see where the authors try to reconcile the absence of phenotype for KIN-G-T301A with the implied importance of KIN-G phosphorylation by PLK in cell division, which calls into question the need for P-ation of KIN-G-T301 in cell division. Suggestions for addressing these concerns are provided below.

My two main questions are:

(1) What is the biological relevance of KIN-G P-ation at T301?

(a) The authors report no defect for the KIN-G-T301A mutant, so what then is the need for T301 P-ation, if the cell gets along fine without it? One step toward addressing this would be to ask what fraction of KIN-G shows P-ation at T301. Although published studies indicate P-ation at T301, it isn't known what percentage of KIN-G in the cell is P-ated. One might anticipate, for example, that T301-P is a small minority of the population in asynchronous cultures and that T301 P-ation increases at specific cell cycle stages.

(b) Published work links PLK to cell division, FAZ elongation, etc... The current work suggests that one role of PLK is to P-ate KIN-G at T301. In contrast, however, the current work also indicates that P-ation of KIN-G at T301 is unnecessary for normal cell division, FAZ elongation, etc....

(c) Some experiments or at least commentary on points a and b above would strengthen the paper.

- The authors have now addressed this question by assessing what % of KING is phosphorylated at T301 and adding commentary on this point in the revised paper.

- I would suggest that the model (new figure 8) include a dephosphorylation step, as that is proposed by the authors in the text. Also include in the legend some commentary on the role of phosphorylation, which is the center point of this paper, but not currently mentioned.

We have modified the model in Figure 8 to include dephosphorylation by an unknown protein phosphatase and a statement about the role of TbPLK phosphorylation on KIN-G function. Thank you.

(2) Is PLK the kinase that P-ates Kin-G T301 in vivo?

(a) The authors show PLK P-ates T301 (and other residues) in vitro, and that T-301 is P-ated in vivo. To bring the analysis full circle, it would be informative to examine KIN-G P-ation in a PLK mutant or upon inhibition of PLK with published inhibitors. This seems to be a very doable experiment with the tools available.

- The authors have addressed this question by demonstrating that T301 phosphorylation is reduced upon treatment with a PLK inhibitor, thus supporting that PLK phosphorylated T301 in vivo. It is noted that one might consider an alternate kinase is also able to phosphorylate T301 in absence of PLK activity, as that could explain the relatively low (~27%) reduction in phosphorylation by PLK inhibitor treatment.

Thank you.

Reviewer #3 (Public review):

Summary:

Here the authors investigate the role of the Trypanosoma brucei polo-like kinase TbPLK in the function of flagellum-associated cellular structures in trypanosomes. They set out to test the hypothesis that a key substrate of TbPLK is the kinesin protein KIN-G, and that TbPLK phosphorylation of KIN-G regulates its functions in cells.

Strengths:

Using in vitro biochemistry with purified proteins, the authors convincingly demonstrate that TbPLK phosphorylates KIN-G at 29 sites. Moreover, they convincingly show that phosphorylation at one site, T301, impairs the binding of purified KIN-G to purified microtubules. They further confirm that inhibition of TbPLK in cells reduces KIN-G phosphorylation at T301 (and S569). Using immunofluorescence-based imaging approaches, they also show that TbPLK colocalizes with KIN-G at centrin arms during early S-phase of the cell cycle. Centin arms are structures that are located near the basal body and flagellum and are important for new flagellum biogenesis, Golgi positioning, and cell division. To evaluate the function of KIN-G phosphorylation in cells, they depleted KIN-G by RNAi, simultaneously expressed phospho-mimetic (T301D) and phospho-ablative mutant proteins, and used immunofluorescene to examine the impact on flagellum-associated cellular structures. They show that expression of the phospho-mimetic mutant KIN-G-T301D causes the following defects: reduced cell proliferation, disruption of centrin arm and Golgi biogenesis, impairment of FAZ elongation and flagellum positioning, and misplacement of the cell division plane. The data convincingly support the conclusion that KIN-G phosphorylation on T301 plays an important role in regulating the cellular functions of this kinesin motor protein.

Weaknesses:

The authors have addressed prior weaknesses in the manuscript through additional experimentation and rewording of the conclusions.

Thank you for your critical review of our manuscript and for the very constructive comments and suggestions to improve the manuscript.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(There is some redundancy below with my comments in the public review, but I've included here for clarity and further explanation.)

The authors have addressed my primary concern, as treatment with PLK inhibitor reduces phosphorylation of T301, while also providing some comment on relative impact of PLK-mediated KIN-G phosphorylation.

It is notable that phosphorylation of T301 was reduced by only ~27%, while phosphorylation of S569 was reduced by ~100% in the presence of PLK inhibitor. The authors note that this might be explained by slower dephosphorylation of T301. In the absence of a phenotype, and with cell doubling continuing unabated in presence of the inhibitor, it is intriguing that more loss is not observed. An alternative explanation is that an alternate kinase might also be able to phosphorylate T301 in the absence of PLK activity, and the authors should consider that possibility.

We added a sentence in the main text to suggest an alternative explanation.

The model shown in figure 8 should include a dephosphorylation step, per the authors comments in the text regarding the small fraction of T301 that is phosphorylated and proposal of a phosphorylation/dephosphorylation cycle. The Fig 8 legend needs to have some commentary on the role of phosphorylation, as phosphorylation is the center point of this paper.

We have modified the model in Figure 8 to include dephosphorylation by an unknown protein phosphatase and a statement about the role of TbPLK phosphorylation on KIN-G function.

Minor comments for improving the text are:

(1) The paper overall is clearly written. However, the Discussion starts with a solid sentence, then becomes a bit diffuse in discussing a wide range of PLK activities that were not addressed in the current work. That detracts attention a bit from the central contributions of this paper.

(2) At least two places in the text state apparent contradictions.

(a) p.5 and Fig 2C. The authors say microtubule gliding speed was "...insignificantly reduced..." by the TbPLK-K70R mutant, yet they then state that motility was "interfered with". If the effect is "insignificant", why do they claim there is an effect?

(b) p6 and Fig 3C. The authors report KIN-G-T301A impact on microtubule gliding activity is insignificant, but then say this mutation reduces motility of KIN-G. These statements are contradictory.

(3) p. 8, and Fig 7. "ventral side" and "leading edge" are not defined but are used to describe the KIN-G RNAi phenotype.

(4) Fig 7B. Please explain labeling - the new flagellum daughter is indicated as having the old posterior, while the old flagellum daughter cell is indicated as having the new cell posterior. This is counterintuitive to a reader not intimately familiar with the T. brucei cell division process.

(5) Fig 4, 5, and 7: "% Cells" is reported. Please indicate what number of cells total were examined.

These minor comments have already been addressed in the previous revision.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Marconcini et al. report results of an ambitious study on the genetic mechanisms that contribute to resistance of Drosophila flies to the toxin octanoic acid (OA). This study was motivated by two observations: first, Drosophila sechellia, a close relative of D. melanogaster, has evolved specialized feeding on fruits of Morinda citrifolia, which contain high concentrations of OA and second, that artificial selection on Drosophila simulans, a sister species of D. melanogaster, can generate higher resistance to OA. Previous studies had performed genetic mapping studies between D. simulans and D. sechellia that implicated certain genomic regions in resistance to OA and, in particular, implicated several Osiris gene paralogs as contributing to resistance, though the molecular mechanisms of resistance remain unclear. In this study, Marconcini et al. performed two major experiments. First, they performed evolution-and-resequence on Drosophila simulans populations exposed to OA for 50 generations and identified candidate regions with excessive shifts in allele frequencies as candidate regions containing OA resistance genes in D. simulans. Second, they performed a CRISPR knock-out screen in a D. melanogaster cell line to identify genes that contribute to OA resistance and susceptibility.

Evolve-and-resequence yielded many candidate genomic regions with extreme allele frequency shifts, which may be regions containing OA resistance genes, or linked genes, or regions that happen to show a strong shift in all replicate populations by chance. As the authors note, detecting significant shifts in allele frequencies is a challenging problem, and the authors use two measures of allele frequency shifts (the Cochran-Mantel-Haenszel method and Bait-ER) and perform simulations under neutrality to estimate a reasonable significance threshold. I am not entirely convinced by this method of estimating significance levels, because the simulations involve assumptions that may not be met by the real populations. I would think that a permutation test would provide an assumption-free method of estimating significance levels. I have tried to think whether there is something about the design of these experiments that would preclude the use of permutation tests (which are used widely for genome-wide studies, such as QTL), but I can't think of one. Perhaps the authors are aware of a reason permutation tests would be invalid here, and if so, they should state this reason.

Significance thresholds have been estimated using a variety of approaches in the literature, including false discovery rate (FDR) control, simulations under neutral drift with predefined cut-offs, arbitrary significance thresholds, haplotype-based analyses, permutation tests, amongst other methods. Our choice was guided by a review (doi:10.1186/s13059-019-1770-8), which compared the performance of several of these approaches and found that the relatively simple assumptions underlying the Cochran–Mantel–Haenszel (CMH) test often performed as well as, or better than, more complex alternatives. As with most significance thresholds used in genome-wide analyses, the CMH threshold applied here is ultimately based on a degree of arbitrariness, although we aimed to be as stringent as possible. As a complementary method, we used Bait-ER; here the threshold used followed the recommendations provided in the original publication describing this method (doi:10.1111/jeb.14134).

One reason that permutation-based approaches may be less widely adopted than theoretical null models is the extensive linkage disequilibrium among SNPs, which results in large blocks of correlated variants that cannot be considered independent observations (and therefore not shuffled). In principle, permutations could be performed at the haplotype-block level; however, defining haplotype blocks itself requires selecting thresholds or criteria that are often user defined or based on significance cut-offs. Although several tools are available for this purpose, our experience has been that the resulting block definitions remain sensitive to these choices and therefore introduce a comparable degree of arbitrariness. In reality, there is not yet a standard method in the field that has emerged as the “best” one.

There is overlap between regions detected by the two methods, but the methods disagree for many regions. The authors state that a "majority of prominent peaks were found by both methods," but I am unclear on what "prominent" means here. It would be more helpful to be more quantitative about the extent of overlap.

To quantify the agreement between the two methods, we calculated the overlap in genomic coverage (base pairs) between CMH and Baiter candidate regions. For G25, the two methods shared 1.90 Mb of candidate regions. The overlap encompassed 65.3% of the genomic span identified by CMH and 64.1% of the span identified by Bait-ER. For G50, the methods shared 4.77 Mb of candidate regions. The overlap encompassed 63.6% of the CMH candidate span and 99.9% of the Bait-ER candidate span. We have now replaced the admittedly qualitative statement the reviewer highlighted ("majority of prominent peaks were found by both methods”) with this information.

The authors hypothesized that the response would be at similar genomic loci in all populations (line 222). It seems at least possible that epistatic interactions would lead to different combinations of alleles evolving in each population. I wonder if it would be possible to test whether there is heterogeneity in the responses across the replicate populations.

We agree that epistatic interactions could lead to different allelic combinations being favored in different replicate populations. However, both BaitER and the CMH test are designed to detect parallel evolutionary responses across replicates, which was the focus of our study. One approach for testing population-specific responses is the LRT-2 test (doi:10.1534/genetics.118.301824). We did not pursue this analysis because it would likely generate many additional candidate loci, making interpretation more challenging, while providing limited additional insight into the repeatable genomic responses that were the primary focus of this work.

The evolve-and-resequence method yielded many possible regions contributing to OA resistance in D. simulans, but perhaps too many regions to test directly or even to build sensible hypotheses about the genes involved. Thus, the authors performed a second experiment to try to narrow down the list of possible candidate genes. They performed a CRISPR knockout screen in a D. melanogaster cell line for genes that contribute to resistance or susceptibility to OA. The authors identify several limitations of this experiment, but they nonetheless identified several genes where knockouts contribute to OA susceptibility or resistance. Intersecting top hits with regions that experienced selection identified two "resistance" genes: kraken and Alkbh7. The selection hit at kraken is quite compelling, whereas the evidence at Alkbh7 is less strong because only two SNPs were marginally significant. Further functional assays, including gene knockouts in D. melanogaster and D. sechellia, provide some support for the claim that both of these genes can contribute to resistance to OA in flies.

Beyond the few issues raised above, I do not have significant questions about methodology or the results. I do think, however, that the authors should be more conservative about the implications and significance of their results. For example, on line 139, the authors claim that this intersection approach provides a "powerful paradigm to investigate ecotoxicology." I am not sure I agree that the identification of two genes that may contribute to OA resistance, after a seemingly heroic selection experiment and CRISPR screen, suggests that this method is all that powerful. It seems that most of the genes that contribute to the selection response remain unidentified.

We agree with the reviewer and have modified the sentence accordingly. While we believe that integrating the approaches discussed in this paper can provide valuable insights into the genetic basis of ecotoxicological traits, these approaches are not a panacea for traits with highly complex genetic architectures, such as OA resistance. Nevertheless, the identification of two candidate genes with some evidence of contributing to the trait represents a meaningful advance toward understanding its underlying genetic basis.

Finally, given that one motivation of this project was to identify genes that contribute to evolved resistance to OA, I am surprised that the authors did not generate CRISPR alleles of kraken and Alkbh7 in D. simulans and then use these together with the existing alleles in D. sechellia to perform reciprocal hemizygosity tests to determine if these two genes actually contribute to evolved resistance in D. sechellia. This test is simpler to perform and may be more sensitive than the allelic replacement that the authors propose (lines 446-449).

While generating null alleles for the candidate genes in D. simulans is beyond the scope of this revision, we note that we did attempt reciprocal hemizygosity tests using the mutants available in D. melanogaster. However, the resulting hybrids were recovered in low numbers, and these animals were rather weak, making them unsuitable for the severe OA exposure conditions employed in our assays. We agree that, where feasible, future studies should incorporate reciprocal hemizygosity tests, as they represent a powerful approach for validating the contribution of candidate genes to the trait of interest. We have revised the final sentence of the Results section accordingly.

Reviewer #2 (Public review):

Summary:

The authors studied the resistance against octanoic acid, a compound of the noni fruit, in D. simulans, using experimental evolution and resistance/susceptibility in D. melanogaster cells. They identified novel candidate genes and performed functional tests.

Strengths:

The idea of using experimental evolution of a non-resistant species to develop resistance is interesting, and the idea of narrowing down a large list of candidate loci by CRISPR-based gene knockout in cell culture is innovative. The reviewer also liked the (easy) follow-up experiments to validate the results.

Weaknesses:

The reviewer is not convinced of the conceptual idea behind their approach: the intersection of the two approaches implicitly assumes that null alleles (or at least compromised alleles) should be selected during experimental evolution. The reviewer considers this unlikely, and the authors made no attempt to test this implicit hypothesis in their data.

We respectfully disagree with the reviewer’s interpretation of the conceptual idea behind our approach. Our strategy did not assume that experimental evolution selects for null alleles, but rather for any type of variant that could contribute to the trait being selected for (i.e., increases in OA resistance), pointing to candidate genes contributing to the trait. Like many evolve-and-resequence experiments, this approach identified hundreds of candidate genes. This is why we took an orthogonal, genome-wide CRISPR screening approach, where loss-of-function mutations could lead to increases or decreases in OA tolerance of cultured cells. However, we stress that the naturally selected alleles – which could be gain or loss of function – may have much subtler phenotypic effects than the null alleles used for functional validation.

Along the same lines, it is not clear how to reconcile an upregulation of candidate genes in resistant flies with the knockout experiments.

We respectfully disagree that these findings are difficult to reconcile. The observed upregulation of the candidate genes in the selected, resistant D. simulans is consistent with a role in promoting OA resistance, while the knockout experiments (whether in cultured cells or in whole animals) demonstrate that loss of gene function reduces resistance. These observations are complementary: increased expression is associated with enhanced resistance, whereas complete loss of function impairs it. The knockout experiments of kraken and Alkbh7 were intended as functional validation of gene involvement and do not imply that the alleles selected during experimental evolution are loss-of-function alleles (we rather hypothesize that the selected alleles are gain-of-function through some, as yet undetermined, mechanism).

The experiments to validate the effect of candidate genes did not match the experimental evolution conditions.

This is correct. As our results suggest that the phenotype is shaped by multiple genes, such that the effect of any individual gene is likely modest compared to their combined contribution. Consequently, detecting and validating the effect of a single gene requires more stringent OA conditions than those needed to observe the overall phenotypic response over the course of several generations. In addition, the shorter-term plate assay was more practical for higher temporal resolution of the analysis of mortality in the presence of OA.

The statistical analysis suffers from some problems and an insufficient description of the analyses performed.

Although D. simulans GWAS data are available, the authors did not make an attempt to estimate the effect of selected variants in the candidate genes in the GWAS data set.

We agree that comparing the experimental evolution and GWAS results (from our previous work, doi:10.1093/g3journal/jkag032) is of considerable interest. We have now expanded the Discussion to explicitly discuss the relationship between the two datasets. Overall, the overlap between the approaches was limited, although two GWAS candidate genes, bez and CG13003, fall within genomic regions exhibiting significant CMH signals at generation 25 (but not generation 50) of the evolve-and-resequence experiment. (We note that these genes could not have been identified in our CRISPR screen, as they are not expressed in S2R+ cells). More broadly, differences between the GWAS and evolve-and-resequence results likely reflect the distinct evolutionary processes captured by each approach: GWAS maps standing phenotypic variation among isofemale lines, whereas experimental evolution tracks allele frequency changes under sustained selection. Understanding why some signals are shared whereas others are not – whether due to effect size, genetic background, epistasis, pleiotropic costs, or the contribution of initially rare variants – remain important open questions.

The reviewer would have liked to see more connection between the experimental evolution and the GWAS data. As some D. simulans genotypes have similar resistance to D. sechellia, it would have been interesting to test whether this genotype contributed to the observed resistance.

While D. simulans genotypes displayed a range of OA resistance levels, none approached D. sechellia levels of resistance (see Figure 2e from our previous work, doi:10.1093/g3journal/jkag032) (The reviewer might have conflated the data from our GWAS of D. melanogaster strain, shown in Figure 2b of that paper, where some lines of that species exhibit comparable resistance to D. sechellia under the conditions of that assay). Regardless, our experimental evolution data do not provide sufficient resolution to identify the specific favorable alleles underlying the response to selection. Instead, we detect genomic regions containing many linked variants whose frequencies change under selection. Consequently, a direct comparison between evolved genotypes and GWAS-associated genotypes is currently difficult. We note, however, that expression of the D. sechellia kraken allele in D. melanogaster did not produce a significant effect on resistance, suggesting that even the most promising candidate alleles might not have strong effects in isolation.

At several places, the authors discuss the challenge of studying a polygenic trait, but at the same time, they claim to have detected and validated candidate genes. It would be helpful if the authors could discuss why they consider that their assays could really detect the contribution of single loci to the polygenic trait. In particular, when GWAS did not detect their candidate genes.

Our results do not imply that kraken and Alkbh7 are major-effect loci or that they explain a substantial proportion of the phenotypic variation. Rather, our data indicate that these genes make measurable contributions to OA resistance, consistent with the expectation that complex traits are influenced by many loci of individually modest effect. The absence of these genes among the top GWAS candidates does not preclude their involvement, as GWAS and experimental evolution interrogate different aspects of the genetic architecture and differ in their power to detect loci of varying effect sizes and allele frequencies.

It is not clear to the reviewer why the authors did not pay more attention to the highly significant peaks emerging from the experimental evolution study. Their functional validation would have been biologically more plausible.

We agree that the significant peaks identified in the evolve-andre sequence experiment represent promising targets for future investigation. However, these peaks typically span large genomic regions containing tens to hundreds of genes, making it difficult to prioritize individual candidates based on the experimental evolution data alone. In this work, we focused our functional validation on genes independently supported by the CRISPR screen, which provided gene-level resolution. We fully acknowledge that additional causal genes are likely to reside within the selected regions and remain to be functionally characterized.

Impact:

Given the obvious challenges of functional testing of polygenic traits and the clear limitations of the interpretation of the results, the study will be helpful for future studies aiming to characterize polygenic traits. Unfortunately, the results are just another piece of controversial results regarding resistance against octanoic acid, a trait that is rather easy to evaluate.

The reviewer appears to imply that a trait being straightforward to phenotype necessarily implies that its genetic basis should also be straightforward to resolve. Many classic complex traits, such as human height, are simple to measure yet have an extraordinarily complex, highly polygenic genetic architecture. We believe that OA resistance represents a similar challenge: while the phenotype is readily assayed, differences in assay conditions, genetic backgrounds, and the contribution of many loci of individually modest effect make its genetic basis difficult to dissect. We have strived to be cautious in our conclusions, in particular the evolutionary interpretations; nevertheless, to our knowledge, this is the first study to provide functional evidence supporting the contribution of specific genes to OA resistance in D. sechellia, combining both loss-of-function phenotypes and expression data. As emphasized by the title of our manuscript, we view the principal contribution of this work as demonstrating how complementary experimental approaches (both of which are fairly novel for study of toxin susceptibility/resistance genetics) can be integrated to prioritize and functionally evaluate candidate genes underlying complex adaptive traits.

Recommendations for the authors:

Reviewing Editor Comments:

Both reviewers propose to include additional statistical and quantitative measures to strengthen the results. Furthermore, certain parts of the manuscript could be rephrased to make sure that the readers can understand more clearly the implications and significance of the results. To test whether the genes identified in the present manuscript (as contributing to octanoic acid resistance) are also involved in the evolution of the resistance, reciprocal hemizygosity tests using CRISPR alleles of kraken and Alkbh7 in D. simulans would be a plus, but such experiments are not required because the main focus of the paper is on the genetic basis of octanoic acid resistance, and not on evolution.

We thank the Reviewing Editor for these constructive comments. We have revised the manuscript to clarify the interpretation and significance of our findings and have addressed the reviewers’ comments throughout. Regarding reciprocal hemizygosity tests, we agree that they would provide a valuable means of assessing the evolutionary contribution of candidate genes. However, generating the necessary reagents in D. simulans represents a substantial undertaking beyond the scope of the present study, particularly given the expected modest effects of individual loci underlying this highly polygenic trait. We have nevertheless revised the end of the Results section to mention reciprocal hemizygosity tests as an important direction for future work.

Reviewer #2 (Recommendations for the authors):

(1) Provide more details about the selection tests: which sequences were used? Please report p-values. It would also be important to discuss the possibility of false positives caused by a bottleneck in D. sechellia. A genome-wide analysis could help to see if the bottleneck increased the signal of positive selection.

We are not entirely sure what additional analyses are being suggested. The sequences and methods used for the selection analyses are described in the Methods, and the statistical support for these analyses is reported in the Supplementary Material (MK test p-values and FUBAR posterior probabilities). We are also unclear as to how a genome-wide analysis would address the interpretation of the gene-specific selection analyses presented here. If the reviewer intended a different analysis, we would appreciate further clarification.

(2) The significance level of the CMH test needs to be determined with the effective population size, not with the census size, as done by the authors. This is important, as it is not clear if the candidate genes remain significant after significance adjustment based on the effective population size.

We thank the reviewer for this comment. In our analyses, effective population sizes were explicitly incorporated by Bait-ER to model the effects of genetic drift. The CMH significance thresholds, however, were obtained from neutral forward simulations following the recommended workflow for the method, which requires census population sizes rather than effective population sizes as input. To make these simulations as realistic as possible, we therefore used the observed census population sizes at each generation of the experimental evolution. Estimating generation-specific effective population sizes for use in an alternative simulation framework would require substantially more temporal data than are available here (e.g., sequencing many additional time points) and is beyond the scope of the present study.

(3) Include the allele frequency trajectory across time for the candidate genes.

We thank the reviewer for this suggestion. However, plotting allele frequency trajectories for the candidate genes is not straightforward because the evolve-and-resequence analysis identified broad linked genomic regions rather than individual causal variants. Each candidate region contains numerous SNPs spanning several kilobases, with each SNP exhibiting its own allele frequency trajectory across the 10 replicate populations. Consequently, there is no single representative trajectory for a given candidate gene, and plotting all SNPs within each region would be difficult to interpret. For kraken, however, we identified seven candidate regulatory SNPs and have plotted their individual allele frequency trajectories, which we include in Author response image 1 to illustrate the diverse patterns observed:

Author response image 1.

(4) Estimate the effect of candidate loci in the GWAS data (independent of significance).

We thank the reviewer for this suggestion. However, we are not entirely sure what analysis is being proposed. In particular, it is unclear which variants the reviewer is referring to, as our candidate genes are associated with multiple linked variants rather than a single causal SNP. Consequently, we are unsure how the effect of a candidate locus should be estimated in the GWAS dataset. Moreover, there is no guarantee that the same variants are represented in both datasets. For example, variants filtered out during the GWAS because of low allele frequency may subsequently have increased in frequency during experimental evolution and therefore contributed to the evolve-and-resequence signals. We would appreciate further clarification of the analysis the reviewer has in mind.

(5) Discuss the challenge of false positives (see: 10.1016/j.cub.2020.12.023).

We thank the reviewer for this suggestion. We agree that false positives (as well as false negatives) are an important consideration when studying complex polygenic traits, both through the initial “screening” efforts (e.g., GWAS, experimental evolution) and follow-up functional validation (e.g., RNAi, mutant, overexpression analyses). We believe this issue is already addressed in the manuscript through our discussion of the limitations of the individual approaches, the polygenic nature of OA resistance, and our cautious interpretation of the functional validation results. Our conclusions are limited to identifying candidate genes that contribute to OA resistance, rather than claiming to have identified all of the loci or variants underlying the evolution of this trait. We are therefore not sure what additional discussion the reviewer has in mind and would appreciate further clarification if a specific point from the cited study is intended.

(6) The figures with the Manhattan plots should be improved to indicate the overlapping genes in the Manhattan plots, rather than in the circle figures below. By using different colors this should be quite easy and clean.

We thank the reviewer for this suggestion. However, we believe Author response image 2 more appropriately illustrate the overlap between the CMH and BaitER analyses. Although the Manhattan plots display individual SNPs, our candidate loci are defined by broader genomic regions comprising blocks of linked significant SNPs rather than by single variants. Simply highlighting SNPs within overlapping regions would therefore add visual complexity without providing additional biological insight beyond that already captured by the circos plots. As an illustration, we provide here an example of the generation 50 Manhattan plot with overlapping SNPs highlighted in red:

Author response image 2.

(7) A more focused discussion of the assumption that functional data from D. melanogaster can explain resistance in D. simulans or D. sechellia. At some places, epistatic interactions are mentioned, but the reviewer feels that the entire screen is based on the idea that similar effects are found across species, hence, this needs to be adequately reflected in the discussion.

We thank the reviewer for raising this important point. We would like to emphasize that our study was not based on the assumption that functional effects identified in D. melanogaster or D. simulans necessarily explain the evolution of OA resistance in D. sechellia. Rather, our motivation stemmed from the longstanding difficulty of identifying individual genes underlying this highly polygenic trait using mapping approaches alone. We therefore sought to combine orthogonal experimental approaches to identify genes contributing to OA susceptibility (of D. melanogaster and D. simulans) and resistance (D. sechellia). We hoped, but did not assume, that genes supported by multiple independent lines of evidence would be informative for understanding the natural evolution of OA resistance in D. sechellia. Indeed, we acknowledge in the manuscript that the cell-based CRISPR screen, experimental evolution, and the natural evolution of D. sechellia occurred under very different selective contexts and timescales. As reflected in the title of our manuscript, our conclusions are intentionally framed around the identification of novel toxin resistance loci, while remaining cautious about their evolutionary interpretation.

(8) Discuss that the controls in the RNAi test were quite variable. Could this reflect some problems with the assay?

We do not believe that the variability among the control lines reflects a problem with the assay. Rather, the different controls (Gal4, UAS-RNAi etc.) represent distinct genetic backgrounds, each of which may exhibit a different baseline level of OA resistance. Indeed, in our recent GWAS of OA resistance (doi:10.1093/g3journal/jkag032), we observed substantial natural variation in OA resistance among D. melanogaster and D. simulans lines. Importantly, each RNAi line was compared with its corresponding genetic background control, so differences among control lines do not affect the interpretation of the individual RNAi experiments.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study examines Müller glia (MG) reprogramming in the uninjured mouse retina through a combination of Notch signaling inhibition and AAV-induced proliferation. Building on their prior work showing that Cyclin D1 overexpression and p27^Kip1^ knockdown (CCA) promotes MG proliferation with very limited neurogenesis, the authors now demonstrate that Rbpj deletion alone induces a modest degree of MG-to-neuron conversion without proliferation, in agreement with recent work in the field. However, combining Rbpj deletion with CCA-mediated proliferation substantially enhances MG dedifferentiation and the generation of retinal neuron-like cells. Through genetic lineage tracing, histological analyses, and single-cell transcriptomics, the authors provide evidence that MG-derived cells acquire molecular features of bipolar (ON, OFF, and rod bipolar) and amacrine neurons. Most MG-derived cells appear to survive long-term (up to 9 months).

Strengths:

Overall, the study is carefully designed and executed, and the manuscript is clearly written with well-presented figures. While the work does not significantly expand the repertoire of neuronal types generated from mammalian MG beyond what has been previously reported in the field, it provides a valuable and improved strategy for inducing robust MG proliferation and neurogenesis in the mammalian retina.

Weaknesses:

(1) It would be better to include a negative control AAV when evaluating the effect of CCA AAV in the Rbpj KO background. This could help distinguish the specific contribution of the CCA construct from potential effects of intravitreal AAV injection itself, which can induce mild inflammation, known to influence MG reprogramming.

To address this concern, in the revised manuscript we included the result from Rbpj KO eyes injected with a negative control AAV (AAV_7m8-GFAP-GFP) (Fig. S14a). MG reprogramming efficiency, quantified as the proportion of tdT⁺Otx2⁺ cells among total tdT⁺ cells, was then compared between the AAV-GFP–treated and Rbpj KO–only eyes. At 4 months post-injection, the percentage of tdT⁺Otx2⁺ cells in the AAV-GFP–treated eyes was comparable to that of Rbpj KO alone (Fig. S14b–c), and substantially lower than in the CCA-treated eyes. Together, these results indicate that the enhanced MG reprogramming observed in the Rbpj KO+CCA group is driven by transgenes expressed rather than by nonspecific effects of AAV or injection.

(2) The extent of MG transduction by the CCA AAV is not clear. As quantifications are normalized to total MG (GFP^+^ or TdTomato^+^) or retinal length, it would be useful to clarify whether near-complete transduction is assumed, or if additional information on transduction efficiency can be provided.

In our previous study (Wu, Liao, et al., 2025, eLife), we have demonstrated that high-dose (4E10vg/injection) AAV7m8 effectively transduced the whole retina, with near-complete MG transduction observed in the vicinity of the injection site, as evidenced by virtually all MG expressing GFP in these regions. In the revised manuscript, we clarified the transduction efficiency in Line 108-110 on Page 5 and Line 625-626 on Page 27.

(3) In Figure S10, the reduced MG proliferation observed in the CCA + Rbpj deletion group could also potentially reflect decreased GFAP promoter activity in dedifferentiated MG following Rbpj deletion. Alternatively, MG-derived cells may be more fragile under these conditions.

We thank the reviewer for these excellent insights. We agree that a down-regulation of GFAP promoter activity following Rbpj-mediated dedifferentiation is a highly plausible explanation for the moderate reduction in proliferation, as lower promoter activity would diminish AAV transgene expression. We have included this possibility in the data interpretation (Line 176-178, page 8). Regarding the alternative possibility of increased cell fragility, we agree that cell death cannot be ruled out, but occasional apoptotic cells over a long period of time are difficult to capture experimentally.

(4) In the CCA + Rbpj deletion condition, do MG undergo single or multiple rounds of cell division?

We have previously demonstrated that MG typically undergo a single round of cell division in wild type mouse retina following CCA treatment (Wu, Liao, et al., 2025, eLife). Given our observation that Rbpj deletion suppresses CCA-induced MG proliferation (Fig. S11), it is unlikely that the addition of Rbpj deletion would trigger multiple or continuous rounds of cell division beyond the single-round baseline established by CCA alone. While we did not re-evaluate cell division kinetics in the current study, we reason that CCA similarly drives MG to undergo a single round of division in the Rbpj KO context.

(5) What fraction of neuron-like cells (bipolar- and amacrine-like) arises from proliferation versus direct transdifferentiation? Quantification of MG-derived cells expressing neuronal markers (e.g., Otx2, HuC/D), with and without EdU labeling, would help distinguish these mechanisms.

The percentages of MG-derived cells expressing neuronal markers with and without EdU labeling, were shown in Fig 3d-e and Fig S19d-e. In the Rbpj KO-only group, neuron-like cells arise exclusively through direct transdifferentiation without cell division, as no EdU incorporation was detected in Rbpj-deficient MG. In this group, a small fraction of MG-derived cells expressed the neuronal marker Otx2 or HuC/D (Fig 3e, Fig S19e). In contrast, the Rbpj KO+CCA group achieved a substantially higher neurogenesis rate, with a significant proportion of Otx2+ or HuC/D+ MG-derived cells also being EdU+ (Fig. 3d, Fig. S19d), indicating that they arose through de novo neurogenesis. By subtracting the contribution of direct transdifferentiation observed in the Rbpj KO-only group, we estimate that majority of MG-derived neuron-like cells in the Rbpj KO+CCA group were generated through proliferation-mediated de novo neurogenesis.

(6) In Figure S18a, the authors state that "while the neuron-like clusters were best classified as BC-like and AC-like based on their distinct marker gene expression, they also exhibited mixed expression of genes associated with other retinal neuronal types, including RGC markers (e.g., Tubb3, Myt1l, Grin1) and photoreceptor markers (e.g., Crx, Prom1, Epha10, Gucy2e, Scg3) (Fig. S18a), suggesting that the regenerated cells exist in a hybrid state" and "MG derived neuron like cells also expressed genes characteristic of RGCs and photoreceptors, indicating enhanced lineage". However, many of these genes are not specific to RGCs or photoreceptors and are instead broadly expressed in retinal neurons or enriched in bipolar/amacrine populations. Therefore, it is unclear whether these cells exhibit hybrid RGC or photoreceptor identity.

We thank the reviewer for this insightful comment and for pointing out the need for greater precision in our terminology regarding these markers. While individual markers may lack absolute, 100% cell-type exclusivity, genes such as Tubb3 and Gucy2e serve as widely accepted lineage-associated genes that characterize RGC and photoreceptor programs, respectively (Soto et al., 2008; Sato et al., 2018; Sotani et al., 2024). We have revised the manuscript to replace terms "RGC-specific genes" and "photoreceptor-specific genes" with "RGC signature genes" and "photoreceptor signature genes", respectively. Furthermore, these RGC- and photoreceptor-signature genes are co-expressed across the entire Otx2+ MG population rather than being segregated into distinct, specialized subpopulations (Fig. 4d, Fig. S20). This uniform distribution indicates that these cells possess a hybrid transcriptional program that concurrently incorporates elements of both RGC and photoreceptor identities.

(7) The authors provide a thorough molecular characterization of MG-derived cells through immunostaining and single-cell sequencing. However, their morphological features, synaptic connectivity (e.g., synaptic marker expression), and electrophysiological properties remain largely uncharacterized. While these experiments may be technically challenging, this limitation should be discussed.

We agree with the reviewer that characterizing the precise morphological features, synaptic connectivity, and electrophysiological properties of MG-derived cells is a crucial step for any neuronal regeneration study, and we acknowledge that this represents an important limitation of our current study.

As demonstrated by snRNA-seq data, the MG-derived neuron-like cells exhibit an incompletely mature state, characterized by hybrid transcriptomic signatures. By immunostaining, we did not observe any MG-derived cells with photoreceptor outer segment or typical RGC morphology. Therefore, it is highly likely that these cells have not established functional synaptic connectivity or acquired mature electrophysiological properties. Performing functional or circuitry assessments at this stage would be premature.

We have added a comprehensive discussion regarding this limitation, along with future directions for long-term functional validation, in the revised manuscript (Line 502-515 on Page 22).

(8) The conclusion that CCA + Rbpj deletion induces neurogenesis without compromising MG supportive functions or retinal homeostasis appears somewhat oversold. This claim is primarily based on gross retinal morphology and ZO-1 staining. Given the extent of MG dedifferentiation and ectopic cell generation in the ONL and INL, it is likely that retinal function is affected. Functional assessments (e.g., ERG) would be required to support this conclusion. The authors should consider tempering this statement.

To address the concern raised by the reviewer, we performed electroretinography (ERG) to evaluate both scotopic and photopic retinal function in the Rbpj KO+CCA-treated eyes compared to contralateral untreated controls (Supplementary figure S23e-h). In addition, we conducted optomotor response testing to assess whether visual behavior is affected following treatment (Supplementary Figure S23d). The results demonstrate that combined Rbpj KO and CCA treatment achieves neurogenesis without compromising retinal function.

(9) Regarding the mechanism by which CCA-induced proliferation enhances MG reprogramming in the Rbpj knockout background, one plausible explanation is that chromatin states (e.g., histone modifications and DNA methylation) are transiently reset during DNA replication and cell division. While this alone may be insufficient to activate neurogenic programs, it could synergize with Rbpj deletion to allow neurogenic transcription factors (such as Ascl1, Otx2, NeuroD1, and NeuroD2) to access previously inaccessible chromatin regions, thereby promoting MG reprogramming.

We thank the reviewer for the insightful suggestion on the model, which aligns well with our experimental findings. Our snATAC-seq data demonstrate that CCA-induced proliferation broadly increases chromatin accessibility at key neurogenic loci, including Neurod2, Dll1, and Otx2, in active MG compared to resting MG (Figure 6f–h). This chromatin remodeling alone is insufficient to drive neurogenesis, as CCA-only treated MG largely revert to a quiescent glial state. However, when combined with Rbpj deletion, which derepresses downstream neurogenic transcription factors such as Ascl1 and Neurog2 by relieving Notch-mediated transcriptional repression, these newly accessible chromatin regions can be effectively occupied and activated by the available neurogenic factors. The concept that cell division facilitates epigenetic resetting to enhance reprogramming efficiency is well established in the somatic cell reprogramming field, where proliferation rate is directly proportional to reprogramming success by promoting the erasure of lineage-restrictive epigenetic marks and the re-establishment of new transcriptional circuits. In the revised manuscript, we incorporated this mechanistic discussion to provide a more comprehensive interpretation of how proliferation and Notch inhibition converge to promote MG neurogenesis in Line 462-477 on Page 20-21.

Reviewer #2 (Public review):

Summary:

The inability of the mammalian retina to regenerate poses a major clinical challenge. Much has been learned about the regenerative potential of the retina from teleost fish, where Müller glia (MG) are able to proliferate and produce new neurons after injury. However, MG do not retain this potential in the mammalian retina. The authors showed previously that forcing MG to re-enter the cell cycle by downregulating p27 and upregulating cyclin D1 could induce MG to dedifferentiate, but the results were transient, and these cells eventually reverted back to MG and did not form neurons. Here, they expand on this to show that in MG, coupling forced cell cycle re-entry with deletion of Rbpj, which inhibits the transcriptional effects of Notch signaling, induces some MG to proliferate and take on features of multiple cell types, including MG precursor cells, amacrine-like cells, and bipolar-like cells. This work lends valuable insight into the regenerative potential of mammalian MG, particularly when Notch signaling is manipulated.

Strengths:

The major claims of the authors are well-supported. They show convincingly - and through multiple methods including immunostaining, single-nucleus RNA sequencing, and in situ hybridization - that coupling notch inhibition with cell cycle reactivation induces the expression of neuronal markers in mammalian MG. The snRNA-seq data are particularly valuable in demonstrating the induction of bipolar-cell subtypes. Edu labeling is effective in demonstrating the induction of proliferation, and the long-term viability of the generated neuron-like cells is intriguing.

Weaknesses:

Whether the newly generated neurons are functionally integrated remains unclear, and the effect of the manipulation on the function of the retina was not tested. Imaging data suggests that many of the newly generated neurons persist for months, but often appear mislocalized. It is also not clear if the manipulation of MG affects long-term MG function. Cell death was not evaluated, and although the authors evaluated the long-term effect on tight junctions, this data was not quantified, and further analysis on morphology or function was not done. Control eyes were untreated, not vehicle-injected.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The transgenic line may be Glast-CreERT, not Glast-CreERT2.

We appreciate the reviewer for bringing this to our attention. The formal allele symbol for this transgenic line is Tg(Slc1a3-cre/ERT)1Nat, while this strain is generically classified as "Cre/ERT2" by the Jackson Laboratory. Some published studies referred to this line as Glast-CreERT and others as Glast-CreERT2. To maintain consistency with the formal allele symbol, we have adopted "Glast-CreERT" throughout the revised manuscript.

(2) For snATAC data in Figure 6 e,f, and Figure 19b. It is most likely gene activity, not gene expression, since these are snATAC, not snRNA data.

For this inaccurate terminology, we have corrected all relevant figure labels and associated text in the revised manuscript to clearly state "gene activity" instead of "gene expression."

(3) Some text in Figure 6 is a bit too small to read.

We have increased the font size of the text elements in Figure 6 to ensure readability and have also reviewed all other figures for consistency. Revised figures with improved legibility have been included in the updated manuscript.

Reviewer #2 (Recommendations for the authors):

(1) There are multiple instances where further elaboration of methods or tools in the test would improve readability and comprehension by a broader audience. It would be helpful to (early, often, and clearly) explain precisely which cell types are labeled in your mouse line and how. Someone unfamiliar with the mouse line may struggle to understand what is labeled by the tdT or GFP. Likewise, it would help to consistently define what cell types are labeled by tdT+ vs. Sox9+, tdT+, etc.

We have added a clear and detailed description of the mouse lines and labeling strategy early in the Results section, specifying which cell types are labeled by tdT and GFP and how the labeling is achieved. We have also ensured that the definitions of cell type identifiers (e.g., tdT⁺ for MG-derived cells, Sox9⁺/tdT⁺ for MG remaining in a glial state) are consistently stated upon first use and maintained throughout the manuscript to improve readability for a broader audience. In addition, we added headings for the quantification graphs to improve readability in all quantification figures.

(2) It is unclear what the difference is between Figure 1c and S1c, and these should be quantified as the % of positive cells, as described in the text.

We have removed Figure S1c and moved Figure 1c to supplementary figure 1. The MG labeled by EdU and Sox9 or Otx2 were quantified as % of the EdU+ MG.

(3) S2e: Clarify what pixel level means, is this pixel intensity?

Yes, "pixel level" in Figure S2e refers to pixel intensity. We apologize for the ambiguous wording and replaced "pixel level" with "pixel intensity" in the revised figure legend to ensure clarity.

(4) Figure 2: In the magnified image of the GFP+, Sox9- cell, the GFP is also very faint. Could these cells be dying? Analysis of the expression profile of these cells (or ruling out apoptosis) would better support a dedifferentiation argument.

The faint GFP signal observed in GFP⁺ Sox9^- cells is a sign of ongoing dedifferentiation rather than cell death. This is likely due to chromatin remodeling during reprogramming. A similar decrease in reporter signal intensity during MG dedifferentiation has been previously reported by Le et al. 2024, 2025, supporting the interpretation that reduced fluorescence is a characteristic feature of this process. It is possible that a small fraction of GFP⁺ Sox9^- cells may undergo cell death over an extended period, which would be difficult to detect using apoptosis assays. Our long-term survival experiments demonstrate that more than 80% of MG-derived neuron-like cells survive for at least 9 months following treatment (Figure 7), indicating that majority of these cells are viable. The discussion is included in line 112-114 on page 5.

(5) Figure 3: The Crx labeling appears everywhere except the identified cell. This seems the opposite of the point you are making.

Crx signal of the MG-derived cell (tdT⁺ Crx⁺), which is pointed out by arrowhead, is in a ring-like pattern. This pattern is consistent with the euchromatin region in inverted nucleus of rod. Crx labeling appears in other cells in the image as Crx is highly expressed in native photoreceptors.

(6) I think it would be nice to address, in the discussion, the apparent disorganization and mislocalization of cells in the long-term images.

We thank the reviewer for highlighting this critical observation. During retinal development, precise laminar positioning of neurons is guided by a coordinated interplay of cell-intrinsic transcriptional programs and extrinsic cues including cell adhesion molecules, guidance factors, and interactions with neighboring cells. In the adult retina, many of these developmental cues are no longer present or active, which likely contributes to the failure of MG-derived neurons to migrate to their appropriate laminar positions. Interestingly, the vast majority of our divided MG cells remained localized within the outer nuclear layer (ONL). Because the ONL is the physiological location of photoreceptors, this preferential position could serve as an advantageous baseline layout for driving targeted photoreceptor differentiation in future work. To address reviewer’s feedback, we have expanded our discussion section (Line 543-559, page 23-34) to cover the mechanisms underlying this structural disorganization and its downstream implications for functional circuit integration.

(7) I'm not convinced that ZO1 alone is sufficient to suggest MG function normally or that retinal homeostasis is maintained. I suggest tempering that conclusion in the text.

For the revision, we have performed additional experiments to address this concern. The optical coherence tomography (OCT) images revealed that retinal layer organization and ONL thickness were comparable among the uninjected eyes, GFP AAV-injected control eyes, and CCA-treated eyes, demonstrating that overall retinal architecture was well-preserved (Fig. S23a–c). Optomotor response testing revealed no significant differences in visual acuity across groups, suggesting that visual function remained intact (Fig. S23d). Furthermore, electroretinography (ERG) demonstrated that scotopic and photopic a- and b-wave amplitudes were unaffected by the treatment, confirming that light responses from photoreceptor and inner retinal neuron were preserved (Fig. S23e–h). Taken together, these findings demonstrate that combined Rbpj KO and CCA treatment achieves neurogenesis without compromising retinal structure and functional visual circuitry.

Author response:

The authors thank the reviewers for their thorough and fair assessment of our manuscript. We are currently working to edit the manuscript based on the critiques and guidance offered by the reviewers. This will consist of fixing grammar and typos, expanding the material and methods section to include more information on the behavioral assays, modifying graphs for clarity between visuals and interpretations, and correcting our mistakes in neuroanatomical labeling.

Public Reviews:

Reviewer #1 (Public review):

In their submitted manuscript, Harkinish-Murray and colleagues from the Kozol lab present convincing evidence for a genetically encoded shift in the odor perception of cavefish compared to their surface ancestors. Surface Astyanax, just as zebrafish, are attracted to food odors and are repelled by death odors and the alarm substance Schreckstoff (released from damaged skin by specialized club cells). Based on the experimental evidence in this manuscript, however, their cavefish counterparts are attracted to these odors as well. This would make sense, in an evolutionary framework, as predation is less likely in cave settings and decaying fish are a valuable source of nutrients for their living counterparts.

Using an F2 hybrid cross scheme between surface fish and cavefish, authors also provide compelling evidence that genetic factors are behind this behavioral shift. Furthermore, they also show that this behavior (i.e., attraction to skin and decay extracts) can be observed in surface fish given long enough food deprivation. This latter observation also makes sense in the light of evolution and is genuinely interesting as it also provides a plausible roadmap to the shift in behavior through Waddingtonian genetic assimilation.

The manuscript is generally well written and clear, we have identified only few weaknesses, some regarding the presentation of the data.

(1) For Figure 3, on the x-axis of panels b, e, and h, supposedly we see surface fish vs. different cavefish populations. This is currently missing and makes the figure harder to interpret. Also, two populations (panel e) show a bimodal distribution upon indirect white light exposure, suggesting that some fish still acted as if they were exposed to direct light, while others acted as if they were in darkness (infrared light). We believe this warrants more consideration as it could tell us something about the existing (and relevant) genetic variance within this population. It is also notable that the third cavefish population also showed increased odor indices under indirect white light and infrared light conditions, suggesting that increasing the number of observations could have yielded a statistically significant result.

We agree with the reviewer that our light testing data suggests complexity in the response to indirect white light within certain cave populations. In addition, an expanded sample size would likely provide clarity on whether individuals fall within two groups, behavior that looks like direct light or infra-red light, that could relate to genetic variation within cavefish populations. We are currently working to reassess the current data and determining the best course of action for continued studies related to light exposure.

(2) Some extra details about the methods could also be provided to enhance the reproducibility of the experiments.

We agree with both reviewers that the methodological section on behavior needs to be expanded. We are currently editing our methods section to include more detail on water exchanges, odor preparation, timing, biological replicates, and binning.

(3) A more serious concern is about the anatomical designation of particular brain regions in Figure 7d and consequently Figure 7f. Whereas we would agree with the positioning of the medial pallium (Dm), we think the region depicting the thalamus is in fact still part of the telencephalon, and the real thalamus should be more posteriorly. On the other hand, we think that the preoptic areas should be under the pallium and not posterior to it (see PMID: 22586363 for corresponding zebrafish anatomy). We would suggest, therefore, that the authors revisit this issue (a minor one, considering the depth of the results presented in the manuscript), and provide a better anatomical annotation - e.g., the identity of particular brain regions could be backed up by Hybridization Chain Reaction experiments for region-specific transcripts. (Disclaimer: we do not consider ourselves experts in adult cavefish neuroanatomy; therefore, we consulted in this case a colleague with much more knowledge on this topic.)

We agree that our annotation was incorrect or more accurately mislabeled in our write-up of the preprint and submitted manuscript. Therefore, we have now re-assessed the regions using the tissue cleared and light sheet collected zebrafish atlas, Adult Zebrafish Brain Atlas (AZBA; doi: 10.7554/eLife.69988). We are now editing the resubmission in the following manner: our initial labeling of the ventromedial thalamus will be changed to the lateral olfactory tract (nLOT) of the pallium and the preoptic region to the ventromedial thalamus (VM). We will provide a comparable z-slice of the AZBA segmentation file to illustrate the similarity in position. This would also support a known continuous circuit of olfactory integration, with information flowing from the lateral olfactory tract-to the piriform cortex-to the thalamus. We also agree that a more accurate assessment in Astyanax would require HCR in situ hybridization of markers for those specific brain regions or a neurocomputational brain atlas for adult Astyanax populations. Finally, we assert that this small dataset is preliminary at best and only provides regions of shared activity that could explain anything from perception related processes to relay of odor signaling unrelated to perception. Further work with larger sample sizes and additional populations are currently underway for a follow-up study on the neurobiological basis of olfactory processing and perception in adult cavefish.

(4) It would also be useful to expand the brain imaging data displaying results for similar tests in surface fish, to see if skin and decay extracts trigger different or similar brain activity in those fish.

We agree with the reviewer that the brain mapping section lacks a sufficient sample size and no control group for comparison (surface fish). However, we found the variation in pERK intensity (notably the putative nLOT) to be informative and decided to include the dataset in the manuscript. We are currently working to fill in these data gaps by sampling all populations and increasing the Pachon cavefish sample size. This will be a follow-up study as mentioned above in the last rebuttal paragraph.

Further work will surely be able to discern the more precise genetic changes that made the shift in behavior possible. Once these causative variants (or at least linked markers) are determined, it will be quite revealing to see if these variants are indeed already present in the surface population (as hinted by the authors), and also, if besides the Surface x Tinaja F2 hybrids, crosses between other cave populations and surface fish can be performed, we could also see how much evolutionary convergence happened in the parallel evolution of different cave morphs. Were there multiple possible pathways for similar behaviors in different cave populations, or - as in freshwater stickleback populations - do we see broadly the same genetic playbook repeated each time?

We agree with the reviewer that the hybrid results setup a promising follow up project to map these traits genetically. We are continuing to test odor perception in other hybrid populations and have started Quantitative Trait Locus mapping experiments.

Another outstanding question, also demonstrated and discussed, albeit briefly, in this paper relates to the behavior-modulating effect of light in cavefish. What is the physiological relevance for a dark-dwelling animal to have this capacity? Is this just the chance result of occasional gene flow from surface populations, or does it have a genuine evolutionary significance?

Reviewer #2 (Public review):

Summary:

The authors tested whether the olfactory cues that drive attraction or avoidance behavior have diverged between surface‑dwelling and cave‑adapted strains of the Mexican cavefish Astyanax mexicanus. They use high‑throughput odor‑discrimination assays between known attractants and repellents by calculating an "odor index" per fish (=the difference in time spent in an odor zone versus a control zone). Further, hybrid crosses to probe heritability, starvation experiments to assess plasticity of odor perception, and whole‑brain pERK detection/mapping to link behavioral changes with known localized neural activity. The results support the hypothesis that the extreme cave environment has selected for an approach response to stimuli that are ancestrally aversive (like alarm or death odors) but in harsh environments can be used as guidance to the rare food sources in this ecosystem.

Strengths:

The odor index analysis is convincing, and the experiments for odor attraction/avoidance are robustly performed. The light-to-darkness shift reflected by avoidance to attraction in cavefish towards skin odors is compelling and carefully analyzed. The analysis of odor indices of three cave-dwelling populations in comparison to surface fish highlights a similar regime, yet with differences among the different populations, suggesting population-specific genetic variation.

Another strength of the paper is exactly this genetic inheritance study by generating F2 hybrids of cave-dwelling and surface-living individuals. The hybrids displayed a continuous range of odor indices for social, alarm, and death odors, indicating that these traits are heritable and likely based on additive genetic markers. Further, the authors uncovered a sexual dimorphism: only female cavefish exhibited approach behavior to social odors, whereas males remained neutral. This result aligns with known differences in olfactory organ morphology between sexes of other species from harsh environments.

Although limited in number, the neurophysiological correlation using whole‑brain pERK mapping after 10 min of odor exposure is convincing. The data revealed overlapping activation in the thalamus and pre‑optic region for food and decay odors, suggesting that these brain areas mediate the evolved attraction response to previously repellent stimuli.

Overall, the manuscript presents a concise story: cavefish have evolved attraction to alarm and death odors as a result of shifting from ancestral avoidance-driven to attraction by genetic changes and physiologically similar activation of specific neural circuits. The evidence is robust, with multiple independent experiments (behavioral assays, hybrid genetics, starvation experiments, and brain mapping) that collectively support the conclusions.

Furthermore, exposure to unpleasant odors can not only be tolerated but can even serve as a trigger for foraging. This plasticity demonstrates that genetic predispositions can be put into practice through active changes in physiology in species or organisms confronted with (drastically) changing environmental conditions.

Weaknesses:

I value that the authors are critical of their own data, indicating low numbers in the pERK/brain experiments. Yet this is a weak point as the statistical power is thus limited. However, their reasoning is careful, based on the results and not over-interpreting.

We agree with the reviewer and direct their attention to the same critique by reviewer 1. We believe this is predominantly preliminary data that was included due to the conspicuous increase in pERK signal from the putative lateral olfactory tract (nLOT) for food and decay exposed cavefish. We are continuing to work on odor stimulated brain mapping and look forward to publishing a comprehensive dataset across wildtype and hybrid populations.

The layout/design of the ethograms (bout category plots) for both individual and population-wise are not easy to follow. Reworking these display items to convey the information is necessary.

We agree with the reviewer that the ethograms are challenging to read, especially due to our use of different colors for odor categories. We are currently preparing alternative graphs for displaying ethograms that reduce confusion and make following bout transitions for individual traces and bout probabilities for populations easier on the eyes.

Taken together, the manuscript uses odor perception and attraction/avoidance behavior studies to show that environmental changes (light-to-darkness) have an immediate impact on smell perception and behavior. Attraction to otherwise repellent odors is used by cavefish to likely adapt to harsh environments with low food sources. The manuscript convincingly demonstrates this plasticity, which is an interesting idea to follow up for other traits spreading among a population. This also underlines that a genome may be fixed and the blueprint for behavioral traits, but extrinsic cues can readily be adapted to change wired behavior even to the extreme as reported here: changing avoidance to attraction.

Author response:

We thank the editors and reviewers for their thoughtful evaluation and constructive feedback. We are pleased that all three reviewers recognize the importance of mapping Cas9-induced sister chromatid exchanges (SCE) as a previously invisible repair outcome, and that the RDCP analysis is a notable feature of the study.

We note that since our manuscript was posted, two companion studies in Science have provided direct biochemical evidence for the TRAIP-dependent pathway we discussed:

(1) Fujisawa & Labib (Science, 2026; DOI: 10.1126/science.aeh2300) showed that TTF2 bridges CDK1-phosphorylated TRAIP to DNA Polymerase epsilon in the replisome, triggering mitotic CMG helicase disassembly, fork cleavage, and repair via SCE. Loss of this pathway reduced replication stress-induced SCE approximately two-fold in mouse ES cells.

(2) Can et al. (Science, 2026; DOI: 10.1126/science.aeh1834) independently identified the same CDK1-TTF2-TRAIP axis in Xenopus egg extracts and validated it in HCT116 cells, showing that disrupting the TRAIP-TTF2 interaction reduced common fragile site deletions.

We will incorporate these references in the revised discussion while still framing our RDCP observations as consistent with, rather than definitive proof of, this pathway.

Below we briefly address the main points raised in the public reviews.

Reviewer #1:

We agree that the mechanistic interpretation of the RDCP signature should be presented more cautiously. We will reframe the URR/TRAIP discussion as a model, replacing language such as "direct genetic evidence" with "consistent with." We will add a summary table of RDCP data. We will also expand the description of rescued SCE calls. We will clarify what the DNA repair gene targeting experiment can and cannot answer (delayed protein loss, essential-gene selection) - we think that there is a notable difference at the bulk vs. at the single-cell level depending on the nature of the assay. Fig.1 fonts, labels, and pileup plot descriptions will be improved.

We agree that the high-SCE subpopulation is particularly interesting and we cannot currently distinguish higher RNP uptake, a permissive cell-cycle state, altered expression, or stochastic variation. This may be better explored by future co-assays with sci-L3-Strand-seq.

Reviewer #2:

We agree with the limitations that Cas9-induced DSBs can be dependent on the cell cycle stage and the number of times cuts are made. We will add a brief discussion on this limitation in extrapolating the mechanisms of DNA instability and DNA repair from the observed genomic rearrangements.

We agree that "a single Cas9 cut" should be revised to "Cas9 targeting of a single genomic locus" to accurately reflect the experimental design. We will clarify the possibility of multiple rounds of cutting at the same sites. We will also clarify "non-local" by modifying Fig.1 - we used this term specifically to include the possibility of inter-sister NHEJ.

Reviewer #3:

We will improve the self-contained nature of the manuscript so that readers need not consult the earlier NAR papers, and the companion preprint to understand the key results.

Joint Public Review

Summary:

In this study, the authors investigated the developmental and molecular basis of the unusual metamorphic program of the black soldier fly, Hermetia illucens, which differs from the canonical holometabolous life cycle by inserting a distinct, non-feeding prepupal instar between the final larval stage and pupation. Most insects that undergo complete metamorphosis molt to the final instar and then develop into the prepupal stage without molting. H. illucens, however, undergoes a molt before entering a non-feeding prepupal stage. Thus, it is an unusual, novel developmental strategy, and its regulation has remained a mystery. Through an integrated approach combining detailed morphological characterization, developmental gene expression profiling, and RNAi-mediated functional analyses of the core components of the Metamorphic Gene Network (MGN), the authors examine the developmental identity of this prepupal stage and how the temporal deployment of conserved metamorphic regulators has been reorganized to accommodate this atypical developmental program. In particular, they show that the prepupal stage expresses a distinct combination of the key genes known to regulate life history transitions, including unusually high levels of Br-C expression.

Strengths:

The study represents a valuable contribution to insect developmental biology. A major strength is the comprehensive characterization of postembryonic development, which establishes a robust developmental framework for H. illucens. This is complemented by detailed expression profiling and RNAi-based functional analyses of the Metamorphic Gene Network (MGN), comprising the temporal specifier factors, Kr-h1, chinmo, Br-C, and E93. The results show that these conserved regulators are deployed in a modified temporal sequence that accommodates the distinctive prepupal stage while largely preserving their canonical developmental functions. Together, the morphological, molecular, and functional data support the conclusion that the prepupal stage of H. illucens is a distinct developmental transition associated with a characteristic configuration of the metamorphic gene network. The results are supported by solid methodology and approaches and will serve as valuable resources for future investigations into insect development, the evolution of metamorphosis, and the diversification of insect life-history strategies.

Weaknesses:

While the study successfully establishes the developmental identity of the prepupal stage and its association with a modified temporal deployment of the MGN, some aspects of the proposed regulatory model are less directly supported by the experimental evidence.

(1) Several regulatory interactions within the MGN remain inferential rather than experimentally demonstrated in H. illucens. In particular, the proposed relationship between juvenile hormone (JH), Kr-h1, and chinmo is based primarily on expression dynamics and RNAi-induced transcriptional changes. Although these observations are consistent with the proposed model, they do not directly demonstrate that JH induces chinmo expression or establish the regulatory relationship between Kr-h1 and chinmo in this species. As a result, the corresponding regulatory interactions presented in the final model should be regarded as plausible hypotheses rather than experimentally validated mechanisms.

(2) A second limitation concerns the developmental role assigned to Br-C and E93 during the larval-to-prepupal transition. The authors conclude that sustained Br-C expression is a defining molecular feature of the prepupal stage and discuss its potential role in prepupal specification. However, the functional analyses of both Br-C and E93 were initiated only after larvae had already entered the prepupal stage. Consequently, while the RNAi experiments convincingly demonstrate essential roles for Br-C during the prepupal-to-pupal transition and for E93 during adult differentiation, they do not directly address whether either factor is required to trigger the formation of the prepupal stage itself. Therefore, the molecular mechanisms governing the initiation of this distinctive developmental transition remain unresolved. In particular, the proposed lack of repression of E93 by Br-C is only weakly supported, yet may be an essential feature of the prepupal stage of Hermetia illucens.

(3) Although knockdowns of Kr-h1 and chinmo knockdowns look superficially similar, it would be good to confirm this with higher-magnification views of the cuticles for all three treatments (control, Kr-h1 RNAi, and chinmo RNAi). In other species, Kr-h1 knockdown leads to premature adult cuticle development, whereas chinmo knockdown typically leads to premature appearance of pupal characteristics. Similarly, in Fig. 4A and 4D, higher-magnification images of the cuticle would be helpful.

(4) (Relating to Line 336 and Figure 7): "This low but persistent prepupal Kr-h1 expression, together with modest chinmo expression from PPD0 to PPD8, may be correlated to a JH-dependent antimetamorphic effect that maintains the prepupal stage." However, we are not aware of a function of JH in extending the prepupal stage. In addition, in most insects, the prepupal stage expresses high Kr-h1 expression; this peak likely prevents the animal from turning into an adult instead of the pupa. We presume the same holds true for H. illucens (although the lower expression of Kr-h1 during that stage is curious). As a result, we suggest that Fig. 7D be revised as it may be difficult to distinguish between pupal formation and prepupal maintenance given the experimental set-up. Fig. 7E may also need to be modified since the development of the pupa may require Kr-h1. It is worth noting that at the prepupal stage, JH and Br-C are co-expressed in many insects. If the authors think that Kr-h1 expression needs to be low at this time, this would imply a novel interaction between Kr-h1 and Br-C, and should be discussed.

Author response:

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

Public Reviews:

Reviewer #1 (Public reviews):

Weaknesses:

Reliance on self-reports

A primary limitation of this study, acknowledged by the authors, is its reliance on self-reports of participants’ emotional states. Although considerable effort was made to minimize expectation effects, further research is needed to confirm that the observed behavioral changes reflect genuine alterations in emotional states. Additionally, the generalizability of the findings to long-term remediation strategies remains an open question.

We agree with this characterisation and have strengthened the corresponding acknowledgment in the Discussion. We would also note that, while self-report measures are inherently subjective, the regularities governing subjective emotional experience are of primary scientific interest in their own right, and no consensus definition of a ”genuine” emotional state that supersedes self-report currently exists. We have added a sentence to the Discussion making this point explicit: ”While emotional self-reports are inherently subjective, we note that the regularities governing subjective emotional experience are of primary scientific interest in their own right, and no consensus definition of a ‘genuine’ emotional state that supersedes self-report currently exists.”

Additionally, we agree that what we have described is limited to a short-term intervention and change. Whether these changes bear on longer-term changes remains to be assessed. Furthermore, the mechanisms or processes that would support such a maintenance are of substantial interest, and will be the focus of future work.

Statistical analysis and interpretation of the dynamics matrix

Second, the statistical analysis, particularly the computational approach, sometimes lacks sufficient detail and refinement. While I will not elaborate on specific points here, one notable issue is the interpretation of the intrinsic matrix (A). The model-free analysis reveals correlations between emotions at a given time or within an emotional state across time points. However, it does not provide evidence to support lagged interactions across states that would justify non-diagonal elements in A. The other result concerning the dynamics matrix only highlights a trend in the dominant eigenvalue, which is difficult to interpret in isolation. The absence of a statistically significant group x intervention interaction furthermore makes this finding a little compelling. This weakens the study’s conclusions about the importance of intrinsic dynamics, as claimed in the title.

We thank the reviewer for raising this important methodological point. We address it in three parts.

(i) Justification for the full dynamics matrix. In response to this comment, we have added a diagonal-constrained variant of A to the model comparison. The full A model was selected by BIC over the diagonal-constrained version, meaning that cross-emotion lagged interactions contributed to model fit over and above what could be explained by individual emotion autocorrelation alone, thereby justifying the inclusion of off-diagonal elements. We have updated the model comparison results section and figure caption accordingly.

(ii) Interpretation of the dominant eigenvalue. We agree that the dominant eigenvalue alone is difficult to interpret. Our primary claim regarding intrinsic dynamics rests on model comparison (which identified a change in A as necessary to explain post-intervention data in the distancing group) together with the change in the direction of the dominant eigenvector (tested via Hotelling T², p = 0.019). The eigenvalue magnitude is reported as a complementary, interpretable summary of the stability shift.

(iii) General analysis of the dynamics matrix. We have added a visualization of the full dynamics matrix A to the Supplementary Materials, reporting per-emotion diagonal elements (persistence) and their variability across participants. This shows that the emotion calm exhibited the highest persistence, consistent with our hypothesis, whereas sadness showed lower-than-expected stability, and other emotions exhibited low mean persistence with substantial individual variability. We have added the following sentence to the Results: ”A general analysis of the dynamics matrix A revealed that while calm exhibited the highest persistence, consistent with our hypothesis (0.59 ± 0.85), sadness did not show the expected stability (0.09 ± 0.58), and other emotions demonstrated low persistence (0.13 to 0.24) alongside substantial individual variability.”

Terminology (controllability, stability, sensitivity, Gramian)

Finally, to avoid potential misunderstandings of their work, the authors should be more careful about their use of terms pertaining to the control theory and take the time to properly define them. For example, the ”controllability” of emotional states can either denote that those states are more changeable (control theory definition), or, conversely, more tightly regulated (common interpretation, as used in the abstract). This is true for numerous terms (stability, sensitivity, Gramian, etc.) for which no clear definition nor references are provided. Readers unfamiliar with the framework of control theory will likely be at a loss without more guidance.

This is an excellent and important point. We have made the following changes throughout the manuscript.

(i) Terminology table. We have added a new Table 1 in the Methods (Conceptual Definitions) providing a side-by-side mapping of the formal control-theory definition and the psychological interpretation for the three key terms: Controllability, Stability, and Sensitivity.

(ii) Abstract. The abstract previously used ”controllability” in a way that could be read in the psychological sense. We have replaced the sentence referencing the Controllability Gramian with a clarified version describing the measure as ”continuous measures derived from the controllability matrix, capturing relative differences in how emotional states can be driven by external inputs.”

(iii) Introduction. We have added a paragraph explicitly distinguishing the control-theoretic definition of controllability from the psychological concept of emotion control or emotion regulation, noting that high controllability in the formal sense does not imply tight regulation or reduced variability. Definitions of sensitivity and stability are also provided.

(iv) Discussion. Occurrences of ”controllability” that could be ambiguous are annotated with brief clarifications of which sense is intended.

(v) Gramian. We now use the ”controllability matrix” (C) throughout, and its SVD-based analysis is described using ”left singular vectors” rather than ”eigenvectors of the Gramian”.

Reviewer #2 (Public reviews):

Online recruitment, selection effects, and remuneration

Acquiring data online inevitably gives rise to selection and self-selection effects. This needs to be acknowledged clearly. Exacerbating this, participant remuneration seems low at an amount below the minimum or living wage in Western countries (do the authors know where their participants came from?).

We thank the reviewer for raising this. All participants were recruited from the UK via Prolific Academic and reimbursed at £7.50/h. Remuneration rates were comparable to other experimental settings, in keeping with other online studies, UK living wage recommendations, and ultimately determined according to institutional ethical guidance. We acknowledge that online recruitment via Prolific may introduce self-selection effects and that the sample may not be representative of the general population. We have added a corresponding statement to the Limitations section: ”Online recruitment via Prolific Academic may introduce self-selection effects, and the sample may not be representative of the general population.”

Intervention ongoing during the second block

Another concern is that the intervention does not simply take place before the second block begins but is ongoing during the whole of the second block in that it is integrated into the phrasing of the task on each trial. It is therefore somewhat misleading to speak of a period ’after the intervention’, and it would have been interesting to assess the effect of this by including a third group where the phrasing does not change, but the floating leaves intervention takes place.

This is a valid and important observation. In the distancing group, the trial-by-trial question phrasing during the second block included a reminder, meaning the intervention was reinforced on every trial. We have acknowledged this as a procedural difference and potential confound in the Limitations section, noting that this reminder may have encouraged a form of retrospective reappraisal rather than in-the-moment distancing. The design choice was intentional (the reminder was included to encourage continued application of the strategy, mirroring how such techniques are deployed in practice) but we agree it is an imperfect feature of the current design and have discussed it openly. We have added to Limitations: ”Relatedly, a procedural difference existed in that only the distancing group received a strategy reminder during the second video block. While intended to facilitate real-time regulation, this prompt may have inadvertently encouraged retrospective reappraisal to align with the distancing narrative.”

Observation noise

As mentioned in the Limitations section, observation noise was assumed and not estimated. While this is understandable in this case, the effect of this assumption could have been assessed by simulation with varying levels of observation (and process) noise.

We would like to clarify that both observation noise (Γ) and process noise (Σ) were in fact estimated from the data, constrained to be diagonal. We have extended the parameter recovery analysis (Supplementary Section: Parameter Recovery) in which, for each of 104 subjects and both time periods (N = 208 observations), we generated 100 surrogate trajectories from the fitted model and re-estimated all parameters. Recovery quality is quantified via Pearson correlations between true and recovered parameters (A, C, Σ, and Γ), alignment of dominant eigenvectors and left singular vectors, and bias analysis for dominant eigenvalue and singular value magnitudes. The analysis confirms that A and C matrix parameters and the critical eigenvector-based metrics all exceed our target threshold of r = 0.7. Noise covariances are poorly recovered, consistent with typical Kalman filter behaviour on short time series. We have expanded the Limitations to note that the Gaussian observation noise assumption does not fully capture the bounded nature of 0–100 rating scales, and suggest that future work could use a truncated or censored observation model.

Reliance on formal model comparison

Relatedly, the reliance on formal model comparison is unfortunate since the outcome of such comparisons is easily influenced by slight changes to assumptions such as noise levels. An alternative approach would have been to develop a favoured model based on its suitability to address the research question and its ability, established by simulation, to distill relevant changes of behaviour into reliable parameter estimates.

We appreciate this methodological concern but would argue that formal model comparison is wellsuited to our research question. Our central aim is not simply to fit emotion trajectories, but to determine which components of the dynamical system (intrinsic dynamics (A), input weights (C), or both) are altered by the distancing intervention. This is inherently a model comparison question: without comparing models that do and do not allow each component to change, no principled inference about the mechanism of action is possible. A single favoured model, however well-motivated, would presuppose the answer.

We also note that the reviewers concern, that outcomes are sensitive to underlying assumptions, applies equally to the favoured-model approach: simulations rely on predefined structures and noise specifications that shape parameter recovery, and a misspecified favoured model risks confounding the parameters intended to capture the intervention effect with artefacts of model structure. By contrast, our approach evaluates a principled, nested set of models of increasing complexity, using BIC to penalise unnecessary parameters, which guards against overfitting. The models are intentionally simple (linear, Gaussian, time-invariant) to limit the degrees of freedom available to absorb noise.

Critically, the approach is not model comparison alone. We followed established best-practice procedures for computational modelling, including posterior predictive checks (simulated trajectories closely matched observed data; Fig. 4C), and parameter recovery establishing that the key metrics are reliably recovered (see Supplementary Materials F Parameter Recovery). We have also added a Random-Effects Bayesian Model Selection (RFX-BMS) to characterise individual heterogeneity in model preferences. Together, these provide converging evidence for the validity of our inference. We have clarified this reasoning in the revised manuscript.

Statistical limitations; Bayesian inference

The statistical analyses clearly show the limitations of classical statistical testing with highly complex models of the kind the authors (commendably) use. Hunting for statistically significant interactions in a multivariate repeated-measures design relying on inputs from time series- derived point estimates is a difficult proposition. While the authors make the best of the bad 3 situation they create by using null-hypothesis significance testing, a more promising approach would have been to estimate parameters using a sampler like Stan or PyMC and then draw conclusions based on posterior predictive simulations.

We agree that fully Bayesian parameter estimation via Stan or PyMC would be a valuable methodological advance. Implementing this for 104 subjects across two time periods with a 5-dimensional Kalman filter is, however, a substantial undertaking beyond the scope of the current revision. In the interim, the RFX-BMS analysis added in response to Comment 4 above provides a group-level Bayesian perspective on model uncertainty that partially addresses this concern.

Reviewer #3 (Public reviews):

Dual meanings of controllability

An interesting but perhaps at present slightly confusing aspect of their described results relates to the ’controllability’ of emotions, which they define as their susceptibility to external inputs. Readers should note this definition is (as I understand it) quite distinct from, and sometimes even orthogonal to, concepts of emotional control in the emotion literature, which refer to intentional control of emotions (by emotion regulation strategies such as distancing). The authors also use this second meaning in the discussion. Because of the centrality of control/controllability (in both meanings) to this paper, at present it is key for readers to bear these dual meanings in mind for juxtaposed results that distancing ”reduces controllability” while causing ”enhanced emotional control”

We are grateful for this observation, which echoes Reviewer 1’s concern about terminology. We have addressed this comprehensively; please see our response to Reviewer 1 Comment 3 above.

Strategy reminder and possible reappraisal

As above the authors use an active control – a relaxation intervention – which is extremely closely matched with their active intervention (and a major strength). However, there was an additional difference between the groups (as I currently understand it): ”in the group allocated to the distancing intervention, the phrasing of the question about their feelings in the second video block reminded participants about the intervention, stating: ”You observed your emotions and let them pass like the leaves floating by on the stream.” I do wonder if the effects of distancing also have been partially driven by some degree of reappraisal (considered a separate emotion regulation strategy) since this reminder might have evoked retrospective changes in ratings.

This is a well-founded concern. As noted in our response to Reviewer 2 Comment 2, we have added an explicit acknowledgment of this procedural difference and the potential for retrospective reappraisal to the Limitations section. We note, as the reviewer themselves observe in the Strengths section, that demand effects are unlikely to account for the specific pattern of dynamic changes observed: uniform demand effects would be expected to produce flat reductions across emotions, whereas our findings show emotion-specific changes in eigenmode structure and controllability direction. Nevertheless, a partial contribution of reappraisal cannot be ruled out from the current design.

Mechanism of distancing effects (eye movement and oculomotor avoidance)

Not necessarily a weakness, but an unanswered question is exactly how distancing is producing these effects. As the authors point out, there is a possibility that eye-movement avoidance of the more emotionally salient aspects of scenes could be changing participants’ exposure to the emotions somewhat. Not discussed by the authors, but possibly relevant, is the literature on differences between emotion types on oculomotor avoidance, which could have contributed to differential effects on different emotions.

We thank the reviewer for raising the oculomotor avoidance hypothesis. Research suggests that different emotions elicit distinct patterns of gaze behaviour: disgust is associated with visual avoidance, whereas anxiety and other negative emotions show increased attentional bias following fear conditioning. These emotion-specific oculomotor patterns could have contributed to the differential effects we observe on the input weight matrix C. What would be particularly interesting to examine in future work is whether a distancing intervention induces multiple, emotionally-specific gaze behaviours, or a single undifferentiated avoidance response. We have expanded the Limitations to: ”[...] The literature on emotion-specific oculomotor avoidance suggests that gaze patterns differ across emotion categories, which could contribute to differential effects on the input weight matrix for specific emotions. [...]”

Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

(1) In the procedure description, the authors suggest that some emotions (e.g. disgust) would be more volatile and stimulus driven, while others (eg. sad) would be more stable. Is this hypothesis reflected in the model-based state dynamics, typically in the diagonal elements of A?

Yes, we added a supplementary figure showing the dynamics matrix A, which confirms that calm exhibited the highest persistence, consistent with our hypothesis. Disgust showed lower persistence, also in line with this expectation. However, sadness did not display the expected stability and instead showed relatively low persistence, contrary to our hypothesis.

(2) Could the authors elaborate on the emotional space covered by the chosen ratings? If the axes are positive-negative and slow-fast, why 5 and not 4?

We added a sentence in the Methods clarifying that five emotions were selected based on the specific affective qualities of the video stimuli provided in the validated databaseto and to better capture the high-dimensional, nuanced states elicited by the stimuli rather than to fit a traditional four-axis model.

(3) The whole methods section crucially lacks references. As an example, the whole derivation of the most important metrics (eigenvalues of the Gramian, energy ellipse, etc) leaves the reader completely on its own.

References have been added throughout the Methods, including for the controllability matrix, SVDbased analysis, and eigendecomposition.

(4) Before equation 1, when introducing x and u: a) time appears twice (typo), and b) the 1Tˆ notation is not standard (especially without bold) and unclear until way below when the one-hot encoding is mentioned.

The typo has been corrected.

(5) Why use one hot-encoding rather than the original ratings from the video database? Videos must vary if not in spread (as suggested in Figure B.1) at least in intensity. Ignoring this variance surely diminishes the accuracy of the modelling.

We used one-hot encoding so that the input weight matrix C can directly estimate participantspecific intensity and sensitivity, rather than fixing input magnitudes to database averages. Using database ratings would assume that the emotional intensity of each video clip generalizes perfectly to our sample; any mismatch would be absorbed as error in C, potentially biasing parameter estimates and obscuring individual differences in emotional reactivity, which are central to our analysis.

(6) Could the authors develop the rationale behind the bias in Equation 1?

We added a sentence clarifying that the bias term h captures the steady-state baseline of the emotional system, i.e. the mean rating toward which emotions converge in the absence of external inputs.

(7) While I can understand why the authors included a set of models with a diagonal C matrix, I do not see why they did not do the same with A. While the diagonal elements are necessary to persist emotional states and induce some autocorrelation in the ratings, as observed empirically, the influence of the non-diagonal elements is not justified (and Figure 5G seems to confirm that). This is critical as, in the end, the controllability metrics will highly depend on those non-diagonal elements which remain very obscure throughout the manuscript.

We now included both diagonal and full variants of A in the model comparison; still the full A was selected by BIC.

(8) Concerning the model comparison, I am not sure what the authors mean by using the BIC at the group level. Did they just sum them across participants? This approach is known to be highly susceptible to outliers and cannot be relied upon in general. So-called ”random effect analysis” tends to be regarded as the gold standard and can be easily implemented by taking - 0.5 * BIC as an approximation to the model evidence. Such an approach would also allow to properly test for group differences (cf. Rigoux et al. 2014).

We have added a Random-Effects Bayesian Model Selection analysis as a new Supplementary Section; see Comment 4 of the public review response above.

(9) The sentence ”proportion of the total amount of predictive power provided by the full set of models contained in the model being assessed” does not make any sense to me. Please rephrase.

The sentence has been rephrased: ”Cumulative model weights (w_j) normalize raw BIC scores so they can be interpreted as the relative probability that a specific model is the best one among the set being compared:”

(10) ”the largest eigenvalue of the dynamics matrix A identifies the most stable combination of emotions” is only true if the eigenvalues are below 1, which is not granted.

We have added the qualifier that this holds provided the dominant eigenvalue lies within the unit circle (|λ| < 1), indicating a system that converges to a steady state.

(11) Equation 3 does not define the Gramian but the controllability matrix, a confusion that goes through the manuscript. The Gramian is formally defined as W = P(AkBB′A′k). Luckily, for discrete systems, it can be approximated by CC′ and therefore the singular values of C can be used to approximate the eigenvalues of W, which are the usual metrics used to define the energy ellipse and so on. While the results reported in the manuscript are correct (up the the approximation), the general description is wrong or misleading.

We thank the reviewer for this important correction; we now consistently refer to C as the ”controllability matrix” throughout, and its SVD-based analysis is described in terms of left singular vectors rather than eigenvectors of the Gramian.

(12) Figure 2: what is the matrix V? If it’s from the singular value decomposition W = USV, then (if I am not mistaken) the direction of the ellipsoid is defined by U. Again, a reference would help.

We have corrected the figure and caption to refer to ”left singular vectors” throughout. We retain the variable name V rather than adopting the standard SVD convention of U to avoid confusion with the input vector u, which appears throughout the model equations.

<(13) Correction for multiple comparisons is mentioned as a way to correct for the number of conducted tests. However, later on, some post-hoc analyses are reported with the mention that the correction is done across emotions (so p/5), while multiple tests are run for each emotion. This is critical when all the pairs across the cells of an ANOVA are tested and no correction seems to be applied, which is inducing a huge risk of false positives.

Along the same line: the correct way to demonstrate the effect of the intervention is to first do an ANOVA to reveal an interaction between group and time, and then only to do post-hoc tests to pinpoint where the interaction is coming from, and not the other way around as reported in the manuscript. Further, a difference in significance is not equivalent to a significant difference, and showing that a time effect is significant in one group but not in the other does not imply that the intervention differs between groups, only testing the interaction can confirm this.

We have added reporting of the significant group × time interaction effects (F(5,208) = 2.6, p = 0.026 for mean ratings; F(5,200) = 2.5, p = 0.03 for the most controllable direction) and flagged these in the figure captions. In the interest of transparency we have left the structure of the results section intact rather than retrospectively reframing it.

(14) The notation DV = b0 + b1IV*b2G is confusing as a full model (interaction + main effects) should have 3 parameters in addition to the intercept. Also, why use different models for testing the main effect and the interaction?

The regression equation has been corrected to DV = β₀ + β₁IV + β₂G + β₃(IV × G) + ϵ, making the interaction term explicit.

(15) Figure 4: the control subject in panel C seems to rate close to 0 in all emotions except for ”calm”. How was this subject fitted? Does model selection (at the subject level) correctly identify a change of dynamics in this case? I don’t see how the behaviour after the intervention could be realistically fitted with a 65-parameters dynamical system. What type of checks were operated to ensure the quality of the fit beyond the recovery analysis (see below)?

The top participant in Figure 4C was from the distancing group and the participant rating close to zero on most emotions except calm shown at the bottom was from the control group. For the distancing participant, model selection correctly identified a change in dynamics and input weights (BIC = 4806) over the same-parameters model (BIC = 4821). For the control participant, model selection similarly favoured a change in dynamics and input weights (BIC = 3723) over the sameparameters model (BIC = 4011), suggesting that the relaxation intervention produced a comparable effect on emotional dynamics to the distancing intervention. Note that these two participants were selected randomly to illustrate the visual quality of model fit (i.e. that simulated trajectories closely resemble the empirical rating curves) and are not intended to be representative examples of group differences.

Regarding the data-to-parameter ratio: the 65 parameters are estimated from 55 observations per emotion per block, giving a more favourable ratio than it might appear.

Beyond the visual trajectory overlays in Figure 4C, we have now added R² and peak cross-correlation as a quantitative measure of individual fit quality. Mean R² across all subjects and emotions was 0.6 and mean temporal correlation was r = 0.74−0.80, confirming that both the timing and magnitude of emotional responses were well reproduced. Notably, for the specific control participant shown in Figure 4C, R² values were 0.74, 0.83, 0.81, 0.83, and 0.83 for disgusted, amused, calm, anxious, and sad respectively, confirming that even for this visually striking participant the model fit was adequate across all five emotion dimensions.

(16) What do the authors mean by ”eigenmodes”? In the following sentence, what does ”This component” refer to?

Eigenmodes is defined in the Stability section as the independently evolving combinations of emotions obtained by projecting the state vector onto the eigenvectors of A, and ”This component” has now an explicit referent.

(17) Figure 5: see above the comment about the necessity for testing the interactions, which should also be reported in the figures.

Interaction effects are now included in the relevant figure caption (Figure 5).

(18) When looking for the relationships between questionnaires and controllability, looking only at the most controllable direction seems rather inefficient due to the multiple comparisons correction. Why not compute the angle (or other measure of similarity) with an ideal ”calm” unit vector?

Along the same line, it’s unlikely that the most controllable direction will smoothly rotate as a function of symptoms. More likely, the winning (highest eigenvalue) direction will switch from one to another, creating some discontinuity in the summary statistic used for the correlation with clinical scores. How could one work around this issue?

This is an interesting suggestion; we have not implemented it in the current revision, but we acknowledge it as a promising analysis for future work.

(19) More generally, it would be interesting to see if there are some regularities in the dynamics across participants. If this is the case, one could construct a canonical emotional dynamics and project all participants on this eigenspace. Emotional trajectories would then differ only in their controllability (eigenvalues) in this common space, making a comparison across participants more straightforward. Could the authors comment on this?

This is a valuable suggestion that we have not pursued in the current revision, as constructing a common eigenspace across participants requires additional methodological choices.

(20) I am a bit puzzled by the hypothesis that questionnaires should mediate the intervention effect. Shouldn’t questionnaires be related to before-intervention controllability only? Similarly, could one use initial controllability to predict the intervention response (irrespective or not of the clinical score)?

Our hypothesis was that participants with greater difficulties in emotion regulation (high DERS-18) would show a smaller intervention effect, as their emotional system might be less amenable to brief distancing. However, this was not the case. We also note that DERS-18 scores were not significantly related to the overall magnitude of pre-intervention controllability (norm of the controllability matrix), but were related to its direction: participants with higher DERS-18 scores showed a most controllable direction pointing toward disgust and away from amusement and calmness, suggesting that trait-level regulation difficulties are linked to the specific emotional configuration of the system rather than its overall controllability.

Regarding using initial controllability to predict the intervention response: we agree this is a mechanistically appealing question, but it is unfortunately not straightforward to address here. The intervention effect would be quantified as the change between pre- and post-intervention controllability, and since pre-intervention controllability is a constituent of that change score, any correlation between the two would be partially circular by construction.

(21) The recovery procedure should be way more detailed. How many surrogates were run, etc.? Which kind of quality checks were used to ensure the recoverability was sufficient at the subject level, especially as parameter recovery seems relatively low for some subjects?

The parameter recovery section now reports that 100 surrogate trajectories were generated per subject (N> = 104) per time period (before and after intervention: N = 208 observations total), with per-subject recovery quality reported across simulations together with across-subject variability; see Supplementary Materials F Parameter Recovery.

(22) As the result of the eigen decomposition is the endpoint of the analysis, it would be a nice addition to test the recoverability of those measures (eg. correlation between simulated and inferred eigenvalues).

Recovery of the dominant eigenvalue/vector and dominant singular value/left singular vector is now reported explicitly, including bias analysis and scatter plots of true versus recovered values. Beyond subject-level recovery, we also assessed whether the observed group differences in emotional dynamics and controllability could be reliably recovered at the group level. See Supplementary Materials F Parameter Recovery.

(23) Although this comment comes close to last, this is a major concern of mine. I am not convinced that the recoverability procedure is sufficient to prove that the inference is working. The model assumes that the observation noise is Gaussian, which is clearly not the case in the data. By simulating surrogate time series with normally distributed noise, the authors do not account for any saturating effects that could destroy a large part of the behavioural information necessary for a successful inversion (eg Figure 4.C showing that simulated data contains a lot of negative ratings). A workaround would be to bind the surrogate time series to mimic the saturation caused by the rating scale, and then run the model estimation on those capped time series.

We acknowledge this important limitation: the Gaussian assumption does not capture the bounded 0–100 scale, and we have added this to the Limitations with a suggestion that future work use a truncated or censored observation model.

(24) Supplementary tables with placeholders (v1, v2) that can vary in meaning depending on the line are extremely hard to decipher.

The supplementary tables have been restructured to a hierarchical format.

(25) Table I9 is not referenced in the manuscript.

A reference to this table has been added in the appropriate Results section.

(26) It’s a shame that neither data nor analysis code has been made available.

Fully anonymised data and analysis code are now publicly available on GitHub (https://github.com/huyslab/emotioncon public).

Reviewer #2 (Recommendations for the Authors):

(1) Abstract: By some definitions, controllability is binary, present or absent, according to whether the controllability Gramian is positive definite. Mention that you use a continuous definition, otherwise ’quantified’ leads to confusion.

The abstract now describes the measure as: ”Controllability was assessed using continuous measures derived from the controllability matrix, capturing relative differences in how emotional states can be driven by external inputs.”, making the non-binary usage explicit.

(2) p 5: ’on [not in] the recruiting platform’.

Corrected.

(3) p 8: Clarify notation of x_tt = 1^T (and same for u). What does this mean?

The notation has been corrected.

(4) p 8: Define h in the paragraph following Eq 1, don’t wait until the next section.

The definition of the bias h (steady-state baseline) has been moved to immediately after Equation 1.

(5) p 9: Give clear references for your methods here. There are different definitions of controllability etc. than the ones you use.

References have been added at each key definition.

(6) p 28: ’20 videos per emotion category were chosen resulting in 50 videos per sequence’ - doesn’t make sense.

This has been clarified: 20 videos per category across 5 categories yield 100 videos in total. These were split into two matched sequences of 50 videos each. Including 2 videos that were repeated twice resulted in 54 videos per sequence and 108 videos in total.

(7) Figure B2: 54 videos are listed, and categorized into five categories. How does this relate to the remark right above?

A clarifying note has been added to the supplementary explaining that each sequence of 54 clips includes repeated videos and is drawn from the pool of 100, with emotion-category sequences matched between blocks.

(8) p 29: What were the process noise Σ and observation noise Γ assumed in the parameter recovery exercise? What were the consequences of that assumption as assessed by simulation?

Both Σ and Γ were estimated from the data constrained to be diagonal; the parameter recovery section now explicitly reports their recovery quality.

(9) p 30: How are results affected by including the excluded participants? The level required to pass attention checks seems arbitrary. How was it chosen?

We have added a sensitivity analysis including the four excluded outliers, showing results remained qualitatively and statistically similar. With 10 binary attention checks, chance performance is 50%, meaning a participant scoring below 70% is performing only marginally above chance and likely not attending consistently. At the same time, 70% is permissive enough to retain participants who may have missed one or two checks due to momentary distraction.

(10) Figure F4: Typographically distinguish capital letters referring to panels in the figure from those referring to matrices.

Panel labels in Figure F4 are formatted in bold to distinguish them from italicised matrix notation.

(11) Table G1: Showing that differences between groups were non-significant before the intervention but significant after is not enough, you need to show that there was a significant interaction between time point and intervention. [I wrote this after reading the supplementary but before reading the main text. It turns out you know what I’m telling you here. You should mention it more prominently though, including in the abstract and the discussion, because in your chosen null-hypothesis significance testing framework, this is the crucial test of your study. I don’t think there’s any harm at all in being up-front about this - certainly much better than making excuses like the one about randomization at the top of page 11, which I recommend removing].

This is very right. The significant group × time interaction effects are now reported prominently in the main text Results and figure captions. We also wish to be transparent: the interaction tests were conducted post-hoc rather than as the primary analysis, which is the reverse of the correct order. In the interest of transparency we have left the structure of the results section intact rather than retrospectively reframing it.

Reviewer #3 (Recommendations for the Authors):

(1) I would encourage the authors to re-add some basic details regarding their power analyses from the supplement to the main text so the reader can immediately reference the intended effect size, which analysis/analyses were considered primary for the power analysis, etc.

More information about the power analysis have been added to the Participants section of the main text.

(2) Similarly, I wondered if there could be a little extra information on how the test-retest reliability was calculated (page 13) - on the first and last views of a video pre-intervention? I wasn’t sure - why do the authors only present ICCs for amusement/joy and disgust/horror? Seems useful to present all (particularly because there may be individual differences in habituation to some emotions).

We have expanded the test-retest section to clarify that reliability was assessed using duplicate videos shown three times pre-intervention, and now report ICCs with confidence intervals, Cronbach’s α, and habituation/sensitization tests for both disgust and amusement; the selection of these two categories reflects which videos were repeated in the design, they were chosen at random during experimental design.

(3) Regarding my comments about controllability/emotional control, I think the authors probably have two choices - address this head-on (e.g. with a note describing the relationship/distinction between these two concepts of controllability), or else avoid using it in one of the senses (I would suggest the mathematical sense since overriding the concept of cognitive control seems harder - the authors could use phrases like ’impact of emotional inputs’ instead of ’controllable’). In particular, the abstract could be clearer about the nature of controllability as implemented by the authors - this seems critical for communicability. Because of the high relevance of both of these ’control’ concepts to the paper, if the authors agree with my concern, I would also suggest changes throughout, such as in the results section phrasing: ”In those participants with high DERS-18 scores, the most controllable direction pointed towards disgust ( = 0.26, p = 0.006), and away from amusement ( = 0.26, p = 0.005) and calmness ( = 0.24, p = 0.011; though this did not survive Bonferroni correction).”

Thank you for this comment. Please see our response to the public review comments above, which we hope address this.

(4) Regarding the control intervention, which is great, is it possible the follow-up question/reminder affected the results – e.g., is there reason to believe that prospective regulation was the primary difference in the distancing group and not a retrospective effect via this question?

See our response to Reviewer 2 public review Comment 2 and the corresponding Limitations addition.

(5) Lastly, purely for interest, the authors could consider elaborating on their brief interpretation as to why difficulties in regulating emotions were specifically linked to the controllability of disgust, amusement, and calmness, but not other emotions (anxiety/sadness) (page 20). I wonder if there is a brief space to discuss the emotional specificity of these results further given the relevance to the wider literature on specific emotion types, e.g. fear vs disgust.

We have expanded the Discussion to elaborate on the emotional specificity of these findings. Amusement and disgust are strongly influenced by external events, suggesting that stimulus-driven controllability is particularly relevant for these emotions. By contrast, anxiety and sadness are maintained through internally generated processes such as rumination and anticipatory cognition, exhibiting greater emotional inertia over time, and their regulation may therefore be less sensitive to momentary stimulus controllability. This provides a mechanistic account of why controllability effects emerged selectively for disgust, amusement, and calmness, and aligns with growing evidence that emotion regulation is emotion-specific rather than domain-general.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This important study partially fills the gap in the knowledge of olfaction at the level of the Anterior Olfactory Nucleus (AON) and Piriform Cortex (Pir) with functional magnetic resonance imaging, electrophysiology, and modeling. The methods used are convincing. Some of the findings confirm ongoing hypotheses, such as the behavioral importance of AON for odor source discrimination. Other results shed light on the dynamics of the connection between the olfactory system and the rest of the brain.

We sincerely thank the editors and reviewers for the thorough review of our manuscript. We appreciate the insightful comments, which have significantly contributed to improving our work. In this revision, we addressed all the concerns posed by the reviewers, including conducting additional analyses and providing the data generated and codes used in this study.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript combined rat fMRI, optogenetics, and electrophysiology to examine the large-scale functional network of the olfactory system as well as its alteration in an aged rat model.

Strengths:

Overall methodology is very solid and the results provided an interesting perspective on large-scale functional network perturbation of the olfactory system.

Weaknesses:

The biological relevance and validation of the current results can be improved.

We thank the reviewer for the comments and suggestions regarding our manuscript. They have been invaluable and instrumental in enhancing our work. Please see R1-1 to R1-8 below for our corresponding responses and revisions.

Comments:

(R1-1) Figure 1A, on the top of the figure, ChR2 may be replaced by ChR2-mCherry, as only mCherry is fluorescent. And also, it’s somewhat surprising that in AON and Pir regions (where only axon fibers should be labelled as red), most fluorescence appeared dot-like and looked more similar to cell body instead of typical fiber. The authors may want to double-check this.

(a) Thank you for pointing out the missing fluorescent marker for ChR2 expression in the label of Figure 1A. We distinguished the transfection of ChR2 in olfactory bulb (OB) neurons from axonal terminals in AON and Pir by identifying the expression patterns in these three regions (see Figure 1). In OB, the cellular nucleus (i.e., labelled in blue by DAPI) was surrounded evenly by ChR2-mCherry expression (red fluorescent, indicated by green arrows in Figure 1), which clearly traced the neuronal cell body shape. Meanwhile, the expression of mCherry in AON and Pir consisted of concentrated red fluorescent dots that were sparsely assembled near the cell nucleus, indicating the presence of synaptic boutons at the axonal terminals. Further, the patterns of expression here did not trace the shape of the neuronal cell body.

(b) In this revision, we amended the label of Fig. 1A to “ChR2-mCherry”.

In this revision, changes were made to the confocal images of AON and Pir, based on Figure 1, for clarity and the figure caption was also edited accordingly.

(R1-2) The authors primarily presented 1 Hz stimulation results. What is the most biologically relevant frequency (e.g., perhaps firing frequency under natural odor stimulation) among all frequencies that were used?

(a) There are various firing rate and oscillatory frequency of neural activities within the olfactory system (i.e., OB, Pir) in rodents during olfaction. For example in OB, neural oscillations ranging from 1 to 12 Hz (i.e., slow to theta) are driven by sensory stimulation and are closely linked to respiration [1]. Specifically, odor-evoked responsive excitatory bursts of mitral and tufted cells in OB are coupled with the low-frequency respiration rhythm (1-4 Hz) [2,3]. Such coupling has also been documented during light anaesthesia [4]. Meanwhile, higher frequencies such as beta oscillations (15 ~ 30 Hz) have been associated with odor learning and sensitization [5,6], and gamma oscillations (40 ~ 80 Hz) evoked by sensory stimulation are associated with fine olfactory discrimination and odor learning [6-8].

The piriform cortex (Pir) also exhibits natural oscillatory activity across various frequency bands, including slow, theta, beta, and gamma oscillations [9-11]. As in OB mitral and tufted cells, slow oscillations (< 1.5 Hz) in Pir are also correlated with the respiratory rhythm, indicating the intrinsic respiration-related oscillatory properties within the olfactory system [12]. However, while it has been shown that the primary burst of firing in the anterior Pir is locked to respiration, its coding strategies differed from OB during olfaction [13].

Despite not being able to entirely mimic the evoked neural activities under natural odor stimulation due to the synchronizations induced by our optogenetic stimulations, our frequencies were chosen to be within the range of firing rates of neurons in the olfactory system under natural circumstances. Our selection of 1 Hz frequency for optogenetic stimulation was based on the balance of experimental simplicity of inducing neural excitation and the biological significance of low-frequency neural oscillations in OB, Pir and AON. The robustness of evoked brain-wide long-range activations is one of our criteria for the selection of 1 Hz stimulation frequency at OB, considering that the goal of this study is to examine long-range olfactory networks. Furthermore, we also examined other frequencies of stimulation covering theta, beta and gamma frequency bands, which provided insights into the response characteristics within the olfactory networks.

(b) In this revision, we added a brief statement in the Results section that 1 Hz was the most biologically relevant frequency based on discussions in R1-2a above.

(R1-3) In Figure 2, the statistical thresholding is confusing: in the figure legend, it was stated that “t > 3.1 corresponding to P < 0.001” but later “further corrected for multiple comparisons with thresholdfree cluster enhancement with family-wise error rate (TFCE-FWE) at P < 0.05”? Regardless of the statistical thresholding, such BOLD activation seemed to be widespread (almost whole-brain activation). Does such activation remain specific to the optogenetic stimulation, or something more general (e.g., arousal level change)? Furthermore, how those results (I assume they are group-level results) were obtained was not described very clearly. Is it just a simple average of individual-level results, or (more conventionally) second-level analysis?

(a) We thank the reviewer for drawing our attention to clarity issues regarding the generation of group-level BOLD activation maps and statistical thresholding methods used.

In brief, we first generate the BOLD activation map of individual animal through conventional general linear model (GLM) analysis. These individual activation maps then underwent a two-step statistical thresholding method to generate the group-level results. Firstly, uncorrected one-sample t-tests were conducted with a threshold of P < 0.001. Secondly, these thresholded activation maps were further corrected using nonparametric inference with threshold-free cluster enhancement multiple comparison correction of family-wise error rate (TFCE-FWE, P < 0.05) before they were averaged. Hence, the BOLD activation maps presented in our manuscript were the result of group-level analysis instead of individual-level analysis.

(b) We note the reviewer’s concern about whether the observed widespread BOLD activations were caused by the animal’s general brain state (e.g., arousal levels) rather than the specificity of optogenetic stimulation. First, such widespread activations were only specific to 1 Hz stimulation of OB neurons and OB afferents at AON (Figs. 2A, B and 3A, B) whereas activations were localized to regions in the primary olfactory network with increasing stimulation frequencies. Furthermore, varied neural activity adaptation properties were observed (Fig. 3A, B) following repeated 1 Hz optogenetic excitation of OB neurons and OB afferents at AON indicating that such widespread propagation of evoked neural activity was not driven by the animal’s general brain state, which would be relatively random across animals as we interleaved the presentation of each stimulation frequencies. While we cannot discount that certain characteristics of brain states differ under anaesthetized and awake conditions, we showed that light (1.0% isoflurane) anaesthesia minimally affects the BOLD fMRI activations and/or the propagation of optogenetically-evoked neural activity across thalamo-cortical, hippocampal-cortical and vestibulo-cortical networks [14-20].

Second, the neural representations in OB have been shown to be brain state-independent to ensure the high fidelity of olfactory inputs to higher olfactory cortices, despite differences in spontaneous baseline activity across states [21-24]. In fact, OB neural activity (i.e., slow to delta oscillations) remains highly coupled to respiration rhythms under low anaesthesia as in awake conditions [4]. Further, low-dose isoflurane (i.e., 1% as in the present study) does not affect cortical gamma oscillations (40 Hz) [25-28]. Although odorant-evoked responses in olfactory cortices (e.g., Pir and olfactory tubercle, Tu) can be modulated by overall brain state, various interactions between such cortical circuits to process odor inputs persist under anaesthesia [29-31].

(c) In this revision, we clarified the two-step statistical thresholding method that was applied to generate the group-level BOLD activation maps, as discussed in R1-3a above, in the captions of Fig. 2 and the Methods section of the manuscript.

In this revision, we also included a statement in the Discussion section that the widespread BOLD fMRI activations were specific to the 1 Hz optogenetic stimulation and not the animal’s general brain state, as discussed in R1-3b above.

(R1-4) In Figure 2, why use AUC to quantify the activation, not the more conventional beta value in the GLM analysis?

(a) We thank the reviewer for raising this concern. We are aware of the more conventional beta value, b, in GLM analysis and have used them for quantification and comparison of the amplitudes of fMRI activations in our previous rodent fMRI studies [18,32,33]. However, in this study, we chose to utilize area under curve (AUC) as it offers a more comprehensive measure of BOLD signal change over time, including shape, duration, and magnitude, thereby capturing the bulk of neural activities and their dynamics throughout the stimulation period. b primarily represents the peak amplitude of BOLD responses (i.e., the % BOLD signal change) [34] and can be constrained by the assumptions and limitations of the GLM analysis, such as the shape of the canonical hemodynamic response function (HRF). Therefore, AUC provides greater accuracy in capturing different aspects of neural responses across various brain regions, such as transient peaks and/or sustained responses.

(b) In this revision, we have included the justifications for using AUC over the more conventional b value to quantify BOLD fMRI activations, as in R1-4a above, in the Methods section.

(R1-5) For Figure 2D, the way that it was quantified can be better described as “relative” activation within one condition, and I don’t know how to interpret the comparison among the relative fraction of activated regions. Perhaps comparison using percentage change (i.e., beta values) is more straightforward.

(a) We thank the reviewer’s comment and suggestion here. “BOLD activation strength” is the AUCs normalized to the respective sum of BOLD activations of their respective stimulation target. We are of the opinion that “strength” can accurately reflect our purpose for conducting this comparison, which is to distinguish the brain networks that were predominantly recruited by AON- or Pir-driven neural activities compared to OB stimulation. 

(b) We conducted a comparison using relative fraction for fair comparison considering the differences in absolute BOLD signal amplitudes upon different stimulation targets. As we found the overall amplitudes of activations evoked by Pir stimulation were appreciably weaker, our normalization step ensures that the contribution of Pir is not underrepresented. Without this normalization process, the Pir stimulation seems not to activate most of the downstream targets based on the relatively weak activations. As discussed earlier in R1-4a above, comparison using percentage change/b value would be skewed towards the absolute amplitude of BOLD responses and would be erroneous for subsequent interpretation of brain networks that are primarily recruited by OB vs. AON vs. Pir.

(b) In this revision, we chose not to include additional statements as we have already described in the Results section the reasons for normalizing AUC to reflect and subsequently compare the BOLD activation strength across various networks that were recruited by optogenetic stimulation of three distinct olfactory regions (i.e., OB, AON and Pir). 

(R1-6) For Figure 3, it may be more convenient for readers to include the results of 1st activation for direct comparison. The current layout makes it difficult to make direct, visual comparisons among all 3 activations. Again, I think using beta values (instead of AUC) may be more conventional.

(a) We agree that it will be more convenient for readers if we include the 1st activation maps in Figure 3 for direct comparison. Please refer to R1-4 for the usage of AUC rather than beta values.

(b) In this revision, we modified Fig. 3 to include activation maps from the 1st fMRI session for easy comparison with the 2nd and 3rd sessions.

(R1-7) Can the DCM results (at least part of it) be verified using the current electrophysiological data? For example, the long-range inhibitory effective connectivity of AON is rather intriguing. If that can be verified using the electrophysiology data, it would be really great. In the current form, the DCM and electrophysiology results seem to be totally unrelated.

(a) We thank the reviewer for raising this concern, and it’s a great suggestion to causally link the outcomes from dynamic causal modeling (DCM) analysis and electrophysiology findings.

(b) In principle, the recorded local field potentials (LFPs) can be treated as the neural dynamic component in DCM analysis under specific conditions. They are as follows:

(1) LFPs are recorded at the identical brain state as the optogenetic fMRI experiments with identical stimulation paradigms.

(2) The electrode locations of LFP recordings must match the nodes of the a priori matrix defined for the existing DCM analysis (Fig. 4A).

However, in the present study, we did not have LFP recordings at the entorhinal cortex (Ent), which will likely influence the modeling of effective connectivity strength as one of the nodes defined is dropped from the analysis. Previous studies have showed that changes in the a priori matrix will result in different connectivity estimations [35-38]. We chose to model the connectivity involving Ent due to its documented interactions with the primary olfactory cortices and hippocampal regions [39,40]. Hence, it would be incomplete without modelling the contributions from Ent.

(c) In this revision, we decided not to redefine the a priori matrix by removing Ent as a node in the DCM analysis to estimate new effective connectivities. Instead, we acknowledge the absence of Ent recordings.

(R1-8) In Figure 6, it would be great if the adaptation of BOLD and electrophysiology signals can be correlated at the brain region level. The current figure only demonstrated there is adaptation in the electrophysiology recording, but did not show if such adaptation is related to the BOLD adaptation.

(a) We thank the reviewer for pointing out that we should associate the electrophysiology and fMRI data to validate the olfactory adaptation. As such, we conducted additional correlation analysis between LFP power and BOLD signal profiles. The method for computing the correlation coefficient is described below:

(1) For each 1 Hz optogenetic stimulation target (i.e., OB, AON, and Pir), regions of interest (ROIs) that have both LFP recordings and BOLD activations were selected. These ROIs were AON, Pir, ventral caudate putamen (vCPu), visual cortex (V1), and ventral hippocampus (vHP) for OB stimulation; OB, Pir, vCPu, V1, amygdala (Amg), and vHP for AON stimulation; and OB, AON, vCPu, V1, Amg, and vHP for Pir stimulation. Note that we excluded the respective stimulated region as a ROI because of BOLD fMRI signal dropout caused by the implanted optical fibre.

(2) We first calculate the individual animal AUC differences of 2nd stimulation session vs. 1st session and 3rd session vs. 1st session in LFP power and BOLD signal profiles, respectively.

Subsequently, the mean of the differences for each ROI across animals was then calculated.

(3) Correlation coefficients and P values of AUC differences between LFP power and BOLD signal profiles were computed using Spearman nonparametric correlation.

(b) The relationship between the differences of LFP power and BOLD signal profiles showing neural adaptation was described by the correlation coefficient, r, and the corresponding P value. The r and P values upon the three distinct stimulations were OB: r = 0.77 (P = 0.01), AON: r = 0.46 (P = 0.13), and Pir: r = - 0.06 (P = 0.85), respectively. This indicates that the decrease of LFP power is highly correlated with the decrease of BOLD activations upon OB and AON stimulation compared to those upon Pir stimulation.

(c) In this revision, we added the description of the correlation analysis conducted, as in R1-8a above, in the Methods section.

In this revision, we also added several statements in the Results section to indicate that neural adaptation observed is significantly related to the decreased BOLD activations when stimulating OB excitatory neurons or OB afferents at AON, as discussed in R1-8b above. Additionally, we also included the outcomes of the correlation analysis as a new Supplementary Fig. 7.

Reviewer #2 (Public review):

Summary:

Ma and colleagues presented a study on the characterization of brain-wide spatio-temporal impact of olfactory cortical outputs. They take advantage of multi-modal techniques on rats: fMRI, optogenetics, and electrophysiology. In addition, they used cutting-edge analytical techniques and modeling to support and interpret their data. The main findings of the study are:

(1) The neurons in the Olfactory Bulb (OB) predominantly activate primary olfactory network regions, while stimulation of OB afferents in Anterior Olfactory Nucleus (AON) and Piriform Cortex (Pir) primarily orthodromically activates hippocampal/striatal and limbic networks, respectively.

(2) Non-specified adaptation or habituation mechanisms may play a significant role in modulating olfactory outputs over subsequent fMRI sessions.

(3) Artificially induced aging in rats induces profound modification in the functional interaction between olfactory cortices and multiple brain regions.

The results on AON are of particular interest because of the lack of functional information on this region, despite its recognized importance in shaping OB output and behavior (odor localization tasks).

Strengths:

The manuscript is very accurate. The figures are well-crafted, and clear and provide much information with the most appropriate plots and graphics. The study’s amount and data quality are remarkable, and the experimental size adequately addresses the scientific questions. I particularly appreciated the details in the description of the methods regarding the missing data and the size of the different animal groups. The supplementary data complete the leading figures and provide information at a single animal level.

We are grateful for the reviewer’s appreciation of our study’s breadth and depth, and the quality and quantity of our data. The recognition of the strengths in our methods and the inclusion of single-animal-level data in the supplementary information is highly encouraging. We are also appreciative for the reviewer’s constructive comments below, which has help us to address specific weaknesses of the study and thereby improving the manuscript text and flow. We have read through the comments carefully and have made the necessary corrections. We hope that our responses to R2-1 to R2-11 below has sufficiently addressed all the reviewer’s concerns.

Weaknesses:

(R2-1) One of the main reasons the Piriform Cx is understudied in rodents is because of the proximity to air, which creates artifacts in fMRI images. This issue becomes more critical at ultra-high magnetic fields, but I would expect it also at 7T. One main achievement of this study is, indeed, the acquisition of fMRI data from Piriform, and this point should be highlighted by showing raw functional data from a rat. The best would be if an fMRI data sample for a rat, no matter which stimulation, is shared on a public repository, like Zenodo or similar. I am curious to check the quality of the BOLD data from such an ‘enormous’ field of view, particularly in the OB, with a single-shot sequence. Also, the visual inspection of raw data is essential to appreciate how many 0.5 x 0.5 x 1 mm voxels fit into AON, and others analyzed small brain structures, like the amygdala, etc. Was the amygdala entirely visible in BOLD, or did the air in the ear channel make an artifact partially shadowing it?

(a) As per the reviewer’s suggestion, we displayed the representative EPI images after preprocessing at a matrix size of 128 x 128 with a pixel size of 0.25 x 0.25 mm in Supplementary Figure 2. Up-sampling was not applied out-of-plane. Note that the atlas-based region-of-interest (ROIs) used to extract BOLD signal profiles (i.e., indicated by colored overlays in Supplementary Figure 2) were drawn based on the up-sampled EPI images (from the acquired 64 x 64 to 128 x 128). Notably, the piriform cortex (Pir) and amygdala (Amg) are visible with no appreciable signal dropout at these regions. To clarify, the Pir in our study represented the anterior Pir.

Signal dropout is pronounced in the posterior ventral regions of the brain (e.g., Bregma- 4 mm, below the Ent) and as expected in a localized region where the implanted optical fiber region that targeted the AON.

(b) In this revision, we included as a new Supplementary Figure 8 and added a statement in the Results section to describe the absence of appreciable signal dropouts at OB, Pir and Amg, which could affect subsequent quantitative analyses.

(R2-2) Surprisingly, the only information missing in the methods is the post-surgery period and the time between two consecutive fMRI sessions. How much time was accorded to rats to recover from the surgeries, and what time interval between two scans? This information is crucial for interpreting the decrease in most BOLD responses in subsequent recordings. The supposed adaptation should fit into the known time frames for odor adaptation. Usually, fast adaptation does not last for days (and it should be measured within a single experiment: is it the case?), while for long-lasting adaptation the stimulus (odor or opto) should be maintained constantly ON. This does not seem to be the case in this study. The hypothesis, alternative to adaptation, of a less efficient light activation, for example, due to gliosis around the fiber tips, should be discarded with more evidence than the preservation of OB > Pir responses or acknowledged in the manuscript.

(a) We thank the reviewer for drawing our attention to the missing information regarding the timeline of each optogenetic fMRI experiment. We conducted fMRI experiments immediately after the surgical procedure for implanting the optical fiber cannula. Such an implantation procedure typically last for 45mins under 1.2-2.0% isoflurane. The animal is then moved from the surgical table to the magnet to begin the optogenetic fMRI experiment. Intervals between two fMRI scans were within one minute. As the stimulation frequencies (i.e., 1 Hz, 5 Hz, 10 Hz, 20 Hz and 40 Hz) were pseudorandomized, the interval between any two identical stimulation frequency was on average 30 minutes. In this case, we are measuring fast adaptation (on the order of tens of minutes) rather than long-lasting adaptation. Further, as the fMRI experiment was conducted immediately following fiber implantation, the risk of gliosis around the fiber tips is expected to be low.

(b) The main representation of olfactory adaptation is the attenuation of neural responses upon continuous or repeated stimuli [41,42]. Several fMRI studies in rodents have reported that olfactory adaptation was detected in primary olfactory cortices (i.e., OB, AON, and Pir) upon repeated odor stimulation [43,44]. Specifically, these studies showed robust decreased responses in primary olfactory cortices under repeated odor stimulation with an odor interval of 30 minutes, which were comparable to those observed in our study upon repeated 1 Hz optogenetic stimulation. As such, the pronounced neural adaptation that we demonstrated when stimulating OB excitatory neurons or OB afferents at AON is unlikely to be caused by less efficient light activation.

(c) In this revision, we added statements in the Methods section, as discussed in R2-2a above, to clarify the timeline of our optogenetic fMRI experiment.

(R2-3) The D-galactose experiments were conducted only after administering the aging molecule, with no baseline/reference data on the same animals. Then, comparisons were made with healthy rats, but the two groups not only can be discriminated with respect to D-galactose administration but also with age (10 VS 18 weeks). A control group for 18-weeks-old rats with no D-galactose treatment would better compare the D-galactose effect and avoid any potential bias from group comparisons of rats at different ages. Do you confirm that D-galactose was injected into each rat 56 times/day in a row, or am I mistaken?

(a) We appreciate the reviewer’s comment here and understand the concerns regarding the absence of an age-matched control group with saline administration instead of D-galactose. We acknowledge that the inclusion of a control group would have provided a more direct comparison to evaluate the differences between healthy and aged animals. However, we were unable to include this group in the present study due to logistical constraints.

To clarify, our experiments were conducted on healthy rats at the median age of 14 weeks to ensure the animals had reached adulthood. The median age of the D-galactose injected animal was 18 weeks. In terms of the lifespan of rats, they reach sexual maturity at approximately 6 weeks of age [45], at which point we conducted the optogenetic viral vector injection. The age of rats at 14 and 18 weeks can both be regarded as teenage adult [45,46]. The primary purpose of the experiments on the aged animal model and corresponding analyses was to provide some potential clues into the dysfunction of olfactory networks at the system level as animals aged. Despite the age difference between the two groups, we believe that the comparison between healthy and aged rats still offers valuable insights into the ageing-related dysfunctions within the olfactory system. 

(b) Note that D-galactose was injected into each rat 56 times in total over the whole experiment (i.e., one injection per day over the course of 8 weeks).

(c) In this revision, we acknowledge that the comparisons made were not with age-matched healthy controls in the Discussion section.

In this revision, we also clarified that D-galactose was administered once daily for 8 weeks (i.e., a total of 56 injections) in the Methods section.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Minor:

(R2-4) The look of the activation maps will greatly improve if the displayed brain slices are coronal (as in the supplementary figures) with no angle.

We thank the reviewer for this suggestion. The purpose of such a display was to maintain the consistency of displaying the overlay of BOLD fMRI activation maps on the 3D renders of rat brain anatomical images. In addition, such 3D display can better impress readers that the optogenetically evoked BOLD activations were indeed long-range and brain-wide. 

As such, in this revision, we decided to maintain the existing displays of BOLD activation maps in the main figures.

(R2-5) The choice of testing different stimulation frequencies deserves more justification. Why was it performed in the OB, which is naturally activated on the breathing rhythm?

(a) We thank the reviewer’s comment here to seek further clarification. OB is widely recognized as the first stage of olfactory information processing in the brain. By activating the OB excitatory neurons, we can ensure that our optogenetically-evoked activations are olfactory-related.

The choice of various frequencies ranging from low (i.e., 1 Hz) to high (e.g., 40 Hz) was made to cover a range of firing rate and oscillatory frequency of neural activities neural oscillations that exist within the rodent olfactory system during olfaction. For example in OB, neural oscillations ranging from 1 to 12 Hz (i.e., slow to theta) are driven by sensory stimulation and are closely linked to respiration [1]. Specifically, odor-evoked responsive excitatory bursts of mitral and tufted cells in OB are coupled with the low-frequency respiration rhythm (1-4 Hz) [2,3]. Such coupling has also been documented during light anaesthesia [4]. Meanwhile, higher frequencies such as beta oscillations (15 ~ 30 Hz) have been associated with odor learning and sensitization [5,6], and gamma oscillations (40 ~ 80 Hz) evoked by sensory stimulation are associated with fine olfactory discrimination and odor learning [6-8].

(b) In this revision, we added a statement in the Results section to further describe our justifications for testing various stimulation frequencies.

(R2-6) The absence of natural (odor) stimulation should be acknowledged as a limitation for the findings of this study in the Discussion.

We thank the reviewer for the suggestion. In this revision, we made the acknowledgement in the Discussion section. 

(R2-7) Line 46: overstatement, the role of the Piriform cortex at the system level is well known and was not discovered by this study. (see Gordon Shepherd’s book: The Synaptic Organization of the Brain, Figure 10.6)

As per the reviewer’s suggestion, we decided to use “distinguishes” rather than “uncovers” for an accurate description of our study’s findings, which demonstrated the differences between the piriform cortex and anterior olfactory nucleus in driving the downstream activations of olfactory and non-olfactory targets.

(R2-8) Line 75: please rephrase for an easier understanding.

As per the reviewer’s suggestion, we edited this statement to “Further, the need to present a multitude of odor combinations also makes it challenging to efficiently and reliably interrogate long-range olfactory networks and their properties”.

(R2-9) Line 313: the intermediary region between the Piriform and Entorhinal cortices is the Perirhinal Cortex. No doubt about that.

As per the reviewer’s comment, we modified the corresponding statement by adding “such as the perirhinal cortex” and cited the appropriate references [47,48].

(R2-10) Line 391: there is no evidence from this study to exclude that the downstream targets would be less activated because of a decreased OB activation in favor of broad inhibition.

As per the reviewer’s suggestion, we modified the statement by replacing “rather than” with “in addition to” for a more precise statement.

(R2-11) Line 585: which was/were the regressor/s used in GLM? Any convolution with common HRFs?

We regarded the block-designed optogenetic stimulation as a task. The regressors are then obtained by convolving the expected task-evoked neural activity (i.e., boxcar function for block design) with the canonical hemodynamic response function, HRF (SPM12, Wellcome Department of Imaging Neuroscience, University College London, UK).

In this revision, we added a statement in the Methods section to provide clarification on the regressors used in GLM and the convolution step with canonical HRF.

References

(1) Kay, L. M. & Stopfer, M. Information processing in the olfactory systems of insects and vertebrates. Semin Cell Dev Biol 17, 433-442 (2006). https://doi.org/10.1016/j.semcdb.2006.04.012

(2) Cang, J. & Isaacson, J. S. In vivo whole-cell recording of odor-evoked synaptic transmission in the rat olfactory bulb. J Neurosci 23, 4108-4116 (2003). 

(3) Margrie, T. W. & Schaefer, A. T. Theta oscillation coupled spike latencies yield computational vigour in a mammalian sensory system. J Physiol 546, 363-374 (2003). https://doi.org/10.1113/jphysiol.2002.031245

(4) Fontanini, A. & Bower, J. M. Variable coupling between olfactory system activity and respiration in ketamine/xylazine anesthetized rats. Journal of Neurophysiology 93, 3573-3581 (2005). https://doi.org/10.1152/jn.01320.2004

(5) Kay, L. M. et al. Olfactory oscillations: the what, how and what for. Trends in Neurosciences 32, 207-214 (2009). https://doi.org/10.1016/j.tins.2008.11.008

(6) Gervais, R., Buonviso, N., Martin, C. & Ravel, N. What do electrophysiological studies tell us about processing at the olfactory bulb level? Journal of physiology, Paris 101, 40-45 (2007). https://doi.org/10.1016/j.jphysparis.2007.10.006

(7) Beshel, J., Kopell, N. & Kay, L. M. Olfactory bulb gamma oscillations are enhanced with task demands. J Neurosci 27, 8358-8365 (2007). https://doi.org/10.1523/JNEUROSCI.119907.2007

(8) Martin, C., Beshel, J. & Kay, L. M. An olfacto-hippocampal network is dynamically involved in odor-discrimination learning. J Neurophysiol 98, 2196-2205 (2007). https://doi.org/10.1152/jn.00524.2007

(9) Kay, L. M. Theta oscillations and sensorimotor performance. Proc Natl Acad Sci U S A 102, 3863-3868 (2005). https://doi.org/10.1073/pnas.0407920102

(10) Lowry, C. A. & Kay, L. M. Chemical factors determine olfactory system beta oscillations in waking rats. J Neurophysiol 98, 394-404 (2007). https://doi.org/10.1152/jn.00124.2007

(11) Vanderwolf, C. H. & Zibrowski, E. M. Pyriform cortex beta-waves: odor-specific sensitization following repeated olfactory stimulation. Brain Res 892, 301-308 (2001). https://doi.org/10.1016/s0006-8993(00)03263-7

(12) Fontanini, A., Spano, P. & Bower, J. M. Ketamine-xylazine-induced slow (< 1.5 Hz) oscillations in the rat piriform (olfactory) cortex are functionally correlated with respiration. J Neurosci 23, 7993-8001 (2003). https://doi.org/10.1523/JNEUROSCI.23-22-07993.2003

(13) Miura, K., Mainen, Z. F. & Uchida, N. Odor representations in olfactory cortex: distributed rate coding and decorrelated population activity. Neuron 74, 1087-1098 (2012). https://doi.org/10.1016/j.neuron.2012.04.021

(14) Leong, A. T. et al. Long-range projections coordinate distributed brain-wide neural activity with a specific spatiotemporal profile. Proc Natl Acad Sci U S A 113, E8306-E8315 (2016). https://doi.org/10.1073/pnas.1616361113

(15) Chan, R. W. et al. Low-frequency hippocampal–cortical activity drives brain-wide resting-state functional MRI connectivity. Proc Natl Acad Sci U S A 114, E6972-E6981 (2017). https://doi.org/10.1073/pnas.1703309114

(16) Leong, A. T. L. et al. Optogenetic fMRI interrogation of brain-wide central vestibular pathways. Proceedings of the National Academy of Sciences 116, 10122-10129 (2019). https://doi.org/10.1073/pnas.1812453116

(17) Leong, A. T. L., Wang, X., Wong, E. C., Dong, C. M. & Wu, E. X. Neural activity temporal pattern dictates long-range propagation targets. Neuroimage 235, 118032 (2021). https://doi.org/10.1016/j.neuroimage.2021.118032

(18) Leong, A. T. L., Wong, E. C., Wang, X. & Wu, E. X. Hippocampus Modulates Vocalizations Responses at Early Auditory Centers. Neuroimage 270, 119943 (2023). https://doi.org/10.1016/j.neuroimage.2023.119943

(19) Wang, X. et al. Functional MRI reveals brain-wide actions of thalamically-initiated oscillatory activities on associative memory consolidation. Nat Commun 14, 2195 (2023). https://doi.org/10.1038/s41467-023-37682-8

(20) Xie, L. et al. Brain-wide resting-state fMRI network dynamics elicited by activation of single thalamic input. Nat Commun 16, 11247 (2025). https://doi.org/10.1038/s41467-025-66104-0

(21) Li, A., Gong, L. & Xu, F. Brain-state-independent neural representation of peripheral stimulation in rat olfactory bulb. Proc Natl Acad Sci U S A 108, 5087-5092 (2011). https://doi.org/10.1073/pnas.1013814108

(22) Lang, J. et al. Odor representation in the olfactory bulb under different brain states revealed by intrinsic optical signals imaging. Neuroscience 243, 54-63 (2013). https://doi.org/10.1016/j.neuroscience.2013.03.057

(23) Chery, R., Gurden, H. & Martin, C. Anesthetic regimes modulate the temporal dynamics of local field potential in the mouse olfactory bulb. J Neurophysiol 111, 908-917 (2014). https://doi.org/10.1152/jn.00261.2013

(24) Wachowiak, M. et al. Optical dissection of odor information processing in vivo using GCaMPs expressed in specified cell types of the olfactory bulb. J Neurosci 33, 5285-5300 (2013). https://doi.org/10.1523/JNEUROSCI.4824-12.2013

(25) Hudetz, A. G., Vizuete, J. A. & Pillay, S. Differential effects of isoflurane on high-frequency and low-frequency gamma oscillations in the cerebral cortex and hippocampus in freely moving rats. Anesthesiology 114, 588-595 (2011). https://doi.org/10.1097/ALN.0b013e31820ad3f9

(26) Joliot, M., Ribary, U. & Llinas, R. Human oscillatory brain activity near 40 Hz coexists with cognitive temporal binding. Proc Natl Acad Sci U S A 91, 11748-11751 (1994). https://doi.org/10.1073/pnas.91.24.11748

(27) Murthy, V. N. & Fetz, E. E. Oscillatory activity in sensorimotor cortex of awake monkeys: synchronization of local field potentials and relation to behavior. J Neurophysiol 76, 3949-3967 (1996). https://doi.org/10.1152/jn.1996.76.6.3949

(28) Tallon-Baudry, C., Bertrand, O., Delpuech, C. & Pernier, J. Stimulus specificity of phaselocked and non-phase-locked 40 Hz visual responses in human. J Neurosci 16, 4240-4249 (1996). https://doi.org/10.1523/JNEUROSCI.16-13-04240.1996

(29) Murakami, M., Kashiwadani, H., Kirino, Y. & Mori, K. State-dependent sensory gating in olfactory cortex. Neuron 46, 285-296 (2005). https://doi.org/10.1016/j.neuron.2005.02.025

(30) Wilson, D. A. & Yan, X. Sleep-like states modulate functional connectivity in the rat olfactory system. J Neurophysiol 104, 3231-3239 (2010). https://doi.org/10.1152/jn.00711.2010

(31) Schreck, M. R. et al. State-dependent olfactory processing in freely behaving mice. Cell Rep 38, 110450 (2022). https://doi.org/10.1016/j.celrep.2022.110450

(32) Gao, P. P., Zhang, J. W., Chan, R. W., Leong, A. T. L. & Wu, E. X. BOLD fMRI study of ultrahigh frequency encoding in the inferior colliculus. Neuroimage 114, 427-437 (2015). https://doi.org/10.1016/j.neuroimage.2015.04.007

(33) Gao, P. P., Zhang, J. W., Fan, S. J., Sanes, D. H. & Wu, E. X. Auditory midbrain processing is differentially modulated by auditory and visual cortices: An auditory fMRI study. Neuroimage 123, 22-32 (2015). https://doi.org/10.1016/j.neuroimage.2015.08.040

(34) Goddard, E. & Mullen, K. T. fMRI representational similarity analysis reveals graded preferences for chromatic and achromatic stimulus contrast across human visual cortex. Neuroimage 215, 116780 (2020). https://doi.org/10.1016/j.neuroimage.2020.116780

(35) Friston, K. J., Harrison, L. & Penny, W. Dynamic causal modelling. Neuroimage 19, 12731302 (2003). https://doi.org/10.1016/s1053-8119(03)00202-7

(36) Friston, K. J., Kahan, J., Biswal, B. & Razi, A. A DCM for resting state fMRI. Neuroimage 94, 396-407 (2014). https://doi.org/10.1016/j.neuroimage.2013.12.009

(37) Bernal-Casas, D., Lee, H. J., Weitz, A. J. & Lee, J. H. Studying Brain Circuit Function with Dynamic Causal Modeling for Optogenetic fMRI. Neuron 93, 522-532 e525 (2017). https://doi.org/10.1016/j.neuron.2016.12.035

(38) Zeidman, P. et al. A guide to group effective connectivity analysis, part 1: First level analysis with DCM for fMRI. Neuroimage 200, 174-190 (2019). https://doi.org/10.1016/j.neuroimage.2019.06.031

(39) Salimi, M. et al. Disrupted connectivity in the olfactory bulb-entorhinal cortex-dorsal hippocampus circuit is associated with recognition memory deficit in Alzheimer's disease model. Sci Rep 12, 4394 (2022). https://doi.org/10.1038/s41598-022-08528-y

(40) Chen, Y. N., Kostka, J. K., Bitzenhofer, S. H. & Hanganu-Opatz, I. L. Olfactory bulb activity shapes the development of entorhinal-hippocampal coupling and associated cognitive abilities. Curr Biol 33, 4353-4366 e4355 (2023). https://doi.org/10.1016/j.cub.2023.08.072

(41) Pellegrino, R., Sinding, C., de Wijk, R. A. & Hummel, T. Habituation and adaptation to odors in humans. Physiol Behav 177, 13-19 (2017). https://doi.org/10.1016/j.physbeh.2017.04.006

(42) Sinding, C. et al. New determinants of olfactory habituation. Sci Rep 7, 41047 (2017). https://doi.org/10.1038/srep41047

(43) Zhao, F. et al. fMRI study of olfaction in the olfactory bulb and high olfactory structures of rats: Insight into their roles in habituation. Neuroimage 127, 445-455 (2016). https://doi.org/10.1016/j.neuroimage.2015.10.080

(44) Zhao, F. et al. fMRI study of the role of glutamate NMDA receptor in the olfactory adaptation in rats: Insights into cellular and molecular mechanisms of olfactory adaptation. Neuroimage 149, 348-360 (2017). https://doi.org/10.1016/j.neuroimage.2017.01.068

(45) Sengupta, P. The Laboratory Rat: Relating Its Age With Human's. Int J Prev Med 4, 624-630 (2013). 

(46) Quinn, R. Comparing rat’s to human’s age: How old is my rat in people years? Nutrition 21, 775-777 (2005). https://doi.org/10.1016/j.nut.2005.04.002

(47) Burwell, R. D. & Amaral, D. G. Perirhinal and postrhinal cortices of the rat: interconnectivity and connections with the entorhinal cortex. J Comp Neurol 391, 293-321 (1998).

(48) Kajiwara, R., Takashima, I., Mimura, Y., Witter, M. P. & Iijima, T. Amygdala input promotes spread of excitatory neural activity from perirhinal cortex to the entorhinal-hippocampal circuit. J Neurophysiol 89, 2176-2184 (2003). https://doi.org/10.1152/jn.01033.2002

Reviewer #2 (Public review):

Summary:

Overall, the authors aimed to provide evidence that clarifies two debates within metacognition research concerning subjective confidence reports:

(1) Does the post-decision confidence report arise from the same process that drives the initial decision, or does a separate, independent process support confidence computation?

(2) How do we stop accumulating evidence for the post-decision confidence report? Is it based on a self-imposed time limit, or on accumulated evidence crossing a boundary?

For the investigation, the authors constructed four models (2 × 2 factorial) to compare each combination of processes to account for random-dot motion tasks data with speed/accuracy manipulations. The models are generally embedded in the drift diffusion model framework, retaining basic parameters such as drift rate, boundary separation, starting point, and non-decision time, while adding linearly collapsing boundaries to model the initial choice. For the single vs. distinct process dimension, the difference lies in whether post-decision evidence accumulation is referenced to the endpoint of the initial decision process or restarts from a new, freely estimated starting point. For the time- vs. boundary-based stopping rule dimension, the key difference is that post-decision evidence accumulation stops either at a deadline sampled from a normal distribution or when the accumulated evidence hits a collapsing boundary.

Based on model comparison, the boundary-based stopping rule clearly outperformed the time-based stopping rule. However, models with the boundary-based stopping rule performed similarly regardless of whether a single or distinct process was used. Here, the authors drew additional insights from EEG recordings during the task, focusing on the centro-parietal positivity (CPP), which has been proposed as a neural correlate of the evidence accumulation process. By simulating evidence accumulation trajectories (with additional assumptions) and comparing the patterns of those trajectories with observed ERP waveforms, the authors argued that the single-process model provided a better match to the CPP findings and was therefore preferred. This was specifically demonstrated by the model's superior ability to match the pre-response CPP amplitude differences conditioned on the post-decision confidence-related variables.

Strengths:

(1) The authors translated existing theories into computational models of decision-making and systematically compared different cognitive processes by assessing model fits to the data. This provides strong evidence supporting the idea that post-decision confidence reports could be better explained by boundary crossing rather than a self-imposed deadline to respond.

(2) Beyond model evidence, an important result is that CPP amplitude predicted confidence before the initial choice was reported, which is a unique prediction of the single-process model. The use of EEG as an independent validation measure provided additional evidence in favour of this model.

(3) Combining points 1 and 2, this study successfully addressed the two key debates with solid evidence to favour one theory over another.

(4) Another strength of this study is the data quality. The high number of trials provided a strong foundation for model inference as well as ERP analysis. The experiment also contained a speed-accuracy manipulation to evaluate model performance across diverse situations.

Weaknesses:

I have two main concerns around the modelling work and neural analyses, which in my opinion could have limited the interpretation of the findings. My responses here will be lengthier, but this reflects the nature of the modelling work rather than implying stronger criticisms than those suggested by the strengths discussed above.

(1) There are a few assumptions in the models that lack psychologically meaningful interpretations, and this study placed more effort into model comparison while lacking discussion of the cognitive processes inferred from parameter estimates.

To start, I think some of the parameterisations were not properly justified. For the boundary models, it is not very clear why the upper and lower boundaries were different and collapsed at different rates for confidence decisions, given that a single boundary parameter and collapse rate were used for the initial decision. This allows more flexible shifts in the model's predictions of confidence ratings without strong justification. Specifically, it is unclear why the boundary-single model has such an implementation while the boundary-distinct model was only equipped with one boundary parameter (a2, compared to a2up and a2down).

Similarly, the inclusion of metacognitive noise creates another layer of flexibility in the predictions of confidence ratings. In most existing evidence accumulation models with a diffusion process, noise comes from two sources: within-trial noisy evidence accumulation and across-trial variability (e.g., drift rate variability). Beyond these, such models almost always assume that the decision is made deterministically once the evidence reaches a specific boundary. The inclusion of metacognitive noise here sounds more like a noisy decision-to-action mapping.

I also have similar doubts about allowing the non-decision time parameter for confidence accumulation in the distinct model to be negative. The authors argued that confidence accumulation may begin during initial evidence accumulation. However, this is a flawed implementation, as the non-decision time was simply added to the evidence accumulation time rather than being incorporated within it. Allowing negative non-decision times may achieve similar predictions, but it is ad hoc.

The inclusion of a collapsing boundary mechanism in the post-decision confidence accumulator helped the model reach more diverse levels of accumulated evidence and ultimately improved predictions of confidence ratings. However, no strong argument is presented for this implementation beyond the observation that the model performs worse without it. The collapsing boundary mechanism has traditionally been interpreted as reflecting a sense of urgency. For the boundary models, I noticed that the collapse rate of the upper boundary differed significantly between speed and accuracy conditions, which is consistent with the urgency interpretation. Overall, I would like to see more discussion of the specific model mechanisms included by the authors, interpreted in light of parameter estimates.

(2) While the ERP findings provided external evidence and validation of the modelling results, I find the simulation practices not particularly useful and potentially misleading for naive readers. Specifically, the authors attempted to draw a parallel between patterns of simulated evidence accumulation traces and observed CPP waveforms. While the CPP has received support as a correlate of the evidence accumulation process, the DDM is by no means a neural model capable of generating predictions of neural observations. To my understanding, the superior fit of the boundary-single model was primarily due to the fact that pre-response CPP amplitude predicts post-decision confidence ratings. Therefore, as the boundary-distinct model did not connect the two phases of evidence accumulation, it would fail to account for this observation. I think this point could be clearly demonstrated without the need to introduce additional assumptions into the model simulations in order to directly compare averaged trajectories with averaged ERP waveforms. While the authors did not explicitly claim otherwise, this approach creates an illusion that the model can mechanistically account for ERP data. I would like the authors to provide explicit clarification on this point.

Appraisal:

Overall, the authors have provided solid evidence in support of their research aims. The findings contribute to longstanding debates with insights from model mechanisms and neural findings that should not be overlooked by future studies on this topic. This study also offers a good starting point for future model development and refinement in broader contexts of confidence reporting, such as paradigms involving simultaneous initial decisions and confidence judgements. The high quality of the behavioural and EEG data will make a valuable contribution to future research.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Strengths:

This manuscript has many strengths, including a clever study design, thoughtful integration of multiple neurocognitive measures, and a set of rigorous and technically sophisticated analyses, which reveal a large set of relationships among the measures and behavior. The findings demonstrating brain/physiology-behavior relationships are particularly important, in that they point to potential functional consequences of MPES.

We thank the reviewer for noting these strengths of the work along with the below encouragement to revise the manuscript to better highlight the key findings and their implications.

Weaknesses:

The technical proficiency and complexity of the study and analysis also present a clear limitation and challenge for interpretation. As a reader, even those who are quite knowledgeable about the methods, constructs, and questions being addressed will often struggle (as this reviewer did) to keep the large set of findings in mind and gain an understanding of how they all fit together.

Indeed, it seems like there are many threads running together in the paper, which makes it challenging to find the through-line of the key findings, or to understand how they might relate to some pre-existing hypotheses, rather than merely interesting patterns detected in the data. In the Introduction and Discussion, it seems as if the key question is to understand the pathways by which MPEs impact cognition, but this is a rather broad topic, so it is not clear exactly what the authors are aiming at with this question and study design.

As an example, authors operationalize frontal theta power as an index of cognitive control demand, and one of the pathways by which MPEs impact cognition. But this point becomes somewhat circular, since it is not clear how or why the Mismatch x Strength interaction in frontal theta reflects that demand. It would have been better to set this pattern up in the Introduction as a theoretically driven hypothesis, since it currently appears more like a post-hoc interpretation. This is mirrored by how the issue is first brought up in the Introduction, where it states somewhat vaguely: "whether MPEs are followed by an increase in frontal theta... warrants closer examination".

Again, we appreciate the reviewer’s thoughtful feedback on where the manuscript can be clearer, especially given the rich set of results it reports. Following the reviewer’s guidance, we restructured and revised the Introduction to further motivate the hypotheses that (a) MPEs increase both attention/arousal (grounded in studies of Event Segmentation Theory) and cognitive control (given findings on reward prediction errors and other types of prediction errors), and (b) there are greater increases in these processes triggered by strong compared to weak MPEs. To better link these hypotheses to resulting statistical tests, we note that hypothesis (a) was tested in our trial-level regression models in Fig. 1 by examining main effects of Strength, whereas hypothesis (b) was tested in our models in the Mismatch x Strength interactions. On point (b) and potentially circularity, we note that previous work indicates that frontal theta scales with negative reward prediction errors; as such, we hypothesized that stronger MPEs would elicit more frontal theta, as evidenced by a robust Mismatch x Strength interaction during the probe period.

Later in the results, there are findings relating frontal theta to pupil dilation, posterior alpha suppression and then subsequent memory. It was hard to understand how all the findings might be linked together functionally or conceptually. Are the authors potentially postulating a mediating or mechanistic pathway, in which the MPE leads to increased cognitive control (frontal theta), which then leads to enhanced subsequent memory of those events? If this is the case, then maybe a formal path analysis would be the best way to test or state this hypothesis. It would also be useful to specify more clearly how the pupil components and alpha suppression factor into this mediating path, since it was not clear.

Relatedly, the authors suggest that internal attention and arousal also play relevant roles in this pathway, but these are also not clear. In some cases, it is stated as if this is a distinct pathway from the cognitive control one, since there is a focus in the results on the independence of frontal theta and posterior alpha, but elsewhere they seem to be treated as two aspects, or distinct steps, within a single pathway. Again, these different threads of the findings were quite challenging for the reader to follow. Pathway analyses, such as with multiple mediation or moderated mediation, could be a useful way to address this question. For example, it seems as if readiness-to-remember is another behavioral outcome (like subsequent memory) that could be used in the search for mediators.

We thank the reviewer for highlighting these ambiguities in the original submission and for the thoughtful encouragement to leverage mediation models to more formally test the hypothesized relationships between MPE magnitude and constructs of control, attention, and arousal. In the revision, we now more clearly hypothesize that the effects of strong MPE-driven increases in attention and arousal might be explained, in part, by cognitive control (as indexed by frontal theta) upregulating attention and arousal. To more explicitly test this model of the relationships between our measures, as recommended by Reviewer #1, we now include multivariate mediation analyses to assess whether, at a trial-level, changes in posterior alpha and the immediate pupil effect PC3 are explained in part by increases in frontal theta. Because changes in posterior alpha following MPEs and PC3 scores did not predict subsequent memory, mediation analyses addressing the hypothesis that our attention/arousal measures mediate the effect of frontal theta on subsequent memory were not conducted. Following insights from a cross-correlation analysis, as recommended by Reviewer #2, we tested an additional model to examine whether the effects of MPE magnitude on frontal theta were explained in part by changes in posterior alpha. Examination of the posterior distributions of the indirect effects did not favor our hypothesized model, nor the alternative model that attention upregulates control. Altogether, these outcomes suggest that increases in control, attention, and arousal following strong MPEs may be elicited independently. Yet, we also note that the current set of experiments may be underpowered for these mediation analyses; future work can further investigate the directionality between these effects. Finally, with respect to the readiness-to-remember findings, they were removed in the interest of space, as recommended by Reviewer #2.

At the minimum, it would be quite helpful to have diagrammatic figures that specify the hypothesized and observed relationships between independent variables (Strength, Mismatch), physiological indices (pupil dilation components, frontal theta, posterior alpha) and key outcome measures (accuracy, RT, next-trial retrieval success, subsequent memory), so that the reader can refer back to them as each component of the analyses is conducted.

To further increase conceptual clarity, we also followed this helpful suggestion, adding diagrammatic figures to illustrate our hypotheses regarding interactions between the effects (Fig. 3a) and to summarize the observed relationships between MPEs, control, attention, and arousal (Fig. 6).

Minor Points:

Many figures had x-axes showing a pupil component or EEG power metric broken down by quartile or quintile. Yet nowhere is it ever explained why this graphical (or analytic?) approach is used and what it reflects, or how it is decided which break down to use (quartile/quintile). If the data are analyzed as a correlation, why is a scatterplot not shown instead?

In the linear mixed effects models, continuous values were used to assess relationships between variables. In the figures, the continuous variables were binned into quartiles or quintiles for ease of visualization. We opted to visualize the data using this approach, rather than with a scatterplot, given the large number of trials. We updated the figure captions to clarify the approach.

It was surprising that, unlike readiness-to-remember, which was analyzed via logistic regression and odds-ratio, subsequent memory was not analyzed in the same fashion (i.e., as a binary outcome variable predicted by frontal theta), rather than in a reverse chronological one (subsequent memory predicting frontal theta). Historically, it was the case that subsequent memory was analyzed in this manner, but that was before the era in which trial-level linear mixed-effect models were in wide usage, as they are implemented in this study. Thus, the choice seems like a wasted opportunity or a step backwards analytically.

We thank the reviewer for this encouragement and agree with the point. In the revision, we note that the readiness-to-remember results were removed in the interest of space and clarity, as was recommended by Reviewer #2. With respect to the subsequent memory analyses, they are now analyzed via logistic regression.

Reviewer #2 (Public review):

Strengths:

The study has a clear behavioral paradigm with multiple measures - behavioral, EEG, and pupillometry that offer an investigation into different aspects of MPE response and memory.

The study is also very comprehensive in looking at multiple phases in processing MPEs: the prediction phase (prior to the violation), the response to MPEs, and subsequent memory of MPEs, all within one study. Specifically, the link between neural mechanisms and subsequent memory is a major advancement, as most prior studies did not include this component. Mechanisms underlying subsequent memory of MPEs are theoretically important, as a primary function of MPEs is to promote learning and memory. As the authors mention, the different neural and pupillary signals are not robustly correlated, suggesting multiple mechanisms underlying MPE detections, which is interesting, offers avenues for future research, and can facilitate a better theory of how MPEs are processed in the brain. Finally, the decomposition of pupil response into different components and their correlation with behavior (RT during match/MPE detection) is interesting.

We thank the reviewer for noting these strengths of the work along with the below encouragement to revise the manuscript to better highlight the key findings and their implications.

Weaknesses:

The methods are rigorous, and the claims are mostly supported by the data, but there are a few weaknesses or places that could be improved:

(1) The authors conduct PCA analysis to identify different components of the pupillary response to MPE and relate them to behavior. Specifically, the authors identify components PC3 and PC4, which they interpret as related to MPE. However, some parts of the interpretation could be clearer or better justified:

(a) The authors refer to PC4 as "post-decision cognitive processing". But, given that RT was between .5-.7s, and PC3 peaked after more than 1s, wouldn't it be cautious to interpret PC3 as postdecision as well?

Thank you for raising this point. Given that pupil is a relatively sluggish response, it is possible that both components reflect post-decision cognitive processing, even if PC3 peaks before PC4. Following the reviewer’s guidance to adopt more cautious language, we replaced “post-decision” with “post-MPE”.

(b) MPEs overall elicit longer RTs in this study, suggesting that long RT is a behavioral marker of MPE. Nonetheless, the authors argue on p. 12: "Altogether, these findings indicate that when stronger mnemonic predictions (as indexed by shorter RTs) were violated." And, PC3 is correlated with shorter RTs for mismatches, meaning that behaviorally, these trials were more similar to matches. Thus, how do the authors interpret shorter versus longer RTs for MPEs, and what processes do these RT reflect?

We thank the reviewer for stressing the need for greater clarity regarding the relationships between RT and the constructs of interest. With respect to RT, we interpret the condition-level difference in RTs between mismatch and match trials as a behavioral marker of an MPE. However, when comparing mismatch trials within a given strength condition to each other (i.e., an analysis at the trial-level), shorter RTs may reflect a stronger prediction, greater certainty that the probe is a mismatch, and therefore the experience of a stronger MPE. Note that while larger PC3 scores were associated with shorter RTs for mismatches (Fig. 2b, right), the mismatch RTs in the largest PC3 quartile were still longer than those on match trials in the corresponding quartile (in other words, there was still a condition-level difference in RTs in the largest PC3 quartile, suggesting that the mismatch trials in this bin are behaviorally still likely to be different from match trials in the corresponding bin).

To clarify these relationships and our interpretation, we modified the referred to text: “(as indexed by shorter strong mismatch RTs).” Moreover, we added text to the Discussion, further delineating our reasoning here and the implications of our findings for understanding the mechanisms giving rise to and triggering by MPEs of varying strengths. This includes adding an explicit summary of the logic and findings that notes that, at the trial-level, shorter RTs may reflect stronger predictions; at the match/mismatch condition-level, longer RTs may reflect the experience of a MPE. For PC3, shorter RTs (trials with a stronger prediction) in the Strong Mismatch condition were associated with a larger pupillary response. The added text notes that “while longer mean RTs for mismatches compared to matches are a behavioral marker of a MPE, within-condition differences in RTs (i.e., between mismatch trials) may reflect more subtle differences in MPE magnitude, with shorter RTs reflecting stronger predictions and thus stronger MPEs. Strong mismatch RTs were used in the mediation models as a proxy measure of MPE magnitude; this estimate may be noisy because RTs in this experiment are likely sensitive to factors independent of mnemonic prediction strength (e.g., preparatory attention (Supplementary Fig. 6) or memory strength of the mismatch probe). This limitation may have additionally reduced sensitivity to detecting indirect effects.”

(2) The brain to pupil relationship (p. 13-14): If I understand correctly, this was done on a trial-by-trial basis, but the high temporal resolution allows doing the analysis in a time-resolved manner - does brain activity at a certain time point preceding/following the pupil response correlate with the pupil response? It might be that cognitive control influences attention mechanisms or vice versa (because there is some overlap in the response). Although not testing causality, this temporally resolved correlation would be an interesting way to start probing how signals might influence each other.

Thank you for this suggestion. We now report a cross-correlation analysis (Fig. 3d) that suggests that cognitive control increases precede attention decreases at retrieval, whereas in response to a strong MPE, cognitive control increases follow attention increases. There were no significant clusters for the temporal relationships between frontal theta and pupil, nor for posterior alpha and pupil.

(3) The relationships the authors find between brain measures and pupil components were largely not specific to mismatches/matches. However, are they specific to this task? I think it would benefit the paper to show that these relationships are potentially specific to making match/mismatch memory decisions, versus, e.g., any stimulus processing. For example, the authors could run the same analyses locked to stimuli in the study phase, anticipating a different pattern, if indeed these findings are specific to the associative memory task.

Many of the associations between our measures indeed did not show an interaction with Mismatch. Due to jitter in the ISI in the study phase, some of the analyses in the retrieval phase cannot be performed in the exact same way for the study phase. We will leave these questions to be addressed in future research. We agree that an important question for future research is to address whether these responses depend on making match/mismatch decisions and now include consideration of this point in the Discussion: “Finally, the magnitude of observed increases in control, attention, and arousal following strong MPEs may be influenced by the decision-making process engaged when making match/mismatch judgments. Not all MPEs necessitate behavioral responses. Whether similar magnitudes in neurocognitive responses and consequences for learning are observed upon detection of an MPE, but in the absence of a decision remains unclear.”

(4) During memory retrieval (i.e., before the probe), the authors find that frontal theta, a marker of cognitive control, was associated on a trial-by-trial basis with more posterior alpha (i.e., less alpha suppression, potentially reflecting less attention), and that this association was stronger for weaker predictions. The authors interpreted this as weaker predictions necessitating more cognitive control, and that more cognitive control was recruited specifically in trials where retrieval included less content (memory reinstatement) to attend to. Generally, cognitive control is recruited to facilitate memory retrieval. If so, one possible interpretation is that this correlation reflects cognitive control effort that has failed to produce enough memory reinstatement. The other possibility is that this correlation reflects more specific retrieval of the correct probe, without retrieval of interfering items (i.e., overall less content). I believe that the former explanation predicts that this correlation would be associated with longer RTs (more difficult decisions), while the latter predicts shorter RTs (easier decisions due to successful retrieval), at least for matches.

Thank you for these insightful comments. Because this analysis is not key to the main questions about MPEs and given both reviewers’ concerns that the manuscript can be overwhelming for the reader given the sheer number of findings reported, we opted to move this point from the main text to the Supplement. However, following the reviewer’s guidance here, we conducted the proposed analyses and tested these alternative accounting by modeling RTs. The results favour the former interpretation:

“Greater control being associated with less attention could reflect failure in controlled retrieval efforts to reinstate sufficient memory evidence of the probe and thus fewer retrieval products to which attention is allocated. Alternatively, greater cognitive control could increase the likelihood of retrieval success, eliciting selective retrieval of the correct probe and inhibition of interfering items. To address these alternatives, we examined how the association between frontal theta and posterior alpha related to the difficulty of a trial, as assayed by RTs. The former failure-of-control account would predict that a stronger positive frontal theta- posterior alpha association would relate to longer RTs, whereas the greater-retrieval-specificity account would predict that a stronger positive association would relate to shorter RTs. In a model predicting RTs as a function of frontal theta, posterior alpha, Strength, Mismatch, and their interactions, we found a two-way frontal theta × posterior alpha interaction (β=0.016, CI=[0.001, 0.031], p=0.033), such that a stronger positive association between frontal theta and posterior alpha predicted longer RTs. This relationship did not differ as a function of Strength (no frontal theta × posterior alpha × Strength interaction: β=-0.015, CI=[-0.033, 0.004], p=0.124), Mismatch (no frontal theta × posterior alpha × Mismatch interaction: β=-0.016, CI=[-0.050, 0.018], p=0.342), or interact with Strength and Mismatch (no frontal theta × posterior alpha × Strength × Mismatch interaction: β=0.024, CI=[-0.014, 0.062], p=0.218). Together, these outcomes support the idea that during memory retrieval, positive coupling between frontal theta and posterior alpha may reflect failure or inefficiency of cognitive control efforts to rapidly accumulate mnemonic evidence to which to attend in support of a memory decision.”

(5) In section 3, the authors found a positive relationship between alpha during memory retrieval and PC3 during MPE. If I understood correctly, this means that less attention during retrieval (less suppression) is correlated with a stronger PC3 response. How do the authors interpret this? Maybe along the same lines as in (5), specifically retrieving the correct information (i.e., less retrieved content to attend to) means a stronger prediction, leading to a stronger MPE, and a stronger MPE response, as reflected by PC3?

We appreciate this comment, as it highlights a need for greater clarity here. The observed relationship was actually negative (Fig. 4f), meaning that more attention during retrieval was associated with a stronger PC3 response. We suspect that the lack of clarity here may be due to the original statement that “there was a positive relationship between posterior alpha suppression during memory retrieval [and PC3 scores]”. To increase clarity, we have modified this statement to “there was a negative relationship between posterior alpha during memory retrieval [and PC3 scores]”. We interpret the negative relationship with posterior alpha (i.e., positive relationship with posterior alpha suppression) to indicate “that greater attentional allocation during memory retrieval, which occurs when memories are stronger and more retrieval products can be reinstated and attended to (Fig. 1e; Fig. 4c), predicts the magnitude of immediate pupil responses to MPEs.”

(6) The results with subsequent memory are important and address a major gap in the field that largely did not relate neural effects of MPE to subsequent memory. However, one major limitation of the study is that the authors did not test memory for matches. I understand the logic of avoiding testing matches. Because matches were repeated more times in the study, it's not a fair comparison, and could change participants' overall criterion for old/new decisions. However, one possibility would have been to test only the weak prediction; this could have given some specificity to the neural subsequent memory findings.

We were indeed concerned about the change in decision criterion and did not include match items for this reason. Nonetheless, this is a useful suggestion that future work could include the weak match items for a better comparison of subsequent recognition memory. We now comment on this in the Discussion: “Whether control-associated enhancements in learning are specific to learning from MPEs can be further tested in future work by including a test of subsequent memory for weak match probes as an additional control condition for comparison.”

(7) The authors nicely characterized the different PC of pupillary MPE response. But, with respect to subsequent memory, they only present pupil size. Unless there is some methodological reason that prevents testing subsequent memory on the PC, I think this will be very informative about the potential mechanisms underlying memory of MPE.

The pupil PCs were not associated with subsequent memory, though there are some interesting trends in the 48-delay condition which could be explored in future work. These findings are now reported in the Supplement (Supplementary Fig. 16).

(8) This paper includes many interesting findings, and I am not sure how they all come together into a cohesive mechanistic understanding of MPE response and subsequent memory. I think the paper would benefit from either a conceptual mechanism figure or, in the Discussion, have a summary of a proposed mechanism integrating the findings together.

We thank the reviewer for stressing this point, which also was raised by Reviewer #1. To better emphasize the novel contributions of the work and to assist the reader’s understanding of the key findings, we: (a) revised the Introduction to more explicitly describe our hypotheses about the relationships among our measures as they relate to MPE responses and subsequent memory; (b) now report mediation models to more directly test these relationships and include diagrams of the hypothesized relationships; and (c) include a schematic figure at the end of the Results to highlight the key mechanistic relationships supported by the data.

(9) Relatedly, the section "Immediate, strength-sensitive neurocognitive impacts of MPEs" does not link the arguments to specific data points, so it's hard to follow which data specifically the authors are interpreting.

The discussion in this paragraph rests on the Strength × Mismatch interactions observed in Figures 1d-f, summarized in the first sentence of the section. To increase clarity, we changed the title of this section to “Neurocognitive impacts of MPEs are strength-sensitive”.

(10) If I understand correctly, the authors did not find improved memory for strong compared to weak MPE. First, I think this behavioral result should be incorporated in the main paper and in the interpretation of the results. Second, given that the neural effects the authors tested either correlated with memory for strong MPE or did not show a relationship with memory, what neural/pupil response could explain memory for weak MPE?

Thank you for raising these points. The behavioral result and the frontal theta trial-level regression model for subsequent memory are now described in the main results and included in the Discussion. As noted in the Discussion, the trial-level regression model indicates pre-probe and post-MPE frontal theta effects may explain memory for weak (and strong) mismatch probes. While the magnitude of probe-period MPE frontal theta is additionally predictive of memory for strong mismatch probes (as indicated by the Subsequent Memory × Strength interaction in the trial-level regression model in Fig. 5c and the logistic regression in Fig. 5b), frontal theta during this period does not additionally enhance memory for strong mismatch probes above that of weak mismatch probes (Fig. 5a). We added more discussion on why memory for strong and weak mismatch probes in the current experiment did not differ. We also discuss potential directions for future research to further probe mechanisms underlying MPE-driven learning.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

It is recommended that the authors determine whether formal path analyses, testing for mediation and moderation, would provide a useful approach from which to better integrate the disparate set of findings and make clear their causal/functional implications.

At a minimum, adding a diagrammatic figure is recommended to visually depict the key components of the study (independent variables, physiological indices, outcome measures) and how they relate to each other both conceptually (ideally in a theoretically hypothesized manner) and in terms of the observed findings. Such a figure will help the reader keep track of the many types of findings and results threads, and with the goal of better organizing the results into a clearer narrative through-line.

Thank you for the suggestions to add mediation analyses and diagrammatic figures. To more formally address our hypothesis that increases in attention/arousal following MPEs are explained in part by increases in cognitive control, we tested two mediation models: one with posterior alpha as the measure of attention and the other with pupil PC3 scores. We now diagram this hypothesis in Fig. 3a. Given the outcomes of the cross-correlation analysis suggested by Reviewer #2, we also tested an additional model where posterior alpha might explain the impact of strong MPEs on frontal theta (now diagrammed in Fig. 3e). We did not find credible evidence for an indirect effect in any of the models, suggesting that strong MPE-driven increases in control, attention, and arousal may be elicited independently. Finally, in a newly added summary diagram (Fig. 6), we highlight the observed effects of strong vs. weak MPEs on RTs, control, attention and arousal; differences in control, attention, and arousal for strong vs. weak predictions preceding the MPE; trial-level mismatch-specific or strong-specific effects on subsequent memory; and mismatch-specific interactions between processes during retrieval and responses to MPEs. We hope these revisions address Reviewer #1’s concerns and that these figures help the reader keep track of the key hypothesized relationships and main findings.

Reviewer #2 (Recommendations for the authors):

(1) The relationship between event segmentation and prediction errors has been reviewed recently in two papers (Nolden et al., 2024, Neuroscience & Biobehavioral Reviews; Rouhani et al., 2024, JOCN for a potentially relevant computational model). I wonder if insights from these papers can inform the Introduction/Discussion of the current manuscript.

Thank you for these suggestions. These papers are now incorporated into the Introduction and the Discussion.

(2) Brod et al. (2022, Psych. Bull. Rev.) have previously reported increased pupil dilations for MPE correlating with subsequent memory, specifically for strong prediction errors. I think it's worth including this paper in the Introduction as the finding is highly relevant. The Brod paper might provide more direct evidence of "MPE-related increases in pupil size" than the evidence the authors provide (p. 3).

Thank you for this suggestion. This paper is now incorporated into the Introduction and Discussion.

(3) I'm confused about the temporal analysis: "Trial-level regression analyses were conducted on the frontal theta, posterior alpha, and pupil time series from the associative retrieval test to identify temporal clusters that were sensitive to the factors of Mismatch (i.e., mismatch vs. match probes) and/or Strength (i.e., strong vs. weak associative pairs). For each participant and each time point, a linear regression model testing main effects of Mismatch and Strength, and a Mismatch × Strength interaction was run using R to compute beta weights for each regressor." What regression exactly was run? A separate model for each participant and time point? Across trials, then? Later, the authors mention that beta weights were averaged across participants and t-tests and permutation tests were conducted. However, if the data were averaged, what t-test was conducted? And how was the permutation test conducted? It's also unclear what the authors mean by "the sign of each participant's beta weights" - what sign?

Thank you for raising this point. A regression was run separately for each participant and each time point, across trials: neurocognitive measure ~ Mismatch + Strength + Mismatch: Strength. Beta weights were averaged only for visualization; t-tests were conducted on each set of beta weights (across participants), separately for each time point. We modified the text of the Methods to describe our procedure more clearly.

(4) The associative memory and recognition accuracy data are presented as d'. In addition, the authors should provide hits and false alarms to facilitate a better interpretation of the results.

We now report these outcomes in Table 1 and refer to them in the main text.

(5) The authors argue regarding the frontal theta that "Qualitatively, the main effect of Strength emerged later than the main effect of Mismatch, suggesting that the increase in frontal theta evoked by the probe was more sustained for weak compared to strong trials (or, as a corollary, that the greater control elicited by strong MPEs enabled more rapid resolution of conflict and ultimate choice selection)." It was unclear to me how that stems from the data.

This statement has been removed altogether.

(6) Especially in Figure 1, I think clarity can be improved if the authors would indicate the specific subsection they are referring to in the text, because even within, e.g., 1d, there are different graphs, so mentioning which graph is relevant for which statement would be helpful to the reader.

Thank you for this suggestion for improving the clarity of the manuscript. Fig. 1d-f includes multiple parts because we wanted to show the raw data (the mean time series on the left) as well as the model coefficients (time series on the right). We are hopeful that, given that each subplot is titled and that the main text refers to both the subplots on the left and on the right, this will be clear to the reader as is. We welcome further guidance if this remains a concern.

(7) This seems highly speculative to me: "Elevated PC4 scores on weak hits, where no error was made, may instead reflect retrieval practice and thus internally oriented attention. On these trials, when cueelicited retrieval may have been weaker, the probe may have provided additional support for pattern completion of the learning episode for that association, and this engagement in memory retrieval may have elicited pupil dilation (c.f., Strength effect in Figure 1f). Overall, PC4 may therefore reflect an attentional orienting response that, depending on the relative success of memory retrieval and probe identity, may direct attention internally or externally. " (p.13). In my opinion, the authors make a lot of assumptions about underlying processes. I'd consider removing.

We removed this text.

(8) In Figure 3c, should the x-axis be PC3 quintile? And (c) is not in the figure caption.

Thank you for this note. We addressed these issues.

(9) The carryover effects the authors report are interesting, but they seem detached, and it is unclear how they fit with the additional findings. In a paper that already includes many findings, I'd recommend either integrating better or removing.

Following this guidance, we removed the readiness-to-remember findings in the interest of space and clarity.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

"Learning is a fundamental source of individuality," by Manna and colleagues, interrogates different sources of variation in individual behavior. The authors place individual flies in a Y-shaped arena, which is a common design in the field, and illuminate the arms of the Y with blue versus green light. They track the color preference of individual animals and also perform operant conditioning, meaning that they teach the fly to avoid a particular color/arm by generating a foot shock when the fly enters that arm. There are a number of things that are impressive about this setup: The authors are able to collect data on thousands of individual flies of many different strain backgrounds, and they demonstrate a strong change in color preference after conditioning. This is nice, because in past papers, visual learning ability has been modest and difficult to study. To put a number on it, in this paper, animals on average don't show a color preference at the start of the assay, spending around 30% of their time in the one arm illuminated green, and the remaining time in the two arms illuminated blue. After conditioning, the average animal spends only 23% of its time in the green arm.

The authors run 64 animals through the assay for each of 88 wild-type strains (maybe? see Major Point 1 below) and see considerable strain-specific (genetic) variation in the change in time spent in the shocked color after conditioning. Some strains show no learning, while others spend <10% of their time in the shocked color after conditioning. They also, I believe, see that some strains have more variability across individuals, which would suggest that some strains have stronger canalization at the development or circuit function level than others, i.e., some genotypes produce more consistent copies of the individual, others less consistent copies. (Or, some genotypes produce robust circuits, and others produce noisy circuits.)

Finally, the authors argue statistically that learning itself increases variability in individual performance. This makes a lot of sense to me intuitively. Learning changes the physical/chemical properties of circuits in the brain, and because it evolves over time and interacts with environmental variables, it seems like it should send different animals down different channels. Or, at a conceptual level, if I learn to play the piano and my sister doesn't (because of some genetic difference between us or something stochastic), this learning experience will cause all sorts of other differences in our behavior as time passes. I also think the authors do have enough data to be able to make this finding. However, the presentation of the argument in this portion of the paper is hard for me to understand, and I am not an expert in statistics, so the strength of the result is difficult for me to evaluate.

Major points

(1) It's difficult to track through the paper the number of animals tested for different assays. At the beginning, it says N=5632, which works out to 64 flies for each of the 88 DGRP strains. 64 happens to be the number of parallel Y arenas they have. Later in the methods, there's a description of more variation within the set of 64 for each strain, two different parent sets per strain, different sexes, conditioned and unconditioned. And, while the results text focuses on the color learning, the methods discuss additional assays (place learning, multi-day learning).

Given the numbers, does each run of the 64 mazes include all the tested flies of one strain, or are flies of many strains included in each batch? Do different flies do different assays (color, place, multi-day), or do they all do all the assays? Perhaps there is a table including this information already in the supplement, but I recommend making it much clearer in the main results text and methods. While the dataset is large, if it is split over many conditions and/or if batch and genotype confound each other, this will affect the robustness of the results and how strong the conclusions can be.

(2) The data presentation in Figure 1 is elegant and easy to follow, but getting into Figure 2 and subsequently, I get lost in the statistics and have trouble understanding what is being measured. My understanding of the big picture is that while genetics and individual randomness contribute a lot to behavior, the evidence for learning as an amplifier of individuality is that variance in behavior among animals of the same strain increases over time in the conditioned group (i.e., the group that is doing the most learning, or a specific kind of learning), but not in the control group. This idea is illustrated in the flattening distributions in the cartoons in Figure 1A. The authors should include graphs of the real data that use the same format as in that cartoon. Instead, the graphs present "residuals," and I don't know what those are. I suspect it's "variation left over after accounting for effects of strain and individual stochasticity." I see the residuals being tracked per strain over time in Figure 2H, but I don't see the change over time in other graphs. I'm looking for something simple like, "variation within the strain at the beginning of learning and at later time points in learning." (But I'm not sure exactly what instantaneous measurement would be the focus in longitudinal analyses of learning behavior.)

(3) Figure 3 is a cool stab at tracking down the precise mechanism by which a stochastic environment interacts with learning to send individuals along different behavioral routes. But again, like in Figure 2, I don't have the sophisticated understanding of statistics to understand exactly what the graphs are telling me, or how they relate to the underlying measurements. I'm relying on the results text alone to reach a conceptual understanding, and just taking the graphs on trust.

So, overall, the authors have a very nice body of work here, and with the potential to add a new facet to our understanding of the origins of diversity in animal behavior. In addition to the interpretations they focus on here, this dataset also represents an advance in studying visual associative learning in general, and quite an amazing ability to make longitudinal measurements of many behavioral decisions within the same animals. Improving the data presentation to make it easier to follow for a larger swathe of researchers, especially in figures 2 and 3, will increase its potential impact.

Reviewer #2 (Public review):

Summary:

The authors set out to test the extent to which differences in learning capacity and experience contribute to behavioural variation in a genetically identical population under identical environmental conditions.

Strengths:

The authors developed and used a scaled-up version of a simple two-choice behavioural paradigm, allowing them to test thousands of individuals across multiple genotypes. They then deployed clever and powerful statistical analysis methods and provided compelling evidence for a role of variability in learning in the expression of behavioural variation.

Weaknesses:

There are no major weaknesses, although some level of longitudinal analysis to strengthen the evidence for a strict definition of individuality would be a welcome extension of a future study. In addition, it would have been very interesting, although understandably beyond the current scope, to delineate a potential source of learning variability in the brain.

Following our provisional response to the reviewers, we have implemented these additions to the manuscript:

(1) We have added 7 additional tables (Table 1-6 and table 8) to the supplementary that detail how many individual flies were used in which of the seven separate experiments, how the individuals were distributed across genotypes, replicates and sexes, and how many were filtered out before the final analysis. At the bottom of each table, we added a short description of the type of experiment and a brief explanation of the filtering. The four smaller experiments where we tested the two mutant lines and one wild-type DGRP line were used primarily to test and validate the experimental platform and the behavioural paradigm used for the main experiment. In these four experiments we tested green place learning, blue place learning, green colour learning, blue colour learning in four separate batches of flies. In each of these experiments we used 192 individuals (64 individuals x 3 genotypes x 4 experiments = 768 individuals in total). In the multiday experiment we used 64 flies per genotype per each of the four groups of sequences of learning paradigms, in total 512 individual flies. Here, each of these 512 individuals were retested in different learning paradigms over 4 days (Table 5). The main experiment was the green place learning (Table 6) where we tested all 88 DGRP lines and again the two mutant lines was used to obtain the majority of the main results and conclusions (64 individuals x 90 genotypes = 5760 individuals). Lastly, additional 896 individuals were measured in the experiment using blue place learning paradigm to test the consistency of learning behaviour as opposed to colour bias within genotype (Table 8). In summary, in all experiments, we have always measured behaviour in 64 flies per genotype (full loading of the behavioural platform), and they were distributed almost entirely evenly across replicates, sexes, and conditions (control vs conditioned). No individual was reused across experiments. In most cases, after filtering the data, 60 or fewer individuals were used in final analyses. For the very few deviations from this experimental design (which occurred due to unforeseen events such as dropped/sick vials, flies flying away or accidentally squished during setup, skewed number of males and females etc.) we added a short explanation in the text below the tables. In total, across all reported experiments in this study, we measured behaviour in 7936 individuals.

(2) We have added a schematic visual representation of classical measurement of individuality (variance of the distribution of behaviour within genotype where genetically identical individuals are raised in the same environment), entropy-based measurement of individuality (residual individuality) and the change in residual individuality, as we use them in this study (Figure 2D). We also provide a list of different DH_resid measures and what distributions are being compared across the DH_resid in the same figure. We hope this will serve as a more intuitive explanation of individuality and help readers interpret and follow more easily the results that we report after this figure.

(3) In the same vein, we added another schematic visual representation to Figure 3 (Figure 3F) where we depict how distributions of individual behaviour may change with every decision and how this change translates to (or can be read out from) the change in residual individuality. We have also renamed the X axis of Figure 3E to “DH_resid Start”, so that it is clearer what is measured here and matches the explanation in Figure 2D.

(4) We have added two additional supplementary figures where the reader can inspect in more detail how the distributions of individual behaviour change longitudinally across time for each genotype in control and conditioned (Figure 3 – Figure supplement 2 and  Figure 3 – Figure supplement 3). From these figures one can glance how variance as well as the shapes of the distributions change as the flies learn in the conditioned setting, and how they remain largely the same in the control where flies behave spontaneously. We have added a sentence in the main text to introduce these figures: “We found that the distributions of individual behaviour were broader and their shapes changed substantially over the course of the experiment for the conditioned flies, and not for the control flies Figure 3 - figure supplement 2, Figure 3 - figure supplement 3).”

(5) As noted in the first provisional response to reviewers, we changed the sentence “In every individual, behaviour is shaped by deterministic, genetic factors and by environmental events throughout lifetime, which may be stochastic and can occur at the molecular, cellular, organismal and even population scales.” to “In every individual, behaviour is shaped by fixed genetic factors and by variable environmental events throughout lifetime, which may be stochastic and can occur at the molecular, cellular, organismal and even population scales.”

(6) Some sentences were edited in the results so that we can correctly refer to the newly added tables and figures. Context, meaning or interpretation of the results in these sentences was not altered.

(7) While adding the new table references to the text, we noticed a typo that propagated in the previous version where the number of flies used in the main experiment was stated to be N= 5238, when in fact it should have been N=5239. This is now fixed.

We once again thank the reviewers for their comments and suggestions – we believe their suggestions helped us improve the presentation and interpretability of our study and we hope the reviewers and readers will agree with this as well.

Author response:

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

eLife Assessment

This important study provides evidence that plateau pikas, at moderate densities, can facilitate yak nutrition by suppressing a poisonous plant, offering a helpful perspective on reciprocal interactions between small mammal ecosystem engineers and large herbivores. The evidence is solid, supported by a manipulative field experiment and appropriate measurements of intermediary ecological processes, although some claims about density dependence, competition, and stress-gradient mechanisms are not fully supported by the experimental design. The work will be of interest to ecologists, conservation biologists, and rangeland managers, particularly those studying grassland herbivore interactions and livestock management on the Qinghai-Tibetan Plateau.

Thank you very much for these positive assessments of our work. Below, we provide point-by-point responses to the comments from the two peer reviewers, and we hope these revisions are satisfied by you and the reviewers.

Reviewer #1 (Public review):

Summary:

This is important and significant work because it helps describe the complexity of interactions between system components where two herbivores interact with vegetation. Whereas other studies have shown that the larger ungulate (yaks, Bos grunniens, in this case) can facilitate the abundance and population growth of the smaller (the semi-fossorial lagomorph, Ochotona curzoniae, plateau pika hereafter), this study flips the tables and shows that, at least under some conditions, moderate densities of the plateau facilitate the nutritional condition of yaks.

The study was not designed to investigate the reasons that pikas clip Stellera chamaejasme. That said, based on other studies and general knowledge of the ecology of these pikas, it is likely that they clip (although do not eat) this plant because its relatively large size hinders predator detection. This species of pika does better where vegetation height is low than where it is higher.

Strengths:

Notably, the strong inference the authors can claim for their results is supported by the careful experimental design. A weaker paper would have simply noted correlations between pika burrow density and yak feeding efficiency without experimental removal. This paper, to its credit, not only used experimental removals but also documented the various intermediary results that support the ultimate conclusions. The statistical approaches used appear to be appropriate. (Readers are encouraged to read the full Materials and Methods, which are available in the Supplementary Materials section.)

We appreciate these positive comments on our work.

Weaknesses:

Although the study was well designed and executed, and its conclusions appear strongly supported, readers interested in the management implications of the Qinghai-Tibetan Plateau should be mindful of its limitations. First, the study site, at approximately 3,200 m elevation, was relatively low by Qinghai-Tibetan Plateau standards. Stellera chamaejasme becomes less common at elevations > 4,000 m, where a majority of livestock grazing occurs. Thus, it would be instructive to learn, through follow-up studies, whether similar facilitation occurs where unpalatable (and mildly poisonous) species in such genera as Astragalus, Oxytropis, and Thermopsis replace S. chamaejasme as the problematic plant for pastoralists.

Thank you for this suggestion. We have acknowledged this limitation in the Discussion by adding the paragraph below (see the Third point):

“Despite of these, several questions deserve further investigation. First, our study examined pika–yak interactions only during the summer period, when food resources are most abundant. Whether such facilitative effects weaken or even shift toward competition under more stressful conditions—for example, when forage becomes limited during autumn or winter—remains to be tested. Second, if the documented facilitation of yak nutrition by pikas prompts herders to increase yak densities, could the resulting rise in livestock herbivory push pika populations beyond the levels observed here, potentially toward the threshold where facilitation gives way to competition? Third, our study site is located at approximately 3,200 m elevation, relatively low by Qinghai-Tibetan Plateau standards. Stellera becomes less common at elevations > 4,000 m, where a majority of livestock grazing occurs. It would be instructive to learn, through follow-up studies, whether similar facilitation occurs where unpalatable (and mildly poisonous) species in such genera as Astragalus, Oxytropis, and Thermopsis replace Stellera as the problematic plants for pastoralists (Lu et al., 2012; Li and Zhao, 2025). Finally, it is unclear whether similar facilitation as observed here applied to the other principal livestock species in the area, such as domestic sheep and goats.”

See these revisions in Line 272-286 in the Discussion section.

Second, the authors make no mention of wild ungulates, so it is unclear what, if any, role they may have played in this system. At least one study in Qinghai Province, albeit at a slightly higher elevation, showed that not only pikas, but also Tibetan gazelles (Procapra picticaudata), which were commonly observed on grazed pastures, grazed more frequently on some dicots avoided by domestic sheep than did the livestock themselves (Harris et al. 2015).

Citation:

Harris RB, Wang, WY, Badinqiuying , Smith AT, Bedunah DJ (2015) Herbivory and Competition of Tibetan Steppe Vegetation in Winter Pasture: Effects of Livestock Exclosure and Plateau Pika Reduction. PLoS ONE 10(7): e0132897. doi:10.1371/journal.pone.0132897

Thank you for this suggestion. We have added more details about the study site, particularly regarding wild ungulates, in the Methods section. Specifically, we have included the sentence of “Wild ungulates, such as Tibetan gazelles (Procapra picticaudata) (Harris et al., 2015), and other small mammals such as rabbits and zokors, occur rarely in the area.”

See these revisions in Line 333-335 in the Methods section.

It would also be instructive to learn if similar facilitation as observed here applied to the other principal livestock species in the area, domestic sheep (which are often herded together with smaller numbers of domestic goats).

Thank you for the suggestion. We have acknowledged this limitation in the Discussion, by adding a paragraph as: “Finally, it is unclear whether similar facilitation as observed here applied to the other principal livestock species in the area, such as domestic sheep and goats.”

See these revisions in Line 284-286 in the Discussion section.

Finally, as suggested by this study, the interactions between all components of the system are complex and interactive. If pika facilitation of yak nutrition at the densities documented results in herders increasing yak density, might the increased herbivory from the domestic animals provide the conditions for the pika population to increase beyond the densities observed here, and thus toward the levels where facilitation yields to competition?

Thank you for your suggestion. We have acknowledged this limitation in the Discussion, by adding the paragraph as “Second, if the documented facilitation of yaks by pikas prompts herders to increase yak densities, could the resulting rise in livestock herbivory push pika populations beyond the levels observed here, potentially toward the threshold where facilitation gives way to competition (Yang et al., 2026)?”

See these revisions in Line 276-279 in the Discussion section.

Reviewer #1 (Recommendations for the authors):

Although no doubt a bit sensitive, it would have been better to reveal a bit more about how pikas were removed.

We have provided more details about how pikas were removed in the no-pika treatment, by adding “For the no-pika treatment, pikas were trapped once every two weeks using 30 live traps (25 cm high × 25 cm wide × 40 cm long) within each plot and relocated elsewhere in the study site.” in the Methods section. We didn’t recorded how many pikas were removed from the corresponding plots, so no data were available for this point.

See these revisions in Line 411-413 in the Methods section.

The authors also missed a few relevant papers worth citing, including Badingqiuying, R. B. Harris, and A. T. Smith. 2018. Summer habitat use of plateau pikas (Ochotona curzoniae) in response to winter livestock grazing in the alpine steppe Qinghai-Tibetan Plateau. Arctic, Antarctic, and Alpine Research 50 (1): e1447190

We have cited this key paper in Line 75 in the Introduction section.

Reviewer #2 (Public review):

Summary:

This study uses a combination of field sampling and manipulative experiments to test for facilitative impacts of pikas on yaks via suppression of a poisonous forb. The authors found that, when Stellera forbs were present, yak weight increases over the growing season were greater in the presence of pikas compared to in their absence. This occurred because, although pikas do not consume Stellera, they clip it and use it in nest/burrow construction, thereby decreasing its relative abundance in the plant community. Thus, overall, the study contributes to our understanding of how herbivores of different size classes indirectly affect each other via the use of shared resources.

Strengths:

It is well known that large herbivores on grasslands impact smaller animals, but the reciprocal interaction is rarely tested. Thus, this study asks a valuable question, and the experiment is well-designed to test it. The authors also do a good job of demonstrating the potential conservation impacts of their research.

We appreciate these positive comments on our work.

Weaknesses:

What the authors tested is really cool, but their claims go far beyond what they can say based on their experimental design. For example, the authors claim to show that pika impacts on yaks display density-dependent transitions from competition to facilitation. However, their experiment only looked at the presence (at moderate densities) and absence of pikas, and they only tested for facilitation, not competition.

The paper would also benefit from changes to the framing in the introduction and discussion. For example, the authors pitch the work as a test of the stress-gradient hypothesis. However, there is no abiotic stress gradient in the study, which is an essential component of the SGH. They also pitch the work in terms of density dependence, but there is no significant variation in population densities beyond the presence-absence binary. The paper would be stronger if they focused their framing around the literature on facilitative interactions across mammals of different size classes, especially indirect facilitation via use of shared resources, which is what this paper is really about.

We agree that our work had explored only the facilitative effects of pikas on yaks, rather than the Stress Gradient Hypothesis (SGH). Thus, we deleted the description on SGH. However, the finding of a humped relation between yak weight gains and pika burrow densities (Figure 3C) is very important which provides evidence that moderate densities of pikas has the best beneficial effects on yak growth. We added a separate paragraph in discussion to have a clear discussion.

We have made the major revisions below to address these concerns.

(1) We have revised the title into “Small mammalian herbivores at moderate densities facilitate livestock growth by improving vegetation composition in grasslands ”.

(2) We have deleted all the statements about facilitation and competition predicted by the SGH in the Abstract (Line 56-59), Introduction (Line 88-91), Discussion (Line 231-233, the whole paragraph about SGH was removed here), and the References sections.

(3) We added a paragraph in discussion (Line 248-259) to have a clear discussion on the humped relation between yak weight gains and pika burrow densities as “Because of the natural variations in pika density in the pika-present treatment, we were able to obtain a hump-shaped relationship between yak weight gains and pika burrow densities in these plots. Compared with the absence of pikas, the facilitative effect reached its maximum at approximately 200 burrows/ha but became competitive at densities exceeding 400 burrows/ha (Figure 3C). This result reveals that pika density modulates the net outcome for yak weight gain, with a facilitation peak at ~200 burrows/ha and a competition onset above 400 burrows/ha. Our findings offer empirical evidence for the non-monotonicity theory, under which the competition-facilitation balance varies with population density: facilitation dominates at low densities, competition at high densities, and these density-dependent shifts may underpin community stability and productivity (Zhang, 2003; Zhang et al., 2015). The theory further holds that the facilitation threshold, not the competition-facilitation transition, is the critical factor governing the stability of interacting species or communities (Zhang et al., 2015).”

Most importantly, there are inconsistencies in what is visualized in the figures compared to the model results. For example, the results section in several places notes a lack of significant interaction terms in the model but shows interactions in the p-values on the figures.

In the Results section, there are only two places where we discussed non-significant interactions: Line 175–177 “Pikas and Stellera had no interactive effects on abundance of sedges, forbs, and neutral detergent fiber (NDF) of total forage for yaks (Figure 3F, I and Appendix 1—figure 1, table 5,8).” and Line 190–192 “Pikas and Stellera had no interactive effects on yaks’ foraging efficiency on forbs (Appendix 1—figure 2, table 10).”.

We have cross-checked both the Results section and the Figures sections mentioned above, and confirmed that they are consistent now.

The authors also plot smoothed lines rather than their model results and then draw interpretations from those lines that cannot be tested in the models that they used.

Thank you for the suggestion. Now we have added the Appendix 1—table 3 and Appendix 1—table 7 for the model results of generalized additive models (GAMs) for Figure 2C and Figure 3C that plotted with smoothed lines in Appendix 1.

There are also missing details that are important for model interpretation, including the distributions used and the sample sizes.

We have provided the Appendix 1—table 13 to summarize all statistical models used in the study, including the distributions used and the sample sizes in the Appendix 1.

We have also added a sentence of “A summary of all statistical models used in the study is available in Appendix 1 table 13.” in Line 475-476 in the Statistical analyses section to indicate this information.

Another major concern with experimental design is in the forage nutrient analyses. The authors picked plants along a grazing trail, then measured nutrient content without standardizing based on plant species, so any differences across treatments could be because of what they happened to grab rather than overall forage quality.

We have revised this section to provide more details on how forage samples were collected and their quality were analyzed. Specifically, five forage samples were collected per grazing plot, focusing on the two dominant plant species—one sedge and one grass—that were most frequently grazed by yaks. To ensure comparability across plots and treatments, we mixed the two species at equal dry mass (5 g). We have revised this section as below.

“To assess forage quality, five forage samples were collected from each grazing plot to quantify their nutritive values. To obtain samples that reflect the forage actually consumed by yaks, we tracked the animals along their grazing paths and collected the plant tissues of the two most frequently consumed species: the dominant sedge Kobresia humilis and the dominant grass Elymus nutans (Figure 2B; Pan et al., 2019). The collected tissues of each species were dried in a forced-air oven at 60 °C for 48 h, then ground through a 1-mm mesh. Subsequently, 5 g of each dried and ground species were combined in a 1:1 dry mass ratio, and the resulting mixture was stored in plastic bags for subsequent analyses.”

See these revisions in Line 439-447 in the Methods section.

Reviewer #2 (Recommendations for the authors):

(1) Introduction

Line 53 - I wouldn't describe small mammals like rodents as keystone species. They can have strong impacts on ecosystems, but not disproportionate relative to population size, which is a key part of that definition. It may be true when you talk specifically about pikas later on, but not small mammals as a general category.

We have replaced this term with “consumers” here, see Line 63.

Lines 58-61 - Good hook

Thank you for this positive comment.

Lines 69-74 - I don't think the stress gradient hypothesis is the right pitch for this work. The SGH posits that facilitation increases with abiotic stress, but no abiotic stressors were measured in this study. Population density interacts with abiotic factors in the SGH, but population density in and of itself is not an abiotic stressor. The papers you cite here all look at the interaction between population density and abiotic stressors (e.g., water availability). So these lines set me up to expect a stress gradient in your experiment that didn't exist, then left me confused later on. It would be better to highlight the strength of your work (lines 70-76 pose interesting questions and predictions) rather than trying to make it fit within the SGH.

Thank you for pointing out this problem. We have deleted the statements about SGH here.

See these revisions in Line 88-91 in the Introduction section.

(2) Materials and Methods

Lines 498-509 - Did you verify beforehand that no plants within the enclosures had been grazed on? How did you know that the consumption or clipping was specifically from those pikas?

We have clarified here by adding “Before cage installation, we carefully checked the plants within each plot and removed those that had been previously grazed or damaged by herbivores.” in the Methods section. In this case, we made it sure that the consumption or clipping was specifically from those pikas with the cages.

See the revisions in Line 349-350 in the Methods section.

Lines 509-512 - I would be careful calling this preference. It's really just a record of what they consumed along paths they were walking, which could be about accessibility and convenience as much as preference.

We have replaced “diet preferences” with “diet composition” here, see Line 359 in the Methods section.

Line 514 - Clarify the specific question or hypothesis you're testing with this field survey, beyond just generally testing associations.

We have modified the sentences here as “In July 2021, we investigated the potential facilitation of pikas on yaks mediated by the poisonous Stellera forbs under unmanipulated field conditions in the study site.”.

See Line 365-366 in the Methods section.

Lines 532-534 - The intro for this paper sets it up to be about density-dependent movement from competition to facilitation, but the experiment here is set up to compare pika presence/absence. The framing of the paper needs to be adjusted to better align with this experimental design.

The same issue as mentioned above. We agree that our work had explored only the facilitative effects of pikas on yaks, rather than the balance between competition and facilitation as predicted by the Stress Gradient Hypothesis (SGH). However, the finding of a humped relation between yak weight gains and pika burrow densities (Figure 3C) is very important which provides evidence that moderate density of pika has the best benefical effect on yak. We added an separate paragraph in discussion to have a clear discussion about this point in the Discussion section.

We have made the major revisions below to address this concern.

(1) We have revised the title as “Small mammalian herbivores at moderate densities facilitate livestock growth by improving vegetation composition in grasslands”.

(2) We have deleted the statements about facilitation and competition and the SGH in the Abstract (Line 56-59), Introduction (Line 88-91), Discussion (Line 231-233, the whole paragraph about SGH was removed here), and the References sections.

(3) We kept the discussion on the humped relation between yak weight gains and pika burrow densities (Figure 3C). We added an separate paragraph in discussion to have a clear discussion about this point. For details, see Line 248-259 in the Discussion section.

Lines 566-569 - Why did you need to simulate pika clipping when you already had pika presence/absence treatments?

We conducted Stellera removal treatment by simulating poisonous plant clipping behaviors of pikas because we want to confirm that the shifts in abundance of this dominant poisonous plant species is the key mechanism in driving pika-yak facilitation in our system. If we simply looked the differences in yak weight gain in the pika presence/absence treatments, it should be difficult to secure the underlying mechanism. In addition to the reduction in abundance of the poisonous Stellera, pikas may cause a variety of shifts vegetation properties including plant productivity and diversity, and soil disturbances that can exert direct and indirect effects on yak foraging activities, and thus their weight gains.

Lines 566-569 - Is there another citation you can give showing that Stellera forbs taller than 20cm are both preferred by pikas and exert greater impacts on plant/animal communities? Those are big assumptions that need to be better supported or explained. If there was a logistical reason that you didn't remove all of the smaller forbs, that needs to be laid out as well.

We have added one new citation here to support this method here. We have revised this section as “To simulate the clipping behavior of pikas, we clipped only those Stellera forbs exceeding 20 cm in height. This threshold was chosen based on previous observations that pikas preferentially target large forbs of this size (Liu et al., 2009).”

Liu W, Zhang Y, Wang X, Zhao JZ, Xu QM, Zhou L. 2009. The relationship of the harvesting behavior of plateau pikas with the plant community (In Chinese). Acta Theriologica Sinica 29:40-49.

Also, we have deleted the sentence of “and can exert significant impacts on the plant community and on yak grazing behaviors (Z.Z., field observations)” mentioned above, because these patterns were observed only by the authors in the field and lack supporting data.

See these revisions in Line 419-422 in the Methods section.

Line 587 - sample size per treatment? Was it consistently one species that you measured, and if so, which one? If you collected different species or a mix of species across treatments, then you can't really compare the nutrient values because you haven't accounted for interspecific variation.

We have revised this section to provide more details on how forage samples were collected and their quality were analyzed. Specifically, five forage samples were collected per grazing plot, focusing on the two dominant plant species—one sedge and one grass—that were most frequently grazed by yaks. To ensure comparability across plots and treatments, we mixed the two species at equal dry mass (5 g).

We have revised this section as below:

“To assess forage quality, five forage samples were collected from each grazing plot to quantify their nutritive values. To obtain samples that reflect the forage actually consumed by yaks, we tracked the animals along their grazing paths and collected the plant tissues of the two most frequently consumed species: the dominant sedge Kobresia humilis and the dominant grass Elymus nutans (Fig. 2B; Pan et al., 2019). The collected tissues of each species were dried in a forced-air oven at 60 °C for 48 h, then ground through a 1-mm mesh. Subsequently, 5 g of each dried and ground species were combined in a 1:1 dry mass ratio, and the resulting mixture was stored in plastic bags for subsequent analyses.”

See these revisions in Line 439-447 in the Methods section.

Lines 603-613 - Please provide the dependent variables in each model, as well as any interaction terms, in addition to the random effects. Please also state explicitly what you were trying to test with each of these models.

There are two models that use the tweedie family (forb and sedge bite rate). Indeed, we need to include the tweedie power parameter to help understand the mixture of the three families. We have included the p-value (power) in the Appendix 1—table 13 in the Appendix 1. We chose to use tweedie because a normal gaussian family model fitted the results poorly.

We have added the Appendix 1—table 13 in the Appendix 1, which provides the summary of all statistical models used in the study, including response variables, model type, distribution family (with Tweedie power parameter where applicable), interaction terms, random effects structure, and sample sizes.

Also, we have added a sentence of “A summary of all statistical models used in the study is available in Appendix 1—table 13.” in Line 475-476 in the Statistical analyses section to indicate this information.

Lines 613-614 - Tweedie is a category of distributions that includes quite a few different options, including Gaussian, Poisson, and Gamma distributions, some of which are normal and some of which are not. So, justifying the use of Tweedie distributions in your model structure doesn't really make sense, and it doesn't really tell me which distribution each model pulled from. Please clarify specifically which distributions you used for each model and why.

We have now added the reason why we used Tweedie distributions by adding the sentence of “There were two models that used the tweedie family (forb and sedge bite rate). We chose to use tweedie because a normal gaussian family model fitted the results poorly” in Line 468-470 in the Statistical analyses section.

We have also included the p-value (power) for forb and sedge bite rate in the Appendix 1—table 13 in the Appendix 1.

Lines 615-618 - Provide citations for R packages described in the text.

We have provided all the related citations for all R packages described in the text, as listed below.

glmmTMB: Brooks, M. E., Kristensen, K., van Benthem, K. J., Magnusson, A., Berg, C. W., Nielsen, A., Skaug, H. J., Maechler, M., & Bolker, B. M. (2017). glmmTMB Balances Speed and Flexibility Among Packages for Zero-inflated Generalized Linear Mixed Modeling. The R Journal, 9(2), 378–400. https://doi.org/10.32614/RJ-2017-066

mgcv: Wood, S.N. (2017). Generalized Additive Models: An Introduction with R (2nd edition). CRC Press. AND Wood, S.N. (2011). Fast stable restricted maximum likelihood and marginal likelihood estimation of semiparametric generalized linear models. Journal of the Royal Statistical Society: Series B (Statistical Methodology), 73(1), 3–36. https://doi.org/10.1111/j.1467-9868.2010.00749.x

DHARMa: Hartig, F. (2022). DHARMa: Residual Diagnostics for Hierarchical (Multi-Level / Mixed) Regression Models. R package version 0.4.6. https://CRAN.R-project.org/package=DHARMa

tidyverse: Wickham, H., Averick, M., Bryan, J., Chang, W., McGowan, L.D., François, R., Grolemund, G., Hayes, A., Henry, L., Hester, J., Kuhn, M., Pedersen, T.L., Miller, E., Bache, S.M., Müller, K., Ooms, J., Robinson, D., Seidel, D.P., Spinu, V., Takahashi, K., Vaughan, D., Wilke, C., Woo, K., & Yutani, H. (2019). Welcome to the tidyverse. Journal of Open Source Software, 4(43), 1686. https://doi.org/10.21105/joss.01686

See these revisions in Line 472-475 in the Statistical Analyses section.

(3) Results

Line 127 - Somewhere in the intro or methods, describe what clipping is and why the pikas do it.

We have provided more details about the clipping behaviors of pikas by adding “Notably, pikas often clip (although do not eat) the wolf poison S. chamaejasmehas because its relatively large size hinders predator detection (Fan et al., 1998).” in Line 330-332 in the Methods section.

Line 128 - Change from "preferred" to "consumed greater proportions of"

See the correction in Line 146 in the Results section.

Line 136 - You measured yak weight once a month, so give the result in monthly weight gain rather than daily.

Here we preferred to keep the unit of daily weight gains (converted from monthly ones), as this is the standard presentation for livestock growth performance, also see Fig. 1 in Odadi et al., 2011 Science’s paper.

W. O. Odadi, M. K. Karachi, S. A. Abdulrazak, T. P. Young, Science 333, 1753–1755 (2011).

Lines 138-140 - The linear models, as you described them in the methods (lines 603-620), don't test for hump-shaped relationships. Please update the methods to explain how you tested the density relationship and how you got this interpretation.

The description for Figure 3C here showed estimates from a GAM (family: gaussian), and we did not use a linear model in this figure.

We have now added a new model summary Appendix 1—table 7 for this Figure 3C in the Appendix 1.

Line 145 - I don't think you can claim that the total available forage was more nutritious for yaks, as you picked plants that yaks happened to be chewing along a grazing path. You would need to take samples from a consistent set of plant species at random locations to make this claim.

Sorry for this confusion. We modified “the total available forage” as “the major available forage” here (see Line 172) because we collected the same forage plant species and analyzed their nutrients.

The same as mentioned above, to clarify the sampling methods, we have also revised this point in the Methods section to provide more detail on how forage samples were collected and their quality were analyzed. See these revisions in Line 439-447 in the Methods section.

(4) Discussion

Line 166 - Need to address inconsistency in how you talk about pika density. Here you talk about the impacts of pikas at moderate densities, which I think is a fair claim. Elsewhere, you talk about density-dependence, which I don't think you really measured, given that all your sampling was either in the absence of pikas or within a narrow window of densities that can all be categorized as moderate.

Done! As mentioned above, we have removed the term of “density-dependence” in the whole manuscript, but keep the term of “moderate density” in the Abstract (Line 56-59), Introduction (Line 88-91), Discussion (Line 231-233, the whole paragraph was removed here), and the References section.

Line 176-178 - This is a really cool finding.

Thank you for this positive comment.

Lines 179-181 - You didn't test competition between plant species, and you didn't measure light, soil moisture, or soil nutrients. So you can suggest competition as a potential mechanism, but you can't say definitively that's what is happening.

We now have lowered our tone here as “We speculate that these improvements in food availability and nutrition for yaks may be due to the release of grasses and sedges from competition with the forbs for limiting above- and below-ground resources”.

See the revision in Line 208-211 in the Discussion section.

Lines 184-186 - You did a good job of it here, suggesting a likely potential mechanism at play without claiming it is for sure happening when it hasn't been measured.

Thank you for this positive comment!

Lines 188-199 - Strong paragraph. The impacts of large herbivores on smaller animals are well-studied, but reciprocal impacts are often overlooked.

Thank you for this positive comment!

Lines 201-205 - You didn't test the stress gradient hypothesis because there was no abiotic gradient. You also did not take any measurements during outbreaks, so you cannot claim to have compared low-moderate to outbreak pika densities. I think the paper would be much stronger if you removed the stress gradient hypothesis and instead focused more on the literature around facilitation between mammals of different body sizes, as you do in lines 205-209.

We agreed that our work didn’t specifically design to test the stress gradient hypothesis (SGH) between pikas and yaks, so we have deleted this paragraph here, see Line 231-233 in the Discussion section.

Line 209-215 - Again, you didn't test a competition-facilitation balance because you never tested or demonstrated competition. One of the main strengths of this paper is demonstrating facilitation, so build on that strength rather than referencing things you didn't measure.

The same as mentioned above, we have deleted this paragraph here, see Line 231-233 in the Discussion section.

Lines 218-222 - Not an accurate description of the relationship between herbivore diet and body size. Larger herbivores typically tolerate lower-quality plants in order to consume sufficient calories, but plenty of them do this via mixed feeding. Grazing in large herbivores and livestock is usually due to specifics of the digestive tract (e.g., hindgut fermentation) rather than specifically about body size.

We have deleted this description of the relationship between herbivore diet and body size here. Instead, we have modified this statement as “The coexistence of a diverse of herbivore species with different diet selections and size classes can lead to an “compensatory effect” on grass and forb biomass that helps to maintain a balance and diverse plant community” in the Discussion section.

See these revisions in Line 234-237 in the Discussion section.

Lines 245-251 - Paragraph addresses an important point. Lines 247-249, though, overstate what you measured. There's no measurement of livestock production or biodiversity in the study.

We have replaced the term of “livestock production and biodiversity” with “livestock growth performance” here. See Line 288-298 in the Discussion section.

(5) Figures

Figure 2C-D - This applies to all figures, but you need to plot the best-fit line generated from your model instead of using geom_smooth, which is what these lines look like. You can do this using functions like predict or ggpredict. Using these smoothed lines implied non-linear relationships that you didn't actually test for.

We have redrawn Figures 2C and 2D to use model estimates directly and have included the related model summaries as Appendix 1—table 3 and table 4 in the Appendix 1.

Figure 3B - This figure doesn't show yak weight gain in the presence of pikas. Instead, it shows weight loss when pikas are absent. It's a subtle difference, but very important for interpretation. Yak can maintain weight just fine without pikas as long as Stellera are absent, too. Your results consistently show no Pika x Stellera interactions, but that doesn't match your significance values here. Need to double-check and explain that.

We have revised the descriptions for Figure 3 and 4 in the Results section, by emphasizing that the absence of pikas REDUCED weight gains of yaks, INCREASED toxic plant abundance, and REDUCED the quantity and quality of palatable grasses and sedges. We have revised these sections as below:

Abstract (see Line 51-53)

“Compared to the pika-present treatment, pika removal dramatically increased cover of the poisonous Stellera forbs by two-fold, reducing the abundance and protein content of palatable grasses and sedges, yak foraging efficiency, and yak weight gain by up to 42%.”

Results (see Line 153-167, Line 169-175, Line 184-192)

Also, we did find significant Pika x Stellera interactions for yak weight gains, we have provided these details in the Appendix 1—table 5 and table 6 in the Appendix 1.

(6) Recommendations

Lines 245-257 - Would recommend combining the last two paragraphs into one.

We have combined the last two paragraphs, see Line 288-298 in the Discussion section.

Line 530 - Can you replace large with a more precise measure of area?

We are unable to provide a more precise measure of area here, so we have deleted the description of “in a large area”, but we have also added the note of “in the study site” by the end of the sentence to better describe the location of the plots.

See the revision in Line 413 in the Methods section.

Line 541 - Does this mean +/- 7.8 standard deviations? If so, how big is that range in kg?

Here should be “115±7.8 kg”, we have done this correction in Line 392 in the Methods section.

Figure 3 - Would be helpful to use "Stellera/pika present" and "Stellera/pika absent" rather than saying "No Stellera/pika" since you also use the No. abbreviation for numbers a lot in this figure.

We have revised all the related Figures for this issue in Figure 3, 4, and Appendix 1—figure 1,2.

Figure 3F and I - Show letters for significance on these two plots as well, even if it is just a row of a's.

We have redrawn Figure 3F,I to address this issue.

Figure S1 - Applies to all boxplots. Be consistent about showing significance, even if it is a row of a's indicating no difference between treatments.

We have re-drawn Appendix 1—figure 1,2 to address this issue.

Table S1 - Something happened with the line numbers, so they are in the table instead of on the left side.

We have fixed this problem for Appendix 1—table 1 in the Appendix 1.

Table S1 - Applies to all tables. Include the type of model that you ran (including distribution if not Gaussian) in the table legend.

We have provided an summary of all statistical models used in the study in Appendix 1—table 13 in the Appendix 1.

Also, we have added a sentence of “A summary of all statistical models used in the study is available in Appendix 1—table 13.” in Line 475-476 in the Statistical analyses section to indicate this information.

Table S9 - This legend has a good description, including the type of model you used and what you were testing. Apply this more detailed legend to the rest of the tables.

Again! We have provided an summary of all statistical models used in the study in Appendix 1—table 13 in the Appendix 1.

Also, we have added a sentence of “A summary of all statistical models used in the study is available in Appendix 1—table 13.” in Line 475-476 in the Statistical analyses section to indicate this information.

Author response:

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

eLife Assessment

This important study provides new insight into the regulation of cell organization and division in Trypanosoma brucei through the control of a kinesin motor protein by a polo-like kinase. The authors present solid evidence from rigorous biochemical and imaging analyses showing that phosphorylation modulates kinesin function and cellular organization. However, direct in vivo evidence that PLK phosphorylates kinesin-G is lacking.

We performed experiments to investigate the effect of PLK inhibition on the phosphorylation of KIN-G in vivo in trypanosome cells by immunoprecipitation and mass spectrometry. The new results showed that treatment of trypanosome cells with GW843682X, a potent TbPLK inhibitor validated previously in procyclic trypanosomes, reduced the phosphorylation levels on Thr301 and Ser569 of KIN-G by ~27% and 100%, respectively. The partial reduction in Thr301 phosphorylation after GW843682X treatment could be attributed to slower dephosphorylation of phosphorylated Thr301 after GW843682X was added to the cell culture. Nonetheless, these new results demonstrated that KIN-G is an in vivo substrate of PLK.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript identifies the orphan kinesin KIN-G as a substrate of Polo-like kinase (TbPLK) in Trypanosoma brucei and demonstrates that phosphorylation of Thr301 inhibits KIN-G microtubule binding and disrupts its cellular function. Using a combination of in vitro kinase assays, phosphosite mapping, microtubule binding and gliding assays, and in vivo complementation with phosphomimetic and phosphodeficient mutants, the authors link TbPLK-mediated regulation of KIN-G to defects in centrin arm integrity, FAZ elongation, Golgi organization, flagellum positioning, and division plane placement. The study provides a mechanistic advance in understanding how TbPLK regulates centrin arm biogenesis and integrates KIN-G into the growing regulatory network controlling hook complex and FAZ assembly. Overall, the work is technically strong, internally consistent, and builds logically on previous studies from this group and others.

Strengths:

A major strength of the manuscript is the clear mechanistic link between phosphoryltion of Thr301 and loss of microtubule binding activity. The use of phosphomimetic (T301D) and phosphodeficient (T301A) mutants in an RNAi-rescue framework provides a clean and convincing demonstration of functional relevance in vivo. The integration of biochemical assays with detailed cell biological phenotyping (centrin arm length, FAZ elongation, basal body segregation, and cytokinesis markers) is particularly effective and makes the central conclusion robust. The observed phenotypic cascade from centrin arm defects to FAZ and division plane abnormalities is also well aligned with existing models of trypanosome morphogenesis.

Weaknesses:

My (more or less main) concern relates to the interpretation of the Golgi phenotype. The conclusion that phosphorylation of KIN-G "impairs Golgi biogenesis" is currently based on fluorescence microscopy using TbGRASP and Sec13 markers and on quantification of the number and distribution of Golgi/ERES puncta in binucleated cells. While these data convincingly demonstrate altered Golgi/ERES number and spatial organization, they do not distinguish between true defects in Golgi biogenesis or duplication and alternative possibilities such as fragmentation, vesiculation, or mislocalization of Golgi membranes. Given the central role of Golgi-centrin arm organization in the proposed model, ultrastructural analysis (for example, by EM or electron tomography) would greatly strengthen this aspect of the study by providing direct evidence for structural alterations of the Golgi and its association with the centrin arm and ERES. Such data would elevate this part of the manuscript from a descriptive fluorescence phenotype to a true structural cell biological insight. I appreciate that this experiment goes beyond the current dataset, but it would substantially enhance the mechanistic depth of the Golgi-related conclusions and strengthen the causal chain linking centrin arm defects to Golgi abnormalities. However, I have to confess, the inclusion of such data would make this reviewer particularly enthusiastic about the work. If this is not feasible, I would recommend tempering the wording of "Golgi biogenesis" to a more conservative description, such as altered Golgi organization or duplication, and explicitly acknowledging the limitations of fluorescence-based analysis for this conclusion.

Thanks for these very constructive comments, which are very well taken. We totally agree with this reviewer on these points. Since it is not feasible for us to perform EM or electron tomography, we have revised the manuscript to describe the effect of KIN-G phosphorylation on the Golgi as “altered Golgi duplication” rather than “Golgi biogenesis”. We also explicitly acknowledge the limitations of fluorescence-based analysis of the Golgi for this conclusion and suggest that further characterization with EM or electron tomography would allow one to reveal the potential structural alterations of the Golgi and its association with the centrin arm.

An additional conceptual point concerns the dual role of TbPLK in centrin arm regulation. TbPLK is known to promote centrin arm biogenesis through phosphorylation of TbCentrin2, yet in this study, TbPLK phosphorylation of KIN-G negatively regulates centrin arm assembly. This dual positive and negative regulatory role is intriguing but could be discussed more explicitly. The manuscript would benefit from a clearer conceptual framework addressing how phosphorylation of KIN-G might serve as a temporal or spatial switch to restrain KIN-G activity at specific stages of centrin arm assembly.

This is a great point. However, we are not sure whether the previous work on TbPLK phosphorylation of TbCentrin2 could lead to the conclusion that TbPLK promotes centrin arm biogenesis through phosphorylation of TbCentrin2. In the published work (de Graffenried et al., MBoC, 2013), trypanosome cells expressing the phospho-deficient mutant TbCentrin2-S54A only showed minor growth defects, exhibiting growth defects after 5 days (de Graffenried et al., MBoC, 2013). Cells expressing the phosphomimic mutant TbCentrin2S54D, however, showed very strong growth defects (de Graffenried et al., MBoC, 2013). The effects of TbPLK phosphorylation on TbCentrin2 appear to be quite similar to that of TbPLK phosphorylation on KIN-G, although the KIN-G-T301A mutant does not have growth defects (up to 5 days in our experiments). It appears that the primary role of TbPLK in regulating TbCentrin2 and KIN-G is negative regulation. Nonetheless, we have added more discussion on these regulatory roles of TbPLK in the revised manuscript.

Finally, a schematic model summarizing the proposed regulatory pathway from TbPLK phosphorylation of KIN-G to centrin arm assembly, FAZ elongation, division plane placement, and Golgi organization would aid the reader.

Thanks for this suggestion. We made a schematic model to summarize the roles of KIN-G and its regulation by TbPLK. This is included in Figure 8.

Reviewer #2 (Public review):

Summary:

The authors identify KIN-G as an in vitro substrate for phosphorylation by TbPLK and show that several of the in vitro P-ated sites, including T310, overlap with P-ation sites seen in live cells. The authors further show that PLK-mediated P-ation inhibits KIN-G binding to microtubules in vitro, as does a KIN-G-T301D mutant, and that expression of a KIN-G-T301D Phospho-mimic in T. brucei phenocopies KIN-G RNAi knockdowns, producing defects in cell division, morphogenesis of the centrin arm, FAZ and other cellular structures, as well as a misplaced cytokinesis furrow.

Understanding cytoskeletal rearrangements that drive cell division in T. brucei is an important and unresolved problem, so the work addresses important questions that are of great interest. PLK and KIN-G have previously been shown to be important for cell division and morphogenesis of cytoskeletal structures that drive cell division in T. brucei. The current work advances our understanding by suggesting a potential mechanism by which PLK and KIN-G might participate, namely through PLK-dependent P-ation to control KIN-G MT binding activity.

Strengths:

The authors use a rigorous combination of biochemistry, phosphoproteomics, cell biology, and mutant analysis to support their conclusion that PLK-mediated P-ation of KIN-G negatively regulates KIN-G microtubule binding, and this may explain the observation that a KIN-G T301 phosphomimic mutant blocks cell division and perturbs biogenesis of cytoskeletal structures that drive cell division and morphogenesis. Combining rigorous and informative in vitro studies with mutant analysis in live cells is a great strength. The work is solid and important, though a few pieces are needed to fully connect the in vitro findings with the in vivo observations, as detailed below.

Weaknesses:

Overall, I find this work to be solid and to provide an important addition to our understanding of mechanisms controlling cell division in T. brucei. The biochemistry, in particular, is rigorous and convincingly demonstrates PLK can P-ate KIN-G, altering its MT-binding ability. Analysis of phospho-mutants of KIN-G in live T. brucei supports the conclusion that P-ation of KIN-G at T301 negatively affects KIN-G function in vivo. I think, however, that the results fall short of supporting the title, because, although the data convincingly show that PLK can phosphorylate KIN-G at T301 in vitro, and that T301 is P-ated in vivo, they do not formally demonstrate (nor even test) whether PLK is the kinase responsible for this phosphorylation in vivo (experiments to address this seem quite feasible). I also do not see where the authors try to reconcile the absence of phenotype for KIN-G-T301A with the implied importance of KIN-G phosphorylation by PLK in cell division, which calls into question the need for P-ation of KIN-G-T301 in cell division. Suggestions for addressing these concerns are provided below.

My two main questions are:

(1) What is the biological relevance of KIN-G P-ation at T301?

(a) The authors report no defect for the KIN-G-T301A mutant, so what then is the need for T301 P-ation, if the cell gets along fine without it? One step toward addressing this would be to ask what fraction of KIN-G shows P-ation at T301. Although published studies indicate P-ation at T301, it isn't known what percentage of KIN-G in the cell is P-ated. One might anticipate, for example, that T301-P is a small minority of the population in asynchronous cultures and that T301 P-ation increases at specific cell cycle stages.

This is a great point that is very well taken. We also had been puzzled by the observation of no growth defects of T301A mutant. This comment enlightened us. From the new experiments we performed to compare the phosphorylated peptides of KIN-G in cells treated and non-treated with the PLK inhibitor GW843682X, we calculated the percentage of phosphorylated Thr301 in non-GW843682X-treated cells. We found that the percentage of peptides containing the phosphorylated Thr301 is ~14% of the total Thr301-containing peptides (Fig. 1H). This result indicates that T301-P is indeed a small minority of the population in the asynchronous trypanosome cells. It is possible that T301 phosphorylation may occur at a specific cell cycle stage such as early S-phase, during which PLK and KIN-G co-localize at the centrin arm.

(b) Published work links PLK to cell division, FAZ elongation, etc.. The current work suggests that one role of PLK is to P-ate KIN-G at T301. In contrast, however, the current work also indicates that P-ation of KIN-G at T301 is unnecessary for normal cell division, FAZ elongation, etc..

Yes, previous work discovered essential roles of TbPLK in basal body segregation, centrin arm biogenesis, FAZ elongation, and cytokinesis. These functions of TbPLK correlate with TbPLK’s localization to multiple subcellular structures, the basal body, the centrin arm, and the new FAZ tip, and are attributed to the regulation of its substrates at these structures. At the basal body, TbPLK phosphorylates SPBB1, which is required for basal body segregation. Defects in basal body segregation can lead to defective flagellum positioning and FAZ elongation. At the new FAZ tip, TbPLK regulates the cytokinesis regulator CIF1, which is required for cytokinesis. At the centrin arm, TbPLK phosphorylates TbCentrin2 at S54 and KIN-G at T301 (and S569, which was newly identified as an in vivo TbPLK site and has not yet been characterized). However, cells expressing TbCentrin2-S54A have very weak growth defects, and cells expressing KIN-G-T301A have no detectable growth defects. In contrast, cells expressing TbCentrin2-S54D and cells expressing KIN-G-T301D have strong growth defects. Therefore, the essential role of TbPLK in centrin arm biogenesis apparently is not attributed to the phosphorylation of TbCentrin2 and KIN-G. It is possible that phosphorylation of other centrin arm-localized protein(s) by TbPLK may be essential for centrin arm biogenesis, but this possibility remains to be explored.

(c) Some experiments or at least commentary on points a and b above would strengthen the paper.

We performed experiments and presented the data in Fig. 1H. We also included commentary in the revised manuscript on the points about the potential role of T301 phosphorylation. Thanks for these great comments that significantly improved the manuscript.

(2) Is PLK the kinase that P-ates Kin-G T301 in vivo?

(a) The authors show PLK P-ates T301 (and other residues) in vitro, and that T-301 is P-ated in vivo. To bring the analysis full circle, it would be informative to examine KIN-G P-ation in a PLK mutant or upon inhibition of PLK with published inhibitors. This seems to be a very doable experiment with the tools available.

We treated trypanosome cells with a potent PLK inhibitor GW843682X, which was previously demonstrated to inhibit TbPLK activity in vitro and mimic TbPLK knockdown in vivo in trypanosomes, and immunoprecipitated KIN-G for mass spectrometry. We compared the KIN-G peptides identified by mass spectrometry from trypanosome cells treated with or without GW843682X, and found that two phosphosites (T301 and S569) were reduced by ~27% and 100%, respectively, after GW843682X treatment (Fig. 1G). These results provided evidence to support that TbPLK phosphorylates KIN-G in vivo.

Reviewer #3 (Public review):

Summary:

Here, the authors investigate the role of the Trypanosoma brucei polo-like kinase TbPLK in the function of flagellum-associated cellular structures in trypanosomes. They set out to test the hypothesis that a key substrate of TbPLK is the kinesin protein KIN-G, and that TbPLK phosphorylation of KIN-G regulates its functions in cells.

Strengths:

Using in vitro biochemistry with purified proteins, the authors convincingly demonstrate that TbPLK phosphorylates KIN-G at 29 sites. Moreover, they convincingly show that phosphorylation at one site, T301, impairs the binding of purified KIN-G to purified microtubules. Using immunofluorescence-based imaging approaches, they also show that TbPLK colocalizes with KIN-G at centrin arms during the early S-phase of the cell cycle. Centrin arms are structures that are located near the basal body and flagellum and are important for new flagellum biogenesis, Golgi positioning, and cell division. To evaluate the function of KIN-G phosphorylation in cells, they depleted KIN-G by RNAi, simultaneously expressed phospho-mimetic (T301D) and phospho-ablative mutant proteins, and used immunofluorescence to examine the impact on flagellum-associated cellular structures. They show that expression of the phospho-mimetic mutant KIN-G-T301D causes the following defects: reduced cell proliferation, disruption of centrin arm and Golgi biogenesis, impairment of FAZ elongation and flagellum positioning, and misplacement of the cell division plane. The data convincingly support the conclusion that KIN-G phosphorylation on T301 plays an important role in regulating the cellular functions of this kinesin motor protein.

Weaknesses:

Some of the broader conclusions are not directly supported by the data. For example, the title states "Polo-like kinase phosphorylation of the orphan kinesin KIN-G negatively regulates centrin arm biogenesis in Trypanosoma brucei," but the data do not directly address the specific role of TbPLK in phosphorylating KIN-G in cells. Moreover, some of the more specific conclusions in the paper, for example, that "phosphorylation of KIN-G" causes various cellular defects, are a bit of an overstatement. The supporting data rely on the expression of a phospho-mimetic mutant of KIN-G. Presumably, phosphorylation in cells is a normal part of KIN-G regulation, and it is not just phosphorylation, but rather hyperphosphorylation that is being mimicked by the mutant. Some rewording of the specific conclusions is warranted, and the broader conclusion would be better supported with additional experimental evidence.

This is a great point that is very well taken. We performed new experiments to address the in vivo phosphorylation of KIN-G by TbPLK. We treated cells with a potent PLK inhibitor, GW843682X, and then immunoprecipitated KIN-G for mass spectrometry to identify changes in phosphorylation. We found that the phosphorylation levels of T301 and S569 were reduced by ~27% and 100%, respectively, confirming that these two sites are in vivo TbPLK phosphosites.

We also calculated the ratio of phospho-T301 versus non-phospho-T301 in non-treated cells and found that phospho-T301 accounts for ~14% of the total KIN-G protein. This new result suggests that it is the hyperphosphorylation that causes growth defects. We have revised the manuscript accordingly to reflect this point.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Several statements use rather strong causal language (for example, "thereby impairing Golgi biogenesis, FAZ elongation, and division plane placement"). While the phenotypic correlations are convincing, direct causality is largely inferred from prior literature. Slightly tempering this wording could improve precision. It would also be helpful to state explicitly in figure legends the number of cells analyzed per condition and the number of independent experiments for each quantified phenotype.

Thanks for these constructive comments, which we agree and appreciate greatly. We have revised the manuscript accordingly to improve precision. The total number of cells analyzed, and the number of independent experiments were included in the figure legends.

Reviewer #2 (Recommendations for the authors):

Minor comments for improving the text are:

(1) The paper overall is clearly written. However, the Discussion starts with a solid sentence, then becomes a bit diffuse in discussing a wide range of PLK activities that were not addressed in the current work. That detracts attention a bit from the central contributions of this paper.

Thanks for this comment. We have deleted the discussion about TbPLK activities that were published previously.

(2) At least two places in the text state apparent contradictions.

(a) p.5 and Figure 2C. The authors say microtubule gliding speed was "...insignificantly reduced..." by the TbPLK-K70R mutant, yet they then state that motility was "interfered with". If the effect is "insignificant", why do they claim there is an effect?

(b) p6 and Figure 3C. The authors report KIN-G-T301A impact on microtubule gliding activity is insignificant, but then say this mutation reduces the motility of KIN-G. These statements are contradictory.

We meant to say that there was a slight but insignificant effect. We agree that such statements are somewhat contradictory and, hence, have been deleted. Thanks.

(3) p. 8, and Figure 7. "ventral side" and "leading edge" are not defined but are used to describe the KIN-G RNAi phenotype.

We have deleted the wording “ventral side”, as it is not necessary. Thanks.

(4) Figure 7B. Please explain the labeling - the new flagellum daughter is indicated as having the old posterior, while the old flagellum daughter cell is indicated as having the new cell posterior. This is counterintuitive to a reader not intimately familiar with the T. brucei cell division process.

Thanks very much. We included two sentences in the revised manuscript to explain this point.

The sentences read as follows: “The nascent posterior is formed near the mid-portion of the NFD cell through microtubule bundling and cytoskeleton remodeling during late stages of the cell cycle (Wheeler et al., 2013). Consequently, the NFD cell inherits the old, existing cell posterior, whereas the OFD cell inherits the newly formed or nascent cell posterior.”

(5) Figure 4, 5, and 7: "% Cells" is reported. Please indicate the total number of cells that were examined.

The total number of cells were included in the figure legends.

Reviewer #3 (Recommendations for the authors):

(1) The manuscript should be carefully edited for minor grammatical errors.

Thanks. We have carefully proofread the manuscript and corrected the grammatical errors.

(2) A general conclusion is that TbPLK phosphorylation of KIN-G in cells is critical for regulating its motor activity. However, this relies on the expression of phospho-mimetic mutants, which bypass TbPLK. Thus, there really is no direct evidence provided to support the specific role of TbPLK other than the in vitro phosphorylation data. Some additional experiments to assess the specific role of TbPLK in phosphorylating KIN-G in cells would lend support for the general conclusion. Is it possible to deplete or inhibit TbPLK and show that this impacts the phosphorylation of KIN-G in cells?

This is a great point that is very well taken. We performed a new experiment by inhibiting TbPLK with a potent PLK inhibitor, GW843682X, and then immunoprecipitating KIN-G for mass spectrometry to identify the phosphorylation levels before and after GW843682X treatment. We were able to confirm that T301 and S569 phosphorylation was reduced after treatment. This confirms that TbPLK phosphorylates T301 and S569 of KIN-G in vivo in trypanosome cells.

Specific:

(1) Figure 2: For microtubule gliding assays, representative videos should be included as supplementary data. Also, when the data do not show a significant difference between KIN-G and KIN-G + TbPLD-K70R, then the authors should not state there is a slight difference, as this is not supported by the data.

We have deleted the statement. We have included the representative videos for all the experiments presented in Figures 2 and 3. Thanks.

(2) Figure 3: As stated above, for microtubule gliding assays, representative videos should be included. Moreover, for KIN-G-T301A, the authors say that the gliding activity was "moderately, but insignificantly, reduced." Again, if the difference is not significant, it cannot be concluded that there is a difference compared with the wild-type protein.

We have deleted the statement. Thanks.

(3) Some of the headings in the Results section are not accurate. Regarding the in vivo results, the heading "Phosphorylation of Thr301 in KIN-G by TbPLK causes defective cell proliferation" seems to be an overstatement. It may be more accurate to state that "Expression of a phospho-mimetic mutant of KIN-G causes defective cell proliferation." The same comment applies to the other headings that follow this one. Presumably, there is a population of phosphorylated KIN-G in cells, and phosphorylation/dephosphorylation is a normal part of its regulation. In the text, the authors might more accurately conclude that hyperphosphorylation causes the defects they are seeing.

This is a great point. We agree and as we responded above, we have revised the manuscript, from the title to the main text, to reflect the point that hyperphosphorylation of T301 by TbPLK causes the defects. Thanks very much for these great comments!

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

Learn more at Review Commons

Reply to the reviewers

Response to the points raised by the reviewers.

Once again, we would like to thank the reviewers for their comments. We have systematically addressed their concerns, as detailed below.

Reviewer #1

Evidence, reproducibility and clarity

This study demonstrates that BICD2, previously known as an adaptor protein for dynein, is involved in regulating centriole engagement during mitosis. First, using different antibodies, it was shown that BICD2 localizes near the mother centriole, as observed by super-resolution microscopy. During G1 and S phases, BICD2 localizes slightly outside the Cep152 ring, while in G2 to mitosis, it localizes near the cartwheel component SAS-6. Moreover, analysis of deletion mutants revealed that BICD2 localizes to the centrosome in a CC domain-dependent manner at the C-terminal end. The localization pattern resembling a ring in the cytoplasm was also observed through the CC3 domain. Next, BICD2 knockout (KO) cells were generated to investigate centriole dynamics. In BICD2 KO cells, the distance between the mother and daughter centrioles was observed to increase from G2 to mitosis compared to controls. Along with this, early centriole disengagement and centriole amplification phenotypes were observed. The increased distance phenotype between centrioles was rescued in BICD2 wild-type (WT) and mutant forms lacking the CC1 domain at the N-terminus, suggesting that this function of BICD2 is independent of dynein. Additionally, BICD2 mutants mimicking phosphorylation at the C-terminus showed reduced centrosome localization and were unable to rescue the phenotypes seen in BICD2 KO cells.

While the study clearly demonstrates BICD2's contribution to centriole engagement, the underlying mechanisms of how BICD2 is involved in centrosome localization and centriole engagement remain unclear. As it is anticipated that the function of BICD2 is independent of dynein, further exploration of this unknown mechanism would enhance the value of the paper. Below are the concerns that should be addressed, including new experiments.